Dissociation between impaired explicit spatial remapping and preserved implicit neural dynamics in Alzheimer’s disease

Reviewer #1 (Public review):

Summary:

Remapping is clearly degraded in amyloid models, but people and animals with a lot of pathology often hold onto more function than their spatial maps would predict. The authors' idea is that CA1 carries two things at once: an explicit code where rate maps onto position, and an implicit one in the temporal relationships between cells, and that AD hits the first much harder. They recorded CA1 with tetrodes in App(NL-G-F) and WT rats running an A-B-B-A sequence of open field sessions, repeated daily for six days, with rest in between. They then compared rate map measures against a cofiring measure (pairwise Kendall's tau) and looked at SWR reactivation during rest.

Strengths:

(1) The design is right for the question. Alternating back to the familiar arena separates "can the network register a new context" from "can it get back to the old one," and the finding that App rats look OK on the first A to B transition but fall apart on the return is the most striking thing here. The confused cell result, 24% vs 4.5%, is easy to read and hard to dismiss.

(2) Six consecutive days is also worth something. Most work on this is cross-sectional, and looking at how the coding changes with accumulated experience is the right way to ask about plasticity.

(3) The PIR analysis in Figure 5 is the bit I liked best. Subtracting each cell's position-predicted rate before computing tau is a reasonable check that the cofiring effects aren't place fields in disguise, and it's more than most papers making this argument do. The theta index control is a good instinct too, though see below on how it's analysed.

Weaknesses:

(1) No behaviour. This is the main problem and everything else is secondary. The title, abstract, intro and discussion all turn on preserved learning and memory, and the rats were never tested on anything. They foraged for popcorn in an open field. No discrimination measure, no novelty preference, no probe, nothing. So "learning" ends up being defined as "decoder accuracy went up across days," which makes the central claim circular. Either add a behavioural readout in these animals or take the learning language out of the title and abstract and say what was actually measured, which is experience-dependent change in neural coding.

(2) Four animals per group is fine for this kind of work, but the statistics don't respect it. Degrees of freedom in the thousands and tens of thousands (t(8616), t(36293), F(1,2674)) treat cells and cell pairs as independent, which they aren't. The mixed models in Figure 1 are the right approach, and I couldn't see why they were dropped everywhere else. The theta result is the clearest casualty: a null across 36,293 cell pairs from four rats isn't evidence that theta coordination is preserved; it's an untested question with n=4.

(3) Also, the reported df do not always match the stated n. The Methods say 4 per genotype, but several animal-level tests give t(4), which implies 3. Figure 4C gives t(32), and Figure 5C gives t(31) for what look like per-day measures. I couldn't work out what the sampling unit was in each case.

(3) Some statistics can't be right. I noticed three, without looking hard. For example. Figure 1C, rate overlap: t(471) = 2.3 with p = 2.0e-7. Fig 1G: t(163) = 5.3 with p = 0.48. Fig 3F: F(1,483) = 36.5 with partial eta squared = 0.7, when the almost identical test in the previous sentence gives 0.07. These are likely all typos, but there are enough that the whole set needs going through.

(4) The dissociation isn't tested with matched methods. Explicit coding gets rate map correlations, PVC, rate overlap, and field size. Implicit coding gets an SVM across six days. The claim is that one improves with experience and the other doesn't, but they're never put through the same analysis. The authors should run the identical decoder on rate vectors and on tau vectors, same cross-validation, day by day, and show the slopes diverging. That would be a real dissociation. Figure 1G does run a rate decoder but only pooled, not across days. As it stands, the difference in learning slopes could partly be the two analyses having different sensitivity.

(5) The PIR residual may not be as clean as it looks. PIR is observed rate minus rate predicted by the cell's own spatial map. If the spatial map is a worse model of firing in App rats, which is the paper's own claim, then less gets subtracted and more is left in the residual. So a group difference in residual tau structure could be partly downstream of the group difference in place coding quality rather than something independent. This is worth some kind of check, e.g. matching cells on spatial information, or at least reporting how much variance the spatial model explains in each group.

(6) Reactivation consistency. This carries a lot of the interpretation, and it's the thinnest evidence in the paper. r = 0.2, p = 0.04 in App against r = -0.2, p = 0.06 in WT. That's a difference in significance, not a tested difference between groups, and with both p-values sitting on either side of 0.05, I wouldn't build a mechanism on it. Needs a group x day interaction. Separately, mean pairwise correlation across SWR population vectors depends on how many cells are active, how many events there are (panels show 189 to 491) and how sparse the firing is. SWR rate, duration, participating cells and firing rates would let the reader judge whether "more consistent reactivation" means what's claimed.

(7) The hyperexcitability to excessive replay to Hebbian consolidation story on pp 21 to 22 runs about a page on the back of one marginal correlation. This section should be cut down and flagged as speculation.

(8) Missing controls. Things I expected and didn't find: histology confirming tetrode placement in CA1, any pathology verification in this cohort rather than a citation to Pang 2022, and A1-A2 spatial correlation shown next to B2-A2. That last one matters. If the App representation of A just drifts across the day, that's a different story from a specific failure to reinstate A, and the confused cell analysis as built can't tell them apart. Also, with the threshold set at the 95th percentile of the A1B1 baseline, the WT value of 4.5% is basically the chance floor by construction, so the number that carries information is the App one.

(9) The issue of males only should be mentioned.

Reviewer #2 (Public review):

This study by Wang et al. longitudinally tracks hippocampal CA1 population dynamics in Alzheimer model rats during repeated exposure to different environments. The authors dissociate two levels of neural coding. "Explicit" spatial coding, assessed by rate maps and population vector correlations, is severely impaired in AD rats and does not improve with experience. In contrast, "implicit" temporal cofiring structure, quantified by pairwise Kendall's tau and population cofiring correlations, becomes progressively more context-specific over days, mirroring behavioral learning. This preserved temporal coding is not merely a byproduct of spatial overlap, as position-independent rate analysis confirms that learning-dependent discrimination arises from intrinsic temporal dynamics rather than from residual spatial tuning. Moreover, offline sharp-wave ripple reactivation shows increasing consistency across days specifically in AD rats. These findings reveal a dissociation in the AD hippocampus and propose that temporally structured population dynamics, rather than spatially selective firing, may support residual cognitive function.

Overall, the findings are novel and thought-provoking; the analyses are comprehensive and well-controlled, and the proposed re-registration framework offers a compelling new lens for understanding cognitive resilience in Alzheimer's disease, with clear potential to guide future neuromodulation interventions.

I have only a few minor comments.

(1) Justification of terminology ("explicit" vs. "implicit").

The manuscript should clearly define the two terms early in the Introduction, ideally in a dedicated paragraph. In my opinion, the current use of "explicit" and "implicit" is not intuitive and may even be misleading.

(2) Does the dissociation reflect differential impairment between rest and running states in AD?

The authors could elaborate on this.

(3) Effect size in Figure 1D - the difference does not appear very large.

The statistical significance in Figure 1D is accompanied by relatively modest effect sizes. The authors may tone down the claim about "failure to distinguish" in the manuscript ("failed to distinguish different contexts during the second transition" on Page 8).

(4) Definition of "confused cells" - why not a fixed correlation threshold?

The authors define "confused cells" as those whose B2‑A2 spatial correlation exceeds the 95th percentile of the A1‑B1 baseline distribution within the same animal. This seems to be unnecessary. A fixed correlation threshold (e.g., r > 0.5 or r > 0.6) would have a direct biological interpretation: it would identify cells that maintain similar firing fields across two putatively distinct environments, i.e., cells that truly fail to remap. In contrast, a relative percentile threshold defines "confusion" not against an absolute standard of similarity, but against the degree of remapping observed during the first A‑B transition.

(5) SVM decoding on spike‑train temporal structure - missing justification.

The authors state that "the temporal structure of spike trains contained distinct contextual information" (P9) and then directly apply an SVM decoder to the data, but the logical bridge is missing. Why is a decoder necessary here, and is it useful for such a task?

(6) Figure 6 - learning occurs during reactivation but does not transfer to the online state (theta state), even after days of training.

What does this mean in terms of different phases of memory? Is the consolidation phase affected more? The authors may provide more discussion along these lines.

Reviewer #3 (Public review):

Summary:

Determining the ways in which Alzheimer's disease (AD) impacts the neural instantiations of memory is a fundamental aim of neuroscience and likely to be critical to understanding and treating disease progression. Previous work has highlighted how the hippocampal spatial code - typically context-specific - fails to discriminate between different environments in rodent models of AD. Here, Wang et al. leverage new analyses in a rat model of AD to test whether this deficit in 'remapping' reflects an impairment in intrinsic temporal coding. The authors find that the intrinsic temporal code of AD rats does come to effectively discriminate between environments (albeit more weakly than their wild-type counterparts), despite persistent impairments in remapping.

Strengths:

One of the major strengths of this work is its focus on distinguishing between two different types of neural impairments in AD. While previous work has highlighted impairments in remapping, these impairments could be due to: (a) impairments in intrinsic neural computations, or (b) impairments in the way these intrinsic neural computations are anchored to the world. The author's evidence supports the latter, with important implications for the nature of these impairments.

Weaknesses:

A handful of weaknesses could be addressed to strengthen this work. Firstly, a number of key measures of place code quality and behavioral quality between groups are omitted. Given that the author's interpretations rely on comparisons between groups and often use decoding analyses for central conclusions, indicating whether the recordings are comparable between groups in terms of behaviors and cell counts would be helpful for the reader. Even better, matching cell counts between groups for decoding analyses could ensure that outcomes are not driven by this potential confound.

Another weakness that is worth addressing involves the pivotal comparison between time-averaged remapping (Figure 4) and intrinsic temporal code discrimination (Figure 3). For temporal code discrimination, the analysis relies on comparisons between pairs of epochs (e.g. from A1B1 to A2B2), while for remapping, the comparison averages together epochs (A1+A2 and B1+B2). As a result, these comparisons are characterizing two slightly different things. Given that this is a key comparison for this paper (cofiring evolves to discriminate contexts while the spatial code does not), I think it would be important to demonstrate that remapping between pairs of epochs also stagnates to more closely mirror the cofiring analysis.

A final weakness is the sharp wave ripple (SWR) ensemble analysis. Here, the authors extract population vectors during SWR (SWR-PVs) during rest in both WT and AD rats. Next, they compare the extent to which SWR-PVs on AVERAGE resemble other SWR-PVs for that epoch. The authors report that this measure increases with experience in AD rats but not wild-type (WT) rats. While the authors interpret this to mean that SWR-PVs come to be more reliable with experience in AD rats, it could alternatively mean that SWR-PVs become less diverse or 'muddier' with experience, while SWR-PVs in WT rats continue to represent diverse trajectories. To make this analysis compelling, a better measure might be something that quantifies the diversity or content of SWR-PVs and something that quantifies similarity between each SWR-PV and the most similar other SWR-PVs.