acceptodds
Under review as a conference paper at ICLR 2027

Modeling human memory with task-trained neural networks

Abstract

Human memory is prone to multiple well-documented forgetting and confusion phenomena. We ask whether these effects also emerge from training general-purpose memory architectures, and what role architecture, training tasks and input statistics each play. We introduce a framework spanning classical cognitive models and modern machine learning architectures, built around a recurrent working memory and an associative episodic memory. Six representative models are trained on sequences with tunable input statistics (semantic structure, temporal structure, partial observability), using recognition, reconstruction and sequential recall tasks. They are tested on standard paradigms in human memory research to assess the qualitative emergence of nine phenomena. We find that some effects always emerge regardless of architecture or training regime (perceptual similarity, conjunction errors, fan effect, set size); semantic false memories emerge specifically from input statistics; and other phenomena emerge from either architecture, training tasks, or input statistics (contiguity, primacy, recency, repetition). Notably, the presence of these phenomena does not appear to depend strongly on performance: most of them persist even when accuracy is close to 1. Our results suggest that some human memory phenomena may be understood as adaptations to environmental constraints, and we provide concrete candidates for what such constraints may look like in a simplified setting. More broadly, our work shows how task-trained models can complement classical cognitive models, as tools to capture many phenomena at once and explore the conditions for their emergence.

Primary area:
applications to neuroscience & cognitive science
Keywords:
Human memory, model, neural network, task-trained

Reviews

Among:
Shape:
1234this paper, Bottom 49%
Figure 1. Mean review rating of the reviewed papers at ICLR 2027. This paper averages 2.25 over 4 reviews, above 49% of the others.
Reviewer_LF2MOpenReview ↗
Rating
2(+1)
Confidence
3
Informativeness
2
Presentation
1
Soundness
1
Read review
Paper summary

This paper proposes a computational framework for assessing whether memory-related cognitive phenomena are model-, task-, or data-dependent. The authors trained six variants of gated RNNs extended with a stack memory (called "episodic memory") on a multi-objective, synthetic memorization task and evaluated whether they exhibit patterns that parallel human performance. The authors classified documented cognitive phenomena based on whether they are replicated from specific model configurations or data distributions.

Critical strengths

The high-level concept of identifying the roots of cognitive phenomena via model/task comparison is appealing.

Critical weaknesses

Limited Representativeness of the Explored Models

The biggest concern lies in the representativeness of the experimented models. While the authors emphasize that their architecture generalizes major models including Transformer, LSTM, and GRU, the actual experimental results are based on just five specific configurations. Accordingly, there are architectural variations left untested such activation functions and the number of heads. Although it is impossible to exhaust all combinations, it is misleading to draw general conclusions like "this cognitive phenomenon roots in data statistics, not in model architectures" from the narrow exploration.

The authors should at least discuss several neural network models that claimed to have replicated biological memory effects (e.g., Gosmann & Eliasmith, 2021, Psychol. Rev.). These biologically oriented models are necessarily formalized as a gated RNN.

The Evaluation Metric is Not Justified Enough

This paper evaluated their models based on Cohen's hh, which is derived from two statistics p1,p2∈[0,1]p_1,p_2 \in [0,1]. Table S3 explains how p1p_1 and p2p_2 were computed.

First of all, I do not think the main text is comprehensive enough to understand the analysis. It just says "Effect sizes were measured using Cohen’s hh" in the caption of Figure 2, without explaining what "effect size" means or how/why hh is computed.

Moreover, the specific choice of p1p_1 and p2p_2 is not justified in the paper. For example, the set size effect was evaluated between the recall probability conditioned on 4/5/6 vs. 10/11/12 study items. What is the philosophy behind these specific thresholds?

Similarly, the referenced human baselines (Table S4 and S5) appear arbitrary. The authors should justify why these specific studies are selected from the long history of psychological research, explaining in what ways they align with the models and/or tasks explored here.

Overall, I do not think the diverse phenomena discussed in this study can be uniformly evaluated by Cohen's hh. Instead, the standard evaluation/visualization specialized for each phonomenon is much friendlier to readers. For example, why don't you simply plot the accuracy or recall probability against presentation time of study items? Such visualization must be easier than force-unified evaluation of multiple phenomena.

Task Design is Not Justified Enough

The task adopted in this paper combines four subtasks. I do not understand what motivated the authors to choose such a complex design rather than simpler, individual experiments aligning with psychological experiments. (In Figure S2, results from "single-task training" are reported. However, they do not report which single task is reported there.) While I agree that "the brain was not shaped to solve any one task in isolation", the combination of four tasks is far apart from a real-world learning. If the authors are truly interested in naturalistic settings, they should rather test few-shot adaptation of vision–language–action models for example. I also think a single-task setting is even more natural for modeling animal experiments.

Additionally, the design of the "semantic structure" is misleading. While the semantic information represented in word embeddings originates in co-occurrence statistics of words, this "co-occurrence" is based on the neighborhood within serialized word sequences, not the simultaneous presentation of multiple items adopted in this study.

Citation

The authors report that they "used generative AI tools [...] to help find related works". Consequently, some of the cited studies have incorrect or non-standard publication years. For example, the Vaswani et al.'s "Attention is All You Need" is usually considered to have been published in 2017, not 2023. I also think the NeurIPS version is more appropriate than the preprint.

Questions for authors

My questions are embedded in the Critical Weaknesses section.

6 comments
AuthorsOpenReview ↗

Response to reviewer LF2M (weaknesses 1 & 2)

We thank the reviewer for their detailed and useful comments. We ran additional simulations, and updated the manuscript accordingly.

Weakness 1: limited representativeness of the explored models

The specific models we used were chosen as representatives of the main families of configurations that can be expressed in the unified model space (working-memory-only, episodic-memory-only, both components with built-in vs learned mechanism). Standard models each belong to one of these families, and in our experiments we found that they behave similarly to their respective representatives. To make this clearer, we have extended our analysis to include additional models (LSTM, GRU, Transformer, and TCM/CMR variants):

  • New figure S5 compares working-memory-only models (LSTM, GRU, our Flexible-c).
  • New figure S6 compares models with built-in mechanism (our Constrained and two variants of TCM/CMR). These variants are described in a new Section A.2.1 and in Table S7.
  • New figure S7 compares episodic-memory-only models (Transformer, our Flexible-M), for different numbers of heads.

In all these new analyses, we compare models across different hidden dimensions and show that the results remain qualitatively similar within each group. As suggested, we also conducted additional analyses on hyperparameters:

  • New figures S3 and S4 evaluate models across different hidden dimensions and new semantic+temporal training regimes
  • New figure S8 compares models across different vocabulary sizes
  • New figure S9 compares models across different cINc^{IN} activation functions (default was tanh)
  • New figure S10 compares models across different number of schemas in the vocabulary

Overall, results remain stable across these hyperparameter changes. We will refer to these analyses in the main text, and we will explain intuitively the difference between our Constrained model and TCM/CMR (which can already be assessed from entries in Table 1 and Table S7). We will also discuss the CUE model by Gossman & Eliasmith, 2021. As it is heavily inspired by the TCM model we expect it to behave similarly to the TCM variants.

Weakness 2: the evaluation metric is not justified enough

The reviewer questions the choice of Cohen's h as our primary metric for assessing the presence of phenomena. We agree that this choice was not well explained in the main text, and that detailed plots would be a good addition. We modified the manuscript:

  • new figures S12 and S13 show detailed plots of each phenomenon, for a more direct visual assessment
  • the following paragraph has been added at the end of the "training and testing" section:

    Effect size computation. All phenomena are evaluated with Cohen’s h (Cohen, 1977), a measure of the difference between two proportions. For two probabilities p1,p2∈[0,1]p_1, p_2 \in [0, 1], it is defined as h=2arcsin⁡(p1)−2arcsin⁡(p2)h = 2\arcsin\left(\sqrt{p_1}\right) - 2\arcsin\left(\sqrt{p_2}\right). The sign of h indicates the direction of the effect: h>0h > 0 when p1>p2p_1 > p_2. For each phenomenon, Table S4 lists the test setting and the two probabilities being compared. In the existing literature, these phenomena are typically assessed qualitatively from the shape of a plot. Our choice of p1p_1 and p2p_2 is a way to make them measurable, which allows for easy and concise comparison across models and training settings. For reference, we computed the same measure for human experiments (Table S5 and Table S6). We also provide detailed plots for each phenomenon in Figure S12 and Figure S13 for a more direct visual assessment.

  • We now provide additional human baselines in Table S5 and S6 (with values reported in main plots), with at least 2 studies per phenomenon. Our choices are based on similarity of tasks and inputs to our setting, and data availability.
AuthorsOpenReview ↗

Response to reviewer LF2M (weaknesses 3 & 4)

Weakness 3: task design is not justified enough

The reviewer asks two questions: why train the models on multiple tasks, and why choose these tasks? We answer both in a new paragraph in the beginning of the "training and testing" section:

Models are given sequences of study observations (Section 2.3), followed by recall cues which determine the tasks that should be performed. The training tasks define the loss against which the model parameters are optimized, and therefore shape the behavior of the model. Ideally, they should reflect the pressures under which biological memory systems were shaped. We considered four candidate tasks, each corresponding to a basic and plausible memory function:

  • Recognition: deciding, given a (possibly partial) cue, whether a matching observation has been seen before. This is useful, for instance, to recognize a familiar place, a known individual or a threat met in the past.
  • Cued recall: recovering the missing part of a partial cue. For example, coming back to a place where danger was encountered should bring back the full memory of that encounter.
  • Backward and forward recall: retrieving the observation that preceded or followed a given cue. Knowing what came before or after an event can support causal learning, prediction and planning.

Implementation details for each task are given in Section A.3. Each task can be switched on or off independently, so that models can be trained on any single task or on any combination of them. Being able to combine tasks matters for two main reasons. First, memory in the brain is unlikely to have been shaped by a single objective, and previous work has shown that training a network on several tasks changes the representations and behavior it develops (Li et al., 2026; Yang et al., 2019). Second, the phenomena we study are measured with different tasks in the human literature (recognition for some, cued recall for others; see Table S5 and Table S6), so a single model can only show all of them if it can solve several tasks.

Another reason why we included forward and backward tasks is their role in the emergence of the contiguity effect, as shown in figure 4(a).

In the following, we answer to other minor comments from the reviewer:

  • We agree that the single-task plots do not show clearly which task the model was trained on. Thanks for pointing this out, we now explain it in the caption and we will highlight on it on the figure.
  • It is true that an animal in the lab is typically trained on one task, but it starts with a memory system already shaped by many other processes.
  • Regarding the semantic structure, we chose that name because this structure is meant to create a form of semantic memory. However, it is true that "semantic" typically applies to words and language, while our notion aims to be more general. We could switch it to "schematic structure".

Weakness 4: Citation

The reviewer noticed a mistake in the date of a reference. This mistake happened because the date of the latest arXiv version of the paper was saved to Zotero. We thank the reviewer for spotting this, we now reference the Neurips version. We want to clarify that AI tools were only used in the process of finding papers, but no AI tool was used to generate in-text citations or reference entries. All reference entries come from a .bib file generated from Zotero.

Conclusion

We thank the reviewer again for their insightful feedback. We believe the modifications have improved the clarity our manuscript without changing the conclusions, and we hope to have answered the reviewer's comments. We would be grateful if the reviewer would re-evaluate their ratings in light of these improvements.

I appreciate the authors' effort on the revisions. I have raised my score to 2. I cannot give them a better score mainly because of Weakness 3; it is true that "memory in the brain is unlikely to have been shaped by a single objective", but I think the ultimate scientific goal is to find the necessary and sufficient components. I don't think starting with a handful of mixed learning objectives helps us step toward it in comparison to atomic analyses based on single objectives.

Reviewer_pDQDOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
3
Soundness
2
Read review
Paper summary

This paper investigates whether human memory phenomena can emerge naturally from task-trained neural networks and how model architectures, training objectives, and input statistics jointly influence their emergence. The authors introduce a unified memory modeling framework that combines recurrent working memory with associative episodic memory. By varying memory architectures, training tasks, and synthetic input distributions, the framework examines nine well-established human memory phenomena, including perceptual similarity effects, semantic false memories, conjunction errors, the fan effect, the set-size effect, temporal contiguity, primacy, recency, and repetition effects. The experiments suggest that some phenomena consistently emerge across different configurations, whereas others depend on specific architectural constraints, training objectives, or statistical properties of the input. Based on these observations, the authors argue that certain classical memory phenomena may arise from adaptation to environmental regularities and task demands without requiring explicitly designed cognitive mechanisms.

Critical strengths
  1. The paper offers a conceptually interesting perspective on computational memory modeling. Unlike traditional approaches that develop specialized cognitive models for individual memory phenomena, this work investigates multiple phenomena within a unified framework while treating architecture, training objectives, and input statistics as three principal dimensions of analysis.
  2. The experimental study covers a relatively broad range of settings, including nine memory phenomena, multiple architectural variants, four input-statistics regimes, and different combinations of training objectives.
  3. The paper is generally well organized, introducing the methodology through three components: memory architectures, input representations, and training tasks, followed by experimental analyses of nine memory phenomena.
Critical weaknesses
  1. Although the authors propose a framework intended to unify classical cognitive models and modern machine learning architectures, its fundamental components largely consist of existing recurrent state-update mechanisms and key-value memory operations. Table S6 primarily reformulates existing models using a common notation rather than establishing their strict functional equivalence within the proposed framework. Furthermore, the experiments mainly consider custom Flexible and Constrained variants without directly evaluating standard LSTM, GRU, Transformer, or classical TCM/CMR implementations.
  2. Although the paper evaluates multiple model variants, these variants primarily constitute architectural ablations within the proposed framework rather than independent implementations of established cognitive models or modern memory networks. In particular, TCM, CMR, and Transformers are incorporated into the unified notation but are not directly evaluated under matched input distributions, training conditions, and evaluation protocols. Consequently, it remains unclear whether the observed memory phenomena demonstrate the specific value of the proposed framework or could be reproduced equally well by existing models trained under comparable conditions.
  3. The paper measures nine memory phenomena using Cohen's h and compares their effect sizes with those reported in human experiments. However, the model evaluations and human experiments differ substantially in stimulus modalities, sequence lengths, and experimental protocols.
Questions for authors

Please refer to the above weaknesses.

3 comments
AuthorsOpenReview ↗

Response to reviewer pDQD

We thank the reviewer for their detailed and useful comments. We ran additional simulations, and updated the manuscript accordingly.

Weakness 1: poor unification of memory models

We believe that the space of memory models is useful to clarify which components models share, which ones are not featured in some models, and how transformations might differ. We now explain this in the "Models detailed" section in the appendix:

Overall, this formulation was made to express as many models from the literature as possible and to make explicit the choices one has to make when designing a model. This allowed to build Table S7 for a direct comparison of the components of each model.

The rest of the related concerns are answered in the next section.

Weakness 2: standard models are missing

This point was also raised by reviewer LF2M. We repeat our answer here for completeness. The specific models we used were chosen as representatives of the main families of configurations that can be expressed in the unified model space (working-memory-only, episodic-memory-only, both components with built-in vs learned mechanism). Standard models each belong to one of these families, and in our experiments we found that they behave similarly to their respective representatives. To make this clearer, we have extended our analysis to include additional models (LSTM, GRU, Transformer, and TCM/CMR variants):

  • New figure S5 compares working-memory-only models (LSTM, GRU, our Flexible-c).
  • New figure S6 compares models with built-in mechanism (our Constrained and two variants of TCM/CMR). These variants are described in a new Section A.2.1 and in Table S7.
  • New figure S7 compares episodic-memory-only models (Transformer, our Flexible-M), for different numbers of heads.

In all these new analyses, we compare models across different hidden dimensions and show that the results remain qualitatively similar within each group. We will refer to these analyses in the main text

Weakness 3: comparison of effect size with human experiments suffers from differences in stimulus modalities, sequence lengths, and experimental protocols

  • We will clarify in the text the limitations of such a direct comparison, and that human values are only reported to give an intuition of the order of magnitude of the effects.
  • We now report human values from additional experiments, with at least 2 values per phenomenon. While this doesn't solve the problem, it at least covers different experimental setting and provides a range of values instead of a single one.

Conclusion

We thank the reviewer again for their insightful feedback. We believe the modifications have greatly improved clarity of our manuscript without changing the conclusions, and we hope to have answered the reviewer's comments. We would be grateful if the reviewer would re-evaluate their ratings in light of these improvements.

Thank you for your detailed response and additional experiments. My concerns regarding the baseline comparisons have been largely addressed. However, the technical novelty of the unified framework remains limited, and the discrepancy between model evaluations and human-subject experiments continues to constrain the strength of the conclusions. While I appreciate these improvements, I believe the remaining issues are significant enough to warrant maintaining my original score.

We thank the reviewer for their response and are glad the additional baseline comparisons addressed their concerns. We briefly clarify the remaining points about the comparison with human experiments for completeness.

  • Differences in sequence length: New Figures S14 and S15 evaluate all phenomena across different study-list lengths. The results stay qualitatively stable.
  • Differences in stimuli and protocol:
    • Phenomena are robust in human experiments: the human experiments themselves differ a lot in sequence length, stimulus modality and protocol (Tables S5 and S6). Yet the phenomena we study replicate across them. This is why we chose robust, widely replicated effects that are not tied to any specific protocol.
    • Abstraction is necessary: abstracting stimuli is part of computational modeling. For example, TCM and related models represent words as one-hot vectors.

We hope these clarifications help put the comparison with human data in context.

Reviewer_jN9YOpenReview ↗
Rating
2
Confidence
3
Informativeness
2
Presentation
2
Soundness
2
Read review
Paper summary

This paper studies whether human memory phenomena emerge in task-trained neural networks and how their emergence depends on architecture, training tasks, and input statistics. It introduces a common notation for recurrent working memory and associative episodic memory, instantiates flexible and constrained models with architectural and distractor variants, and trains them on recognition, cued recall, and forward/backward recall under four synthetic input regimes.

The models are evaluated on nine phenomena: perceptual similarity, semantic false memories, conjunction errors, the fan effect, set size, contiguity, primacy, recency, and repetition. The reported results distinguish effects that occur broadly in the evaluated settings from effects contingent on semantic structure or on temporal/training constraints. Embedding analyses, training trajectories, retrieval weights, and decoder probes provide additional evidence. I view the contribution as a framework for controlled computational experiments and candidate explanations of memory behavior. Its relevance to human mechanisms requires evaluating how strongly those candidates are constrained by the reported evidence.

Critical strengths
  1. A useful framework for controlled comparisons -- Separating architecture, task objectives, and input statistics makes explicit several choices that are often intertwined in task-trained modeling. Section 2.2 and Table S6 offer a useful common language for relating cognitive memory models to neural architectures. The resulting framework supports systematic investigation across several phenomena within a single experimental setup.

  2. Training-environment manipulations yield informative effects -- The semantic-structure comparison and the temporal/partial-observability manipulations show how training conditions can alter subsequent memory behavior. Figure 4 tests contiguity on independent, distinct study items, so the observed effect cannot be explained simply by temporal overlap in the test inputs. The variation of task weights and partial observability further supports the influence of training conditions.

  3. The paper reports meaningful repetitions and interpretability analyses -- Appendix A.4 reports ten training/testing repetitions and 2,000 test sequences per phenomenon. Figure 2h provides a 30-seed analysis of effect sizes over training for Flexible. Human reference effect sizes, architectural variants, and retrieval/decoder analyses supply evidence beyond a single illustrative run. These are substantive strengths of the experimental effort.

Critical weaknesses
  1. The generality of the findings across capacity and task scale is not established. The experiments use a vocabulary of 64 symbols, four schemas, up to nine item positions, hidden dimension 64, and training lists of length 2–16 (Appendices A.1–A.2). Most phenomenon tests use length-eight lists (Table S3). A full training run contains 500 epochs of 5,000 sequences, corresponding to 2.5 million sequence presentations, so the main concern is the restricted generative environment despite substantial training exposure. The paper does not report systematic capacity, vocabulary-size, or substantially longer-context sweeps. Consequently, it remains unclear whether the phenomenon taxonomy is stable when representational capacity and memory load change. The training-trajectory analysis is valuable, but does not answer this scaling question. Small controlled models are appropriate here; nevertheless, a modest capacity/load stress test is needed to support broader generality.

  2. The attribution of phenomena to architecture, tasks, or inputs remains conditional on shared modeling choices. The tested models share the symbolic input interface, embedding construction, task readout, and training setup. Broad agreement across memory-module variants therefore does not rule out effects driven by these common components. Likewise, the four main input regimes are not a full factorial design: partial observability is evaluated alongside temporal structure, while joint semantic and temporal structure is not systematically tested. Figure 4b provides a useful partial-observability sweep, but at a fixed temporal-training setting. These experiments establish informative conditional effects. They do not fully separate interactions among the proposed explanatory factors or justify an unrestricted interpretation of architecture independence and input-structure-only explanations.

  3. Qualitative resemblance provides limited identification of human memory mechanisms. Using artificial neural networks to study memory is a legitimate modeling strategy, and biological differences alone do not invalidate it. However, the same phenomenon appears through different routes in this paper: for example, contiguity can arise from constrained architecture or from training. This demonstrates that behavioral resemblance alone does not identify the generating mechanism. Figure 2 and Tables S4–S5 provide human effect-size references, but these span heterogeneous modalities, list lengths, and baseline performance. The paper does not report a protocol-matched predictive comparison that discriminates its account from alternatives such as temporal-context explanations. The authors appropriately describe qualitative emergence and explicitly leave human validation of the contiguity mechanism open in Section 3.3. A distinctive prediction tested against existing human data would substantially strengthen the cognitive contribution.

Questions for authors
  1. Capacity and memory load. Do the key effects persist across a small grid of hidden dimensions, vocabulary sizes, and longer study lists? Please report effect sizes together with task accuracy, so changes in memory load can be distinguished from changes in overall error rate.

  2. Shared components and factor interactions. Can the central architecture/input conclusions be checked under an alternative embedding or readout and a combined semantic-plus-temporal regime? Which conclusions describe sufficient conditions within the tested family, and which are intended as stronger independence or necessity claims?

3 comments
AuthorsOpenReview ↗

Response to reviewer jN9Y

We thank the reviewer for their detailed and useful comments. We ran additional simulations, and updated the manuscript accordingly.

Question 1: capacity and memory load

  • New figures S3, S4, S5, S6, S7 evaluate models across different hidden dimensions.
  • New figure S8 compares models across different vocabulary sizes
  • New figure S10 compares models across different number of schemas in the vocabulary
  • New figures S14 and S15 evaluate phenomena across different lengths of study list

Overall, results remain stable across these hyperparameter changes. We will refer to these analyses in the main text.

Question 2: Shared components and factor interactions

  • New figure S9 compares models across different cINc^{IN} activation functions (default was tanh). Results remain stable, except when normalizing cINc^{IN} in the Constrained model.
  • New figures S3 and S4 evaluate Flexible and Constrained models in combination of temporal and semantic structure (with and without partial observability). We want to note that partial observability only makes sense when the environment shows temporal structure.
  • New figure S16 compares models with different embeddings and readout components.

We will refer to these analyses in the main text.

Question 3: limitations of qualitative assessment.

While qualitative assessment is a common way of validating task-trained models (Lu et al., 2022, Li et al., 2026), we agree that it does not replace a quantitative comparison with human data. However, such a comparison is difficult in our setting, which we now explain in a "limitations" section:

... our comparison with human behavior is qualitative: we test whether models reproduce effects, rather than fitting human data quantitatively. A quantitative comparison is limited by data availability and by differences in experimental protocols across the effects we study, which would be difficult to capture jointly. Building task-trained models in richer settings that allow a more precise comparison with human data is a direction for future work.

Conclusion

We thank the reviewer again for their insightful feedback. We believe the modifications have greatly improved the clarity of our manuscript without changing the conclusions, and we hope to have answered the reviewer's comments. We remain open for additional comments. We would be grateful if the reviewer would re-evaluate their ratings in light of these improvements.

The authors have addressed some of my concerns, particularly by adding supplementary experiments. However, my main concerns, such as Q3, remain. Therefore, I have to maintain my current evaluation.

We thank the reviewer for their response and are glad the additional baseline comparisons addressed some of their concerns. We are puzzled, however, by the reviewer's insistence on Q3. Good models need to tackle questions at the right level of abstraction to generate insights without getting lost in the idiosyncrasies of individual experiments.

Quantitative comparison with human data is most meaningful when focusing on a single experiment or a few related ones. Here, we deliberately consider many phenomena observed in experiments that differ in stimuli, modalities, and protocols. It is unrealistic to replicate all of these experiments exactly within one insightful model that is not just a gigantic blackbox. Instead, we built an abstracted environment in which models are trained on comparable tasks, and asked whether these robust phenomena emerge. In this setting, absolute effect sizes depend on modeling choices (e.g., vocabulary size, number of schemas, capacity), but, importantly, the presence of each effect is stable across them (Figs. S3-S16). This makes qualitative emergence the appropriate level of comparison.

We see this approach as complementary to narrow memory models designed to fit specific experimental datasets, filling the gap of memory models that are broadly consistent with human memory phenomena. For instance, we find that some effects, such as contiguity, can emerge through different routes. Further experiments are needed to distinguish between these candidate mechanisms.

Reviewer_HxnhOpenReview ↗
Rating
3
Confidence
2
Informativeness
3
Presentation
3
Soundness
2
Read review
Paper summary

The paper studies existing memory phenomena through the lens of network architectures, training tasks, and input statistics. By using a generalized architecture of recurrent memory and associative memory, together with multi-task training and customizable input statistics, the authors show that different memory phenomena may emerge from different lenses, rather than only from the architectures. The setup is modular, which enables the isolation of certain phenomena by varying the configuration accordingly. The experiment is thorough, utilizing the modularity of the setup to expose the emergence of the studied memory behavior.

Critical strengths

The study is well motivated, and the experimental setup is mostly convincing. I can generally understand the intuition for the design of the architecture and the accompanying experimental setup. I think the experiment is thorough, as the architecture, training tasks, and input format cover relatively fundamental options. The representative architectures in Table 1 closely resemble existing mechanisms like LSTM and transformer and can help complement existing literature.

The paper provides a principled framework for probing some of the memory phenomena. While some of the explained phenomena appear intuitive, I appreciate a well-defined approach to empirically test them on neural models. I find the insights potentially interesting to a broader audience, given that the claims are reproducible and sufficiently backed up.

Critical weaknesses

I didn't find any apparent critical weaknesses, but rather some moderate weaknesses that deserve clarification. Please take a look at the questions in the next section that I'd like clarification on.

Questions for authors

Q1. While the generalized architecture seems to cover substantial prior literature, it is still a bit unclear to me what the motivations are for placing each component the way it is (lines 164-169). For example, the authors mention that some methods choose to read-before-update, while the proposed architecture updates before reading. A section in the appendix explaining the overall decisions, i.e., which literature they are motivated by, or just for the purpose of generalizing existing works (which is still a valid reason in my opinion), etc., is useful. I think it is worth making them explicit since these decisions can also materially affect the observed phenomena.

Q2. What do the authors perceive as the limitations of their study? I find the study interesting, but the conclusions that can be drawn regarding human memory correspondence require careful interpretation. For example, I find the input scale quite small. Therefore, although it is useful for probing the phenomenon, generalizing the conclusion to more complex tasks can be quite difficult.

Also, just a minor suggestion on clarity (not affecting the decision), but I find Figure 1b quite hard to parse.

2 comments
AuthorsOpenReview ↗

Response to reviewer Hxnh

We thank the reviewer for their useful comments. We updated the manuscript accordingly.

Question 1: choice of model components

We adapted equations in lines 164-169 to include both read-before-update and update-before-read models. We also added the following in the "Models detailed" section in the appendix:

Overall, this formulation was made to express as many models from the literature as possible and to make explicit the choices one has to make when designing a model. This allowed to build Table S7 for a direct comparison of the components of each model.

As suggested, we will also try to make fig 1b clearer.

Question 2: limitations

We added a new limitations section:

This study has several limitations. First, although our training setup was inspired by features of the real world, it remains highly abstract. The inputs are also small in scale, both in sequence length and in the number of items to be stored. Second, our model space is defined at a level of abstraction that lets all models be trained on a variety of tasks using backpropagation. As a result, we do not consider more biologically detailed models, such as those based on spiking neurons (Gosmann & Eliasmith, 2021, Zhou et al., 2024). Third, each of our tasks consists of a single recall cue that must be answered with a single memory access. Our setting therefore excludes the possibility of sequential memory accesses to solve a task, which may occur in human experiments. Fourth, our comparison with human behavior is qualitative: we test whether models reproduce effects, rather than fitting human data quantitatively. A quantitative comparison is limited by data availability and by differences in experimental protocols across the effects we study, which would be difficult to capture jointly. Building task-trained models in richer settings that allow a more precise comparison with human data is a direction for future work. Finally, although we have tried to cover the space of memory models, tasks, and input statistics as broadly as possible, it is practically impossible to test all combinations. We believe we have covered the most relevant cases, but we cannot exclude that some untested combination would show unexpected behavior.

Conclusion

We thank the reviewer again for their insightful feedback. We believe the modifications have improved the clarity of our manuscript without changing the conclusions. We remain open for additional questions.

Thank the authors for the effort in revising the paper. My questions have been mostly clarified, and I will maintain my acceptance score.

Comments on the paper

2 comments

Thank you for your response. However, I think you answered to the wrong comment, as this was the response to reviewer pDQD.

Sorry, it seems I accidentally deleted my previous comments. It has been updated in my slot. Thank you for your efforts, your reply solves most of my concern, but my main concerns remain.

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

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