Author response:
Public Reviews:
Reviewer #1 (Public review):
Summary:
The authors addressed how viral-mediated expression of amyloid in medial septum (MS) cholinergic neurons, or broadband amyloid expression, affects the integrity of MS cholinergic neurons in aging mice, as well as cognition, sleep, and hyperexcitability. Using fiber photometry and viral tracing, they show that MS cholinergic neurons are active during wakefulness and REM sleep and that they also project to many different areas. Next, they show that when they express a viral vector carrying APP to encode amyloid beta in MS cholinergic neurons, these neurons express amyloid as they do in a globally expressing APP model (APP-NLGF). They find that amyloid may spread largely following MS projections and that MS die over time presumably due to amyloid expression. They also describe the emergence of memory deficits and reduced REM sleep attributable to loss of MS cholinergic neurons. Lastly, they report a higher burden of epileptiform activity in mice with broadband amyloid expression and the emergence of neuroinflammation in MS, which may be contributing to cell loss and network dysfunction.
Strengths:
(1) New insights on a potential role of MS cholinergic neurons in spreading amyloid.
(2) Use of several different methods to address effects of MS dysfunction in aging mice (AAV, global, lesioning).
(3) Combination of activity-related readouts including fiber photometry, EEG coupled to histological, behavioral, tracing, and neuropathology measures.
(4) Consideration of potential confounds to behavioral measures using proxies of anxiety-related behavior.
Thank you for the positive assessment and for recognizing the novelty of our findings, the complementarity of our experimental approaches, and the breadth of our multi-modal readouts. We will address the weaknesses raised below point by point.
Weaknesses:
(1) The authors aim to model the prodromal phase of Alzheimer's disease (AD) neuropathology, which is a very promising area to target therapeutic intervention. While reduction in basal forebrain volume has been reported early in AD, presumably functional changes may be happening much earlier, i.e., even before MS start to degenerate or before REM sleep is reduced. This view has been proposed by human studies showing increased ChAT reactivity in MCI (PMID: 11835370) and evidence in mouse models showing that MS cholinergic neurons may be hyperactive early and degenerate late with distinct implications for memory (PMID: 41717904). Thus, functional changes could be considered before structural changes could be discussed, as earlier ages in this model could reveal such early changes.
This is an insightful comment. We fully agree that early functional changes preceding structural degeneration represent an important and exciting avenue, and we will explicitly acknowledge this in the revised manuscript, including the relevant literature on early cholinergic hyperactivity. Examining earlier time points in our model to capture such changes is a compelling perspective that we will discuss as a key direction for future work.
(2) One limitation of the tracing methodology (Figure 1) that could be improved is sample size, as only 2 mice have been used. Moreover, it would be interesting to conduct the same tracing experiments in APP mice to see how these projections are affected by amyloid pathology.
We acknowledge this limitation and will increase the sample size for the tracing experiments in the revised manuscript. However, we wish to clarify that the tracing was performed in a separate cohort of young animals specifically to characterize baseline MS cholinergic projections independently of any amyloid-related disturbances. While we agree that replicating these experiments in APP mice would be of great interest, this falls outside the scope of the current study and will be highlighted as an important direction for future work.
(3) Figure 3 measurements included the whole hippocampal formation, but a region-specific analysis would be warranted as the authors discuss specific accumulation areas.
We agree with this pertinent suggestion. We will perform and report region-specific analyses of the hippocampal formation in the revised manuscript, in line with our discussion of specific amyloid accumulation areas.
(4) Figure 5 novel object recognition comparisons use a group of 10 sec exploration, which is unclear why. Novel vs familiar comparisons and reporting of discrimination indexes are considered more robust measurements to report.
We respectfully maintain our analytical approach. As the test phase was terminated upon reaching a predefined cumulative exploration time of 20 seconds rather than using a fixed trial duration, computing a discrimination index is not appropriate in this context, as total exploration time is constrained by design. We instead followed the validated protocol described by Leger et al. (2013, Nature Protocols; PMID: 24263092), which controls for inter-individual differences in exploratory motivation by fixing cumulative exploration time, ensuring equivalent sampling conditions across animals. We will clarify this methodological choice in the revised manuscript.
(5) Interictal spike detection would benefit from more methodological detail and examples of spikes detected. Reference 72 does not seem to detail interictal spike detection. Moreover, when during sleep do these spikes happen? It has been shown that they occur primarily during REM sleep when mice show cholinergic hyperactivity (PMID: 37714307). From panel 7B, it seems they occur during NREM, which may be explained by a diminished drive of cholinergic circuits to drive spikes in these mice (vs REM in younger mice). Thus, a NREM vs REM vs Wake analysis will be insightful.
We appreciate this constructive suggestion. We will provide additional methodological detail on interictal spike detection, include representative examples, and perform a vigilance state-specific analysis in the revised manuscript. We agree this will provide valuable mechanistic insight and will update the reference accordingly.
Reviewer #2 (Public review):
Summary:
In this study, Nollet and colleagues sought to determine whether selective amyloid pathology confined to medial septal (MS) cholinergic neurons is sufficient to recapitulate the prodromal Alzheimer's disease-like phenotypes observed in global AppNL-G-F knock-in mice. To this end, the authors employed a cell-type-specific AAV-mediated approach to selectively express the familial AppNL-G-F allele in MS-ChAT neurons, and subsequently characterized sleep-wake architecture, EEG spectral features, cognitive function, emotional behavior, and histological changes over 13-14 months. By comparing these mice with global AppNL-G-F knock-in mice and with mice in which MS-ChAT neurons were selectively ablated via caspase expression, the authors found that cholinergic cell lesioning recapitulated most disease phenotypes, suggesting that cholinergic loss, rather than amyloid deposition, is a likely driver of these phenotypes.
Strengths:
The study has several notable strengths. First, the experimental design is rigorous and well-controlled, employing three complementary mouse models that enable elegant causal inference. The use of cell-type-specific APP expression is a powerful approach for distinguishing the contributions of MS-ChAT neurons and amyloid deposition. Second, the combination of multiple behavioral assessments, EEG spectral analysis using FOOOF parameterization, and detailed histological quantification strengthens the validity of the conclusions. Third, the finding that caspase-induced cholinergic lesions largely recapitulate the cognitive and REM sleep phenotypes, while amyloid pathology contributes additional features such as epileptiform spikes and astrogliosis, represents an important mechanistic dissection.
Thank you for this positive assessment and for recognizing the rigor of our experimental design, the value of our multi-modal approach, and the mechanistic significance of our cholinergic lesion comparison. We will address the weaknesses below point by point.
Weaknesses:
Despite the overall strength of the study, several limitations warrant consideration. First, the mechanism by which amyloid is "broadcast" from MS-ChAT terminals to distant brain regions remains unclear. The authors do not definitively determine whether the amyloid detected in hippocampal and cortical regions represents released soluble Aβ, transported APP fragments, or amyloid derived from degenerating axons. Second, while the authors demonstrate that MS-ChAT cell loss correlates with cognitive, emotional, and REMS deficits, the causal relationship among these phenomena and the specific circuits involved remains unresolved.
Regarding amyloid broadcasting, we fully acknowledge that the precise mechanism remains to be elucidated; while this was not a primary objective of the study, it represents a fascinating and unexpected finding that we will discuss more carefully as an open question for future investigation. Regarding the causal relationship between MS<sup>ChAT</sup> cell loss and the observed phenotypes, we agree that the specific circuits involved remain to be fully resolved; however, we would like to emphasize that the convergent evidence from our three complementary models (and in particular the recapitulation of cognitive and REM sleep deficits by selective cholinergic ablation) provides strong causal support for MS<sup>ChAT</sup> neuronal loss as a key driver of these phenotypes, independent of amyloid deposition per se.
Reviewer #3 (Public review):
Summary:
The central idea of the study is strong and potentially important: that the vulnerability of the cholinergic medial-septal population can account for a substantial fraction of prodromal-like AD phenotypes, thereby shifting part of the mechanistic focus from cortex-centered pathology to subcortical neuromodulatory circuit failure. The work has several notable strengths. The authors combine circuit mapping, calcium photometry, longitudinal EEG/EMG sleep phenotyping, histology, behavior, and a caspase-based lesion comparison to build a multi-level case for medial septal cholinergic involvement in REM Sleep and memory phenotypes. The inclusion of both a focal amyloid model and a partial cholinergic ablation model is especially valuable because it attempts to separate effects of Ch-neuronal loss from effects of amyloid itself.
However, the manuscript has several issues, from manuscript formatting to experimental design, overarching statements, insufficient exclusion of alternative explanations, incomplete quantification details for key histological results, a discussion that often moves beyond the actual data into speculative translational framing, and a discussion that completely ignores the early presence of p-tau in human AD patients and even lacks supplementary materials.
Strengths:
(1) The conceptual premise is compelling: cholinergic basal forebrain vulnerability is a real and important feature of AD, and testing whether selective medial septal cholinergic pathology can drive REM sleep and cognitive phenotypes is mechanistically interesting and clinically relevant.
(2) The experimental framework is broad and generally thoughtful, spanning anatomy, function, sleep architecture, EEG spectral parameterization, behavior, and histopathology.
(3) The projection mapping and photometry provide a useful systems-level introduction, establishing that MSChAT neurons are Wake/REM sleep-active and project strongly to hippocampal and cortical targets before the disease manipulations are introduced.
(4) The MSΔChAT comparison group is valuable because it allows the authors to argue that some phenotypes track with cholinergic loss rather than amyloid per se.
(5) The longitudinal sleep analysis is one of the strongest parts of the study, especially the emphasis on REM sleep quantity and bout architecture over time rather than relying only on an endpoint comparison.
Thank you for acknowledging the compelling conceptual premise of our study, the thoughtful and broad experimental framework, and the value of our longitudinal sleep analysis and lesion comparison. We will address all concerns raised below point by point.
Weaknesses:
(1) The title overreaches in its use of "prodromal phase." In the clinic, "prodromal AD" denotes a biomarker‑positive, pre‑dementia phase with subtle, progressive cognitive decline before widespread neurodegeneration, whereas here the authors demonstrate substantial cholinergic degeneration alongside cognitive impairment, which corresponds to advanced pathology within these models rather than a clinically prodromal stage. Moreover, APP knock‑in mice are amyloid‑centric, lack tau pathology, and don't recapitulate human disease staging; therefore, it would be better to avoid terms used for AD staging in the clinic. A more accurate framing of the title would be "Modeling the prodromal-like phase in an Alzheimer's disease mouse model".
This is a valid point. We agree that the term “prodromal phase” requires more careful framing in the context of animal models, and we will revise the title and relevant statements accordingly. We would like to note, however, that the REM sleep disturbances we report seem to emerge prior to overt cognitive decline in our longitudinal analysis, which we consider to reflect a prodromal-like feature of the model. Nevertheless, we will adopt more precise terminology throughout the manuscript to avoid conflation with clinical staging criteria.
(2) The opening statement in the abstract (line no 22) is overstated. Current evidence supports that changes in REM sleep, slow‑wave sleep disruption, and excessive daytime sleepiness are associated with a higher risk of AD and reflect early involvement of brain regions vulnerable to AD proteinopathy. No study indicates that REM sleep changes per se are a strong predictor on their own. For example, Jin et 2025 studied REM latency in AD and concluded that prolonged REM latency may be a marker of early neurodegeneration (PMID: 39868572). Thus, the opening statements need to be modified.
We appreciate this comment and will carefully nuance our opening statement to better reflect the current state of evidence. However, we respectfully note that several reports, including Pase et al. (Neurology, 2017; PMID: 28835407) and Ibrahim et al. (Sleep, 2024; PMID: 38001022), have demonstrated that REM sleep loss is associated with increased risk of incident neurodegenerative disorders, particularly Alzheimer's disease, supporting the broader validity of our framing. We will revise the statement to more accurately capture the complexity of this relationship while preserving its scientific relevance.
(3) Line 63: The current phrasing of neuromodulators being also essential for orchestrating sleep/wake states is very simplistic. Sleep/wake regulation is a highly complex process involving several interacting neurotransmitters and neuromodulatory systems. I recommend revising this sentence to reflect the broader, multi‑system nature of sleep/wake control.
We agree and will revise this sentence to better reflect the multi-system complexity of sleep/wake regulation, acknowledging the interplay between multiple neurotransmitters and neuromodulatory systems.
(4) Line 64: "ACh is required for the generation of REMS" is incomplete. The sentence implies REM sleep generation depends exclusively on ACh. Instead, the sentence must emphasize that ACh is a crucial component of a broader REM sleep circuitry and explain why it is critical for REM sleep.
We agree and will revise this sentence to clarify that ACh is a crucial component of a broader REM sleep-generating circuitry, rather than a sole requirement, while better contextualizing its specific contribution to REM sleep regulation.
(5) Line 65: The sentence "Importantly, reductions and alterations in REMS have emerged as strong predictors of clinical AD onset" (Reference 37) is an overstatement of the evidence; Peas et al. 2017 analyzed a dementia cohort that included AD cases and concluded: "Despite contemporary interest in slow-wave sleep and dementia pathology, our findings implicate REM sleep mechanisms as predictors of clinical dementia." The authors should rephrase this to reflect that the study examined REM sleep changes in a mixed dementia population with AD, rather than to establish REM alterations as strong, standalone predictors of AD onset.
We will revise this statement to more accurately reflect the evidence. We would like to note, however, that while the Pase et al. (2017) cohort included a mixed dementia population, 75% of incident dementia cases (24 out of 32) were consistent with Alzheimer's disease, lending meaningful support to the relevance of REM sleep alterations specifically in the context of AD. We will ensure this nuance is clearly conveyed in the revised manuscript.
(6) Lines 73-75 address human Alzheimer's studies and state that basal BF-Ch neurons are vulnerable to Aβ but largely omit the well-established contribution of early tau pathology. In human AD patients, p-tau accumulation in BF is an early event (Braak I-II) and is closely associated with BF-Ch neuronal loss and BF atrophy and has been documented extensively. By relying almost exclusively on Aβ-centric framing, the current text risks implying that BF-Ch degeneration is solely amyloid-driven, which is not accurate. Even though the mouse model used here is "amyloid-heavy" and lacks tau pathology, the introduction should acknowledge the role of p-tau (especially when the paragraph contextualizes human studies) and clarify that in humans, BF-Ch vulnerability reflects converging amyloid and tau insults, so that readers do not infer a purely amyloid-dependent mechanism from the way the background is presented.
We agree and will revise this section to acknowledge the well-established contribution of tau pathology to BF cholinergic neuronal vulnerability in human AD, including its early accumulation at Braak stages I-II. We wish to clarify, however, that the present study focuses exclusively on amyloid-driven mechanisms, and the introduction will be revised to ensure readers do not infer a purely amyloid-dependent mechanism in the broader human disease context.
(7) Line 92: and elsewhere in the manuscript, I recommend avoiding the term "prodromal phase" and instead using the phrase "prodromal-like phase in an AD mouse model". The authors should be more precise in describing the disease stage in animal models that don't recapitulate human disease staging and ensure that clinical staging terminology is specific to human studies.
As noted in our response to weakness (1), we will systematically revise the manuscript to replace “prodromal phase” with more precise terminology that clearly distinguishes our animal model findings from clinical disease staging.
(8) Age and duration of pathology are major concerns. The different models are not adequately matched for amyloid exposure duration and age at testing. Age is the strongest risk factor for AD, and varying both chronological age and time under pathology across groups is a major design flaw. In MSChAT-AppNL-G-F/GFP mice, AAV injection was delivered at 11-13 weeks of age, and animals were sacrificed at 13-14 months post-injection (roughly 15-16 months old), whereas AppNL-G-F/NL-G-F knock-in mice and APPWT were 13-14 months old at the time of termination. Thereby, there is a difference in the duration of Aβ exposure across models. This mismatch directly weakens comparisons such as the lower epileptiform spike counts in MSChAT-AppNL-G-F versus AppNL-G-F/NL-G-F mice, because differences could simply reflect shorter cumulative pathology exposure rather than a genuinely weaker circuit-specific effect.
The same issue affects the internal control logic of the MSΔChAT model, which is intended to isolate cholinergic neuron loss from amyloid aggregation. For this comparison to be clean, ages and exposure durations should be aligned as closely as possible. Instead, MSΔChAT mice are tested earlier than the AppNL-G-F/NL-G-F and MSChAT-AppNL-G-F/MSChAT-GFP cohorts, introducing a 4 to 7-month age gap that complicates attribution of phenotypic differences solely to cholinergic loss versus amyloid pathology.
Finally, the absence of sham-operated controls is a concern, as it prevents separating the effects of the surgical procedure and AAV delivery from those of amyloid expression or cholinergic ablation.
Thank you for raising these important points. Regarding age matching, we acknowledge that chronological ages are not perfectly aligned across groups; however, we wish to emphasize that the duration of amyloid pathology is carefully matched across models. Indeed, AAV injection in MS<sup>ChAT</sup>-AppNL-G-F mice marks the onset of amyloid expression, directly paralleling the onset of pathology from birth in App<sup>NL-G-F/NL-G-F</sup> knock-in mice. We believe pathology duration represents the most biologically relevant variable for comparison in this context, and we will clarify this in the revised manuscript. Regarding the MS<sup>ΔChAT</sup> cohort, animals were culled upon reaching a comparable degree of REM sleep loss, providing a functionally meaningful matching criterion. Finally, regarding sham-operated controls, we acknowledge this limitation; however, based on our experience, surgical procedure alone has negligible effects on the cellular populations under study, and the inclusion of an additional sham group across all experimental cohorts would have required a prohibitive number of animals, raising significant ethical concerns under the 3R principles. We will address these points more explicitly in the revised manuscript.
(9) Line 115 through 117: The text cites Figure 2D, but does not refer to Figure 2C for the statement "their phenotypes were then compared in detail with MSChAT-AppNL-G-F and AppNL-G-F/NL-G-F global knock-in mice that were aged at the same time". Figure 2C depicts D54D2 amyloid staining in MSChAT-GFP vs MSChAT-AppNL-G-F mice. For clarity and consistency, I suggest adding a Figure 2C notation to this sentence (e.g., "Figures 2A, 2C").
Thank you for this observation, we will correct the figure citation accordingly in the revised manuscript.
(10) In Figure 1C-D, the authors map MSChAT projection targets across a wide range of brain areas, including hippocampal subfields, mPFC, primary cortices, entorhinal cortex, olfactory bulb, thalamus, anterior hypothalamus, amygdala, and medial habenula, and identify several of these as substrates through which MSChAT activity could influence REM sleep and cognition. However, the lateral hypothalamic area (LHA) is conspicuously absent from both the listed projection targets and the tracing panels shown in Figure 1D, despite the anterior hypothalamus being reported as an innervated region.
This omission is notable given that LHA-MCH neurons are among the best-established REM-sleep-promoting neurons, and the authors themselves cite prior work implicating LHA-MCH neurons in the AppNL-G-F REM sleep phenotype (ref. 49, 107; line 403) as an alternative cell-circuit candidate, a claim they explicitly try to weigh against their own MSChAT-centered model in the discussion.
a) The MSChAT neurons are reported to be REM sleep- and wake-active (Figure 1A-B), the same vigilance-state profile as LHA-MCH neurons,<br />
b) The Discussion directly engages with LHA-MCH neurons as a competing/complementary REM sleep-generating mechanism, and<br />
c) The reported anterior hypothalamus innervation (Figure 3C) raises the question of whether MSChAT axons specifically innervate LHA, and whether any projections specifically to LHA or LHA-specific amyloid deposition were examined. Clarifying this would help position the proposed MSChAT-hippocampal circuit mechanism relative to the well-established LHA-MCH REM sleep node.
We appreciate this important observation. We will carefully re-examine our tracing data to determine whether MS<sup>ChAT</sup> axons specifically innervate the LHA, and whether amyloid deposition was detectable in this region in our MS<sup>ChAT</sup>-App<sup>NL-G-F</sup> model. We agree that clarifying the potential anatomical relationship between MS<sup>ChAT</sup> projections and LHA-MCH neurons is important to properly position our proposed circuit mechanism relative to this well-established REM sleep-promoting node, and we will address this in the revised manuscript.
(11) Line 125: "13- to 14-month-old MSChAT-AppNL-G-F mice immunohistochemical analyses employing the amyloid-specific antibodies....", in the methods section (Line 652) the authors mention MSChAT-AppNL-G-F and MSChAT-GFP mice were perfused 13-14 months after AAV injection (age at the time of injection was 11-13 weeks of age). This leaves the question of how they have 13- to 14-month-old MSChAT-AppNL-G-F mice available to study Amyloid-β load.
Thank you for catching this inconsistency. We confirm that this is an error in the manuscript: line 125 should read “15-16 month-old” referring to the chronological age of the animals at the time of perfusion, rather than “13-14 months,” which corresponds to the duration of AAV expression. We will correct this in the revised manuscript.
(12) Line 174-175: As currently written, the sentence could be read as both wild-type and homozygous AppNL-G-F/NL-G-F mice received AAV injections and were then aged 13-14 months post‑injection. In fact, the Methods clearly state that knock‑in mice are simply aged from birth without any AAV manipulation. The sentence should be rephrased to avoid suggesting that global APP knock‑in animals are part of the AAV‑injected cohorts.
Thank you for flagging this ambiguity. We will revise the sentence to clearly distinguish between AAV-injected and global knock-in cohorts in the revised manuscript.
(13) Lines 182-183, 196-197, and 209 refer to "Supplementary information" and imply that detailed behavioral data and analyses are provided in that section. However, in the current submission, the supplementary material consists only of Figures S1-S7 (Amyloid marker and cerebral vasculature, Aβ in hippocampus, GABA and glutamatergic neurotransmission, and sleep/wake parameters) and does not include supplementary figures or tables for the behavioral assays described in the main text. This discrepancy makes it impossible to verify the full behavioral dataset and the analyses referred to in the results section. The authors should carefully check the submission package and ensure that all referenced supplementary figures, tables, and detailed behavioral results are included and appropriately labeled.
The supplementary information referenced in the main text will be provided in full in the revised manuscript, together with analyzed datasets and analysis scripts, in accordance with eLife's data sharing policy.
(14) The lack of details for histological quantification is a major concern for a manuscript in which major conclusions hinge on Aβ load and MS-Ch neuronal counts. The histological quantification section is severely under-specified. The authors describe a 23% MSChAT loss, differences in regional Aβ burden, and a vascular association; however, the methods section is strangely silent about the quantification pipeline. For Aβ quantification, it is not clear whether "load" reflects percent positive area, plaque counts, or another metric; which Fiji thresholding algorithm(s) were used; how ROIs were defined; how staining batch effects were controlled; and how autofluorescence was normalized. For neuronal counts, the strategy for identifying and counting ChAT-positive neurons, normalization, and blinding are not described. There are no details on section spacing, axis of counting, the number of sections counted per animal, or whether both hemispheres were analyzed. Given that the reported differences are modest and central to the main claims, a more detailed and rigorous description of the image-analysis pipeline is essential.
We agree that a comprehensive description of our histological quantification pipeline is essential. We will provide full methodological details in the revised manuscript, including: the metric used for Aβ load quantification, ROI definitions, Fiji/ImageJ thresholding algorithms (accounting for batch effects and autofluorescence normalization), as well as the strategy for identifying and counting ChAT-positive neurons, section spacing, number of sections per animal, hemisphere coverage, normalization, and blinding procedures. All ImageJ scripts will be made available to ensure full transparency and reproducibility.
(15) Statistical annotations in figures: There is inconsistency in how statistical significance is indicated across the figures. For example, in Figure 5C, the significance between MSΔChAT and AAV‑Aβ<sup>-</sup> is indicated by a connecting bracket (**), whereas the comparison between AAV‑Aβ<sup>-</sup> and AAV‑Aβ<sup>+</sup> is marked by asterisks (***) placed above AAV‑Aβ<sup>+</sup>. In addition, the single asterisk above KI-Aβ<sup>+</sup> does not clearly specify which pairwise comparison it refers to (e.g., AAV‑Aβ<sup>-</sup> vs WT‑Aβ<sup>-</sup> or another contrast). This heterogeneity makes it difficult to decipher exactly which group comparisons have been tested and found significant. The notation should be standardized and explicitly linked to the corresponding pairwise comparisons (for example, by using consistent brackets/lines and specifying all contrasts in the figure legend). Figures must be self-explanatory.
We acknowledge that the current statistical annotations can be difficult to interpret when multiple experimental groups are displayed within a single plot. While the notation is consistent across figures, we agree that clarity can be improved, and we will revise all figure annotations to explicitly link significance indicators to their corresponding pairwise comparisons, using standardized brackets throughout, with all contrasts clearly specified in the figure legends.
(16) Figure 5D statistical notation and group comparisons: The statistical markings in Figure 5D do not seem to match the results text and are difficult to interpret. The authors state that both MSΔChAT and AAV‑Aβ<sup>+</sup> mice lack a preference for the novel object compared with AAV‑Aβ<sup>-</sup> controls, yet the figure does not clearly indicate significance for MSΔChAT versus AAV‑Aβ<sup>-</sup>, and the notation over AAV‑Aβ<sup>+</sup> is ambiguous. As a result, it is unclear which group differences are being tested and reported. It would be preferable to use the standard convention of placing significance annotations directly over the experimental groups (e.g., AAV‑Aβ<sup>+</sup>, KI-Aβ<sup>++</sup>, MSΔChAT) or use notation above brackets to ensure that the figure labels are fully consistent with the statistical statements in the results.
We wish to clarify that in Figure 5D, the absence of novel object preference manifests as equal exploration of both objects (approximately 10 seconds each), such that comparisons against the 10-second chance level reflect this lack of preference. We will revise the annotations and figure legend to make the statistical comparisons explicit and fully consistent with the results text.
(17) The discussion contains many compelling ideas, but it needs pruning and recalibration. The best discussion points are those linking the lesion comparison to REM sleep/cognitive outcomes and those situating MS cholinergic neurons within broader REM sleep circuitry. The least convincing sections are those implying disease-stage equivalence, prion-like spread, and direct therapeutic implications without sufficient evidentiary support.
This is a constructive feedback, and we agree that the Discussion would benefit from pruning and recalibration. We will streamline it to focus on the most evidentially supported points, particularly those linking cholinergic loss to REM sleep and cognitive outcomes, while toning down or removing speculative statements regarding disease-stage equivalence, prion-like spreading mechanisms, and direct therapeutic implications.
(18) Line 448: The authors discussing reduced anxiety-like behavior in their model corroborates with the 3xTg mouse model (Ref: 116). Interestingly, they don't consider or include reports of anxiety-like disorders from human cohort studies that indicate the prevalence of higher anxiety and its association with preclinical and prodromal AD stages (SCD, MCI) and progression of AD. This apparent contradiction with the human literature is not discussed in the discussion section. The authors should explicitly address how their anxiolytic-like phenotype fits with clinical data (e.g., species differences, task specificity, disease stage, or model limitations) and clarify whether they view this as a limitation of the model or as evidence for a more complex relationship between amyloid, cholinergic dysfunction, and emotional behavior.
Thank you for raising this important point. We will expand the Discussion to address this apparent contradiction with the human literature. Indeed, while increased anxiety is reported in early AD stages, it tends to normalize or decrease at later stages (Botto et al., 2022; PMID: 35461471), which may partly reconcile our findings. In addition, anxiety-like phenotypes are highly inconsistent across AD mouse models, varying with model type, age, sex, and behavioral assay (Pentkowski et al., 2021; PMID: 33979573). Anxiety-related changes in human AD may reflect damage to brain regions beyond the MS cholinergic system, involving additional circuits and mechanisms not captured by our model.
(19) Line 654 states, "Comparable durations of amyloid pathology," but this is not fully substantiated, as the onset and progression of amyloid in the AAV-driven MSChAT-AppNL-G-F model versus the global AppNL-G-F knock-in model are not described. The data support comparison at a similar late-stage amyloid burden, but not necessarily equal duration of pathology.
We will nuance our wording at line 654 by replacing “comparable durations of amyloid pathology” with “comparable amyloid burden,” acknowledging that while both cohorts were aged for matched durations, the kinetics of amyloid progression may inherently differ between an AAV-driven focal model and a germline knock-in model.
