Author response:

The following is the authors’ response to the original reviews.

Reviewer #1 (Public review):

Summary:

Measurement of BOLD MR imaging has regularly found regions of the brain that show reliable suppression of BOLD responses during specific experimental testing conditions. These observations are to some degree unexplained, in comparison with more usual association between activation of the BOLD response and excitatory activation of the neurons (most tightly linked to synaptic activity) in the same brain location. This paper finds two patients whose brains were tested with both non-invasive functional MRI and with invasive insertion of electrodes, which allowed the direct recording of neuronal activity. The electrode insertions were made within the fusiform gyrus, which is known to process information about faces, in a clinical search for the sites of intractable epilepsy in each patient. The simple observation is that the electrode location in one patient showed activation of the BOLD response and activation of neuronal firing in response to face stimuli. This is the classical association. The other patient showed an informative and different pattern of responses. In this person, the electrode location showed a suppression of the BOLD response to face stimuli and, most interestingly, an associated suppression of neuronal activity at the electrode site.

Strengths:

Whilst these results are not by themselves definitive, they add an important piece of evidence to a long-standing discussion about the origins of the BOLD response. The observation of decreased neuronal activation associated with negative BOLD is interesting because, at various times, exactly the opposite association has been predicted. It has been previously argued that if synaptic mechanisms of neuronal inhibition are responsible for the suppression of neuronal firing, then it would be reasonable

Weaknesses:

The chief weakness of the paper is that the results may be unique in a slightly awkward way. The observation of positive BOLD and neuronal activation is made at one brain site in one patient, while the complementary observation of negative BOLD and neuronal suppression actually derives from the other patient. Showing both effects in both patients would make a much stronger paper.

We thank reviewer #1 for their positive evaluation of our paper. Obviously, we agree with the reviewer that the paper would be much stronger if BOTH effects – spike increase and decrease – would be found in BOTH patients in their corresponding fMRI regions (lateral and medial fusiform gyrus) (also in the same hemisphere). Nevertheless, we clearly acknowledge this limitation in the (revised) version of the manuscript (p.8: Material and Methods section).

Note that with respect to the fMRI data, our results are not surprising, as we indicate in the manuscript: BOLD increases to faces (relative to nonface objects) are typically found in the LatFG and BOLD decreases in the medialFG (in the revised version, we have added the reference to an early neuroimaging paper that describes this dissociation clearly:

Pelphrey, K. A., Mack, P. B., Song, A., Güzeldere, G., & McCarthy, G. Faces evoke spatially differentiated patterns of BOLD activation and deactivation. Neuroreport 14, 955–959 (2003).

This pattern of increase/decrease in fMRI can be appreciated in both patients on Figure 2, although one has to consider both the transverse and coronal slices to appreciate it.

Regarding electrophysiological data, in the current paper, one could think that P1 shows only increases to faces, and P2 would show only decreases (irrespective of the region). However, that is not the case since 11% of P1’s face-selective units are decreases (89% are increases) and 4% of P2’s face-selective units are increases. This has now been made clearer in the revised manuscript (p.5).

As the reviewer is certainly aware, the number and positions of the electrodes are based on strict clinical criteria, and we will probably never encounter a situation with two neighboring (macro-micro hybrid electrodes), one with microelectrodes ending up in the lateral MidFG, the other in the medial MidFG, in the same patient. If there is no clinical value for the patient, this cannot be done.

The only thing we can do is to strengthen these results in the future by collecting data on additional patients with an electrode either in the lateral or the medial FG, together with fMRI. But these are the only two patients we have been able to record so far with electrodes falling unambiguously in such contrasted regions and with large (and comparable) measures.

While we acknowledge that the results may be unique because of the use of 2 contrasted patients only (and this is why the paper is a short report), the data is compelling in these 2 cases, and we are confident that it will be replicated in larger cohorts in the future.

Finally, information regarding ethics approval has been provided in the paper.

Reviewer #2 (Public review):

Summary:

This is a short and straightforward paper describing BOLD fMRI and depth electrode measurements from two regions of the fusiform gyrus that show either higher or lower BOLD responses to faces vs. objects (which I will call face-positive and facenegative regions). In these regions, which were studied separately in two patients undergoing epilepsy surgery, spiking activity increased for faces relative to objects in the face-positive region and decreased for faces relative to objects in the face-negative region. Interestingly, about 30% of neurons in the face-negative region did not respond to objects and decreased their responses below baseline in response to faces (absolute suppression).

Strengths:

These patient data are valuable, with many recording sessions and neurons from human face-selective regions, and the methods used for comparing face and object responses in both fMRI and electrode recordings were robust and well-established. The finding of absolute suppression could clarify the nature of face selectivity in human fusiform gyrus since previous fMRI studies of the face-negative region could not distinguish whether face < object responses came from absolute suppression, or just relatively lower but still positive responses to faces vs. objects.

Weaknesses:

The authors claim that the results tell us about both 1) face-selectivity in the fusiform gyrus, and 2) the physiological basis of the BOLD signal. However, I would like to see more of the data that supports the first claim, and I am not sure the second claim is supported.

(1) The authors report that ~30% of neurons showed absolute suppression, but those data are not shown separately from the neurons that only show relative reductions. It is difficult to evaluate the absolute suppression claim from the short assertion in the text alone (lines 105-106), although this is a critical claim in the paper.

We thank reviewer #2 for their positive evaluation of our paper. We understand the reviewer’s point, and we partly agree. Where we respectfully disagree is that the finding of absolute suppression is critical for the claim of the paper: finding an identical contrast between the two regions in terms of RELATIVE increase/decrease of face-selective activity in fMRI and spiking activity is already novel and informative. Where we agree with the reviewer is that the absolute suppression could be more documented: it wasn’t, due to space constraints (brief report). We provide below an example of a neuron showing absolute suppression to faces (P2), as also requested in the recommendations to authors. In the frequency domain, there is only a face-selective response (1.2 Hz and harmonics) but no significant response at 6 Hz (common general visual response). In the time-domain, relative to face onset, the response drops below baseline level. It means that this neuron has baseline (non-periodic) spontaneous spiking activity that is actively suppressed when a face appears.

Author response image 1.

(2) I am not sure how much light the results shed on the physiological basis of the BOLD signal. The authors write that the results reveal "that BOLD decreases can be due to relative, but also absolute, spike suppression in the human brain" (line 120). But I think to make this claim, you would need a region that exclusively had neurons showing absolute suppression, not a region with a mix of neurons, some showing absolute suppression and some showing relative suppression, as here. The responses of both groups of neurons contribute to the measured BOLD signal, so it seems impossible to tell from these data how absolute suppression per se drives the BOLD response.

It is a fact that we find both kinds of responses in the same region. We cannot tell with this technique if neurons showing relative vs. absolute suppression of responses are spatially segregated for instance (e.g., forming two separate sub-regions) or are intermingled. And we cannot tell from our data how absolute suppression per se drives the BOLD response. In our view, this does not diminish the interest and originality of the study, but the statement "that BOLD decreases can be due to relative, but also absolute, spike suppression in the human brain” has been rephrased in the revised manuscript: "that BOLD decreases can be due to relative, or absolute (or a combination of both), spike suppression in the human brain”.

Reviewer #3 (Public review):

In this paper the authors conduct two experiments an fMRI experiment and intracranial recordings of neurons in two patients P1 and P2. In both experiments, they employ a SSVEP paradigm in which they show images at a fast rate (e.g. 6Hz) and then they show face images at a slower rate (e.g. 1.2Hz), where the rest of the images are a variety of object images. In the first patient, they record from neurons over a region in the mid fusiform gyrus that is face-selective and in the second patient, they record neurons from a region more medially that is not face selective (it responds more strongly to objects than faces). Results find similar selectivity between the electrophysiology data and the fMRI data in that the location which shows higher fMRI to faces also finds face-selective neurons and the location which finds preference to non faces also shows non face preferring neurons.

Strengths:

The data is important in that it shows that there is a relationship between category selectivity measured from electrophysiology data and category-selective from fMRI. The data is unique as it contains a lot of single and multiunit recordings (245 units) from the human fusiform gyrus - which the authors point out - is a humanoid specific gyrus.

Weaknesses:

My major concerns are two-fold:

(i) There is a paucity of data; Thus, more information (results and methods) is warranted; and in particular there is no comparison between the fMRI data and the SEEG data.

We thank reviewer #3 for their positive evaluation of our paper. If the reviewer means paucity of data presentation, we agree and we provide more presentation below, although the methods and results information appear as complete to us. The comparison between fMRI and SEEG is there, but can only be indirect (i.e., collected at different times and not related on a trial-by-trial basis for instance). In addition, our manuscript aims at providing a short empirical contribution to further our understanding of the relationship between neural responses and BOLD signal, not to provide a model of neurovascular coupling.

(ii) One main claim of the paper is that there is evidence for suppressed responses to faces in the non-face selective region. That is, the reduction in activation to faces in the non-face selective region is interpreted as a suppression in the neural response and consequently the reduction in fMRI signal is interpreted as suppression. However, the SSVEP paradigm has no baseline (it alternates between faces and objects) and therefore it cannot distinguish between lower firing rate to faces vs suppression of response to faces.

We understand the concern of the reviewer, but we respectfully disagree that our paradigm cannot distinguish between lower firing rate to faces vs. suppression of response to faces. Indeed, since the stimuli are presented periodically (6 Hz), we can objectively distinguish stimulus-related activity from spontaneous neuronal firing. The baseline corresponds to spikes that are non-periodic, i.e., unrelated to the (common face and object) stimulation. For a subset of neurons, even this non-periodic baseline activity is suppressed, above and beyond the suppression of the 6 Hz response illustrated on Figure 2. We mention it in the manuscript, but we agree that we do not present illustrations of such decrease in the time-domain for SU, which we did not consider as being necessary initially (please see below for such presentation).

(1) Additional data: the paper has 2 figures: figure 1 which shows the experimental design and figure 2 which presents data, the latter shows one example neuron raster plot from each patient and group average neural data from each patient. In this reader's opinion this is insufficient data to support the conclusions of the paper. The paper will be more impactful if the researchers would report the data more comprehensively.

We answer to more specific requests for additional evidence below, but the reviewer should be aware that this is a short report, which reaches the word limit. In our view, the group average neural data should be sufficient to support the conclusions, and the example neurons are there for illustration. And while we cannot provide the raster plots for a large number of neurons, the anonymized data is made available at:

(a) There is no direct comparison between the fMRI data and the SEEG data, except for a comparison of the location of the electrodes relative to the statistical parametric map generated from a contrast (Fig 2a,d). It will be helpful to build a model linking between the neural responses to the voxel response in the same location - i.e., estimate from the electrophysiology data the fMRI data (e.g., Logothetis & Wandell, 2004).

As mentioned above the comparison between fMRI and SEEG is indirect (i.e., collected at different times and not related on a trial-by-trial basis for instance) and would not allow to make such a model.

(b) More comprehensive analyses of the SSVEP neural data: It will be helpful to show the results of the frequency analyses of the SSVEP data for all neurons to show that there are significant visual responses and significant face responses. It will be also useful to compare and quantify the magnitude of the face responses compared to the visual responses.

The data has been analyzed comprehensively, but we would not be able to show all neurons with such significant visual responses and face-selective responses.

(c) The neuron shown in E shows cyclical responses tied to the onset of the stimuli, is this the visual response?

Correct, it’s the visual response at 6 Hz.

If so, why is there an increase in the firing rate of the neuron before the face stimulus is shown in time 0?

Because the stimulation is continuous. What is displayed at 0 is the onset of the face stimulus, with each face stimulus being preceded by 4 images of nonface objects.

The neuron's data seems different than the average response across neurons; This raises a concern about interpreting the average response across neurons in panel F which seems different than the single neuron responses

The reviewer is correct, and we apologize for the confusion. This is because the average data on panel F has been notch-filtered for the 6 Hz (and harmonic responses), as indicated in the methods (p.11): ‘a FFT notch filter (filter width = 0.05 Hz) was then applied on the 70 s single or multi-units time-series to remove the general visual response at 6 Hz and two additional harmonics (i.e., 12 and 18 Hz)’.

Here is the same data without the notch-filter (the 6Hz periodic response is clearly visible):

Author response image 2.

For sake of clarity, we prefer presenting the notch-filtered data in the paper, but the revised version makes it clear in the figure caption that the average data has been notch-filtered.

(d) Related to (c) it would be useful to show raster plots of all neurons and quantify if the neural responses within a region are homogeneous or heterogeneous. This would add data relating the single neuron response to the population responses measured from fMRI. See also Nir 2009.

We agree with the reviewer that this is interesting, but again we do not think that it is necessary for the point made in the present paper. Responses in these regions appear rather heterogenous, and we are currently working on a longer paper with additional SEEG data (other patients tested for shorter sessions) to define and quantify the face-selective neurons in the MidFusiform gyrus with this approach (without relating it to the fMRI contrast as reported here).

(e) When reporting group average data (e.g., Fig 2C,F) it is necessary to show standard deviation of the response across neurons.

We agree with the reviewer and have modified Figure 2 accordingly in the revised manuscript.

(f) Is it possible to estimate the latency of the neural responses to face and object images from the phase data? If so, this will add important information on the timing of neural responses in the human fusiform gyrus to face and object images.

The fast periodic paradigm to measure neural face-selectivity has been used in tens of studies since its original reports:

• in EEG: Rossion et al., 2015: https://doi.org/10.1167/15.1.18

• in SEEG: Jonas et al., 2016: https://doi.org/10.1073/pnas.1522033113

In this paradigm, the face-selective response spreads to several harmonics (1.2 Hz, 2.4 Hz, 3.6 Hz, etc.) (which are summed for quantifying the total face-selective amplitude). This is illustrated below by the averaged single units’ SNR spectra across all recording sessions for both participants.

Author response image 3.

There is no unique phase-value, each harmonic being associated with a phase-value, so that the timing cannot be unambiguously extracted from phase values. Instead, the onset latency is computed directly from the time-domain responses, which is more straightforward and reliable than using the phase. Note that the present paper is not about the specific time-courses of the different types of neurons, which would require a more comprehensive report, but which is not necessary to support the point made in the present paper about the SEEG-fMRI sign relationship.

(g) Related to (e) In total the authors recorded data from 245 units (some single units and some multiunits) and they found that both in the face and nonface selective most of the recoded neurons exhibited face -selectivity, which this reader found confusing: They write “ Among all visually responsive neurons, we found a very high proportion of face-selective neurons (p < 0.05) in both activated and deactivated MidFG regions (P1: 98.1%; N = 51/52; P2: 86.6%; N = 110/127)’. Is the face selectivity in P1 an increase in response to faces and P2 a reduction in response to faces or in both it’s an increase in response to faces

Face-selectivity is defined as a DIFFERENTIAL response to faces compared to objects, not necessarily a larger response to faces. So yes, face-selectivity in P1 is an increase in response to faces and P2 a reduction in response to faces.

Additional methods

(a) it is unclear if the SSVEP analyses of neural responses were done on the spikes or the raw electrical signal. If the former, how is the SSVEP frequency analysis done on discrete data like action potentials?

The FFT is applied directly on spike trains using Matlab’s discrete Fourier Transform function. This function is suitable to be applied to spike trains in the same way as to any sampled digital signal (here, the microwires signal was sampled at 30 kHz, see Methods).

In complementary analyses, we also attempted to apply the FFT on spike trains that had been temporally smoothed by convolving them with a 20ms square window (Le Cam et al., 2023, cited in the paper ). This did not change the outcome of the frequency analyses in the frequency range we are interested in. We have also added one sentence with information in the methods section about spike detection (p.10).

(b) it is unclear why the onset time was shifted by 33ms; one can measure the phase of the response relative to the cycle onset and use that to estimate the delay between the onset of a stimulus and the onset of the response. Adding phase information will be useful.

The onset time was shifted by 33ms because the stimuli are presented with a sinewave contrast modulation (i.e., at 0ms, the stimulus has 0% contrast). 100% contrast is reached at half a stimulation cycle, which is 83.33ms here, but a response is likely triggered before reaching 100% contrast. To estimate the delay between the start of the sinewave (0% contrast) and the triggering of a neural response, we tested 7 SEEG participants with the same images presented in FPVS sequences either as a sinewave contrast (black line) modulation or as a squarewave (i.e. abrupt) contrast modulation (red line). The 33ms value is based on these LFP data obtained in response to such sinewave stimulation and squarewave stimulation of the same paradigm. This delay corresponds to 4 screen refresh frames (120 Hz refresh rate = 8.33ms by frame) and 35% of the full contrast, as illustrated below (please see also Retter, T. L., & Rossion, B. (2016). Uncovering the neural magnitude and spatio-temporal dynamics of natural image categorization in a fast visual stream. Neuropsychologia, 91, 9–28).

Author response image 4.

(2) Interpretation of suppression:

The SSVEP paradigm alternates between 2 conditions: faces and objects and has no baseline; In other words, responses to faces are measured relative to the baseline response to objects so that any region that contains neurons that have a lower firing rate to faces than objects is bound to show a lower response in the SSVEP signal. Therefore, because the experiment does not have a true baseline (e.g. blank screen, with no visual stimulation) this experimental design cannot distinguish between lower firing rate to faces vs suppression of response to faces.

The strongest evidence put forward for suppression is the response of non-visual neurons that was also reduced when patients looked at faces, but since these are non-visual neurons, it is unclear how to interpret the responses to faces.

We understand this point, but how does the reviewer know that these are non-visual neurons? Because these neurons are located in the visual cortex, they are likely to be visual neurons that are not responsive to non-face objects. In any case, as the reviewer writes, we think it’s strong evidence for suppression.

We thank all three reviewers for their positive evaluation of our paper and their constructive comments.

Author Response

The following is the authors’ response to the previous reviews.

Reviewer #1:

Concerns Public Review:

1)The framing of 'infinite possible types of conflict' feels like a strawman. While they might be true across stimuli (which may motivate a feature-based account of control), the authors explore the interpolation between two stimuli. Instead, this work provides confirmatory evidence that task difficulty is represented parametrically (e.g., consistent with literatures like n-back, multiple object tracking, and random dot motion). This parametric encoding is standard in feature-based attention, and it's not clear what the cognitive map framing is contributing.

Suggestion:

1) 'infinite combinations'. I'm frankly confused by the authors response. I don't feel like the framing has changed very much, besides a few minor replacements. Previous work in MSIT (e.g., by the author Zhongzheng Fu) has looked at whether conflict levels are represented similarly across conflict types using multivariate analyses. In the paper mentioned by Ritz & Shenhav (2023), the authors looked at whether conflict levels are represented similarly across conflict types using multivariate analyses. It's not clear what this paper contributes theoretically beyond the connections to cognitive maps, which feel like an interpretative framework rather than a testable hypothesis (i.e., these previous paper could have framed their work as cognitive maps).

Response: We acknowledge the limitations inherent in our experimental design, which prevents us from conducting a strict test of the cognitive space view. In our previous revision, we took steps to soften our conclusions and emphasize these limitations. However, we still believe that our study offers valuable and novel insights into the cognitive space, and the tests we conducted are not merely strawman arguments.

Specifically, our study aimed to investigate the fundamental principles of the cognitive space view, as we stated in our manuscript that “the representations of different abstract information are organized continuously and the representational geometry in the cognitive space is determined by the similarity among the represented information (Bellmund et al., 2018)”. While previous research has applied multivariate analyses to understand cognitive control representation, no prior studies had directedly tested the two key hypotheses associated with cognitive space: (1) that cognitive control representation across conflict types is continuous, and (2) that the similarity among representations of different conflict types is determined by their external similarity.

Our study makes a unique contribute by directly testing these properties through a parametric manipulation of different conflict types. This approach differs significantly from previous studies in two ways. First, our parametric manipulation involves more than two levels of conflict similarity, enabling us to directly test the two critical hypotheses mentioned above. Unlike studies such as Fu et al. (2022) and other that have treated different conflict types categorically, we introduced a gradient change in conflict similarity. This differentiation allowed us to employ representational similarity analysis (RSA) over the conflict similarity, which goes beyond mere decoding as utilized in prior work (see more explanation below for the difference between Fu et al., 2022 and our study [1]).

Second, our parametric manipulation of conflict types differs from previous studies that have manipulated task difficulty, and the modulation of multivariate pattern similarity observed in our study could not be attributed by task difficulty. Previous research, including the Ritz & Shenhav (2023) (see below explanation[2]), has primarily shown that task difficulty modulates univoxel brain activation. A recent work by Wen & Egner (2023) reported a gradual change in the multivariate pattern of brain activations across a wide range of frontoparietal areas, supporting the reviewer’s idea that “task difficulty is represented parametrically”. However, we do not believe that our results reflect the task difficulty representation. For instance, in our study, the spatial Stroop-only and Simon-only conditions exhibited similar levels of difficulty, as indicated by their relatively comparable congruency effects (Fig. S1). Despite this similarity in difficulty, we found that the representational similarity between these two conditions was the lowest (see revised Fig. S4, the most off-diagonal value). This observation aligns more closely with our hypothesis that these two conditions are most dissimilar in terms of their conflict types.

[1] Fu et al. (2022) offers important insights into the geometry of cognitive space for conflict processing. They demonstrated that Simon and flanker conflicts could be distinguished by a decoder that leverages the representational geometry within a multidimensional space. However, their model of cognitive space primarily relies on categorical definitions of conflict types (i.e., Simon versus flanker), rather than exploring a parametric manipulation of these conflict types. The categorical manipulations make it difficult to quantify conceptual similarity between conflict types and hence limit the ability to test whether neural representations of conflict capture conceptual similarity. To the best of our knowledge, no previous studies have manipulated the conflict types parametrically. This gap highlights a broader challenge within cognitive science: effectively manipulating and measuring similarity levels for conflicts, as well as other high-level cognitive processes, which are inherently abstract. We therefore believe our parametric manipulation of conflict types, despite its inevitable limitations, is an important contribution to the literature.

We have incorporated the above statements into our revised manuscript: Methodological implications. Previous studies with mixed conflicts have applied mainly categorical manipulations of conflict types, such as the multi-source interference task (Fu et al., 2022) and color Stroop-Simon task (Liu et al., 2010). The categorical manipulations make it difficult to quantify conceptual similarity between conflict types and hence limit the ability to test whether neural representations of conflict capture conceptual similarity. To the best of our knowledge, no previous studies have manipulated the conflict types parametrically. This gap highlights a broader challenge within cognitive science: effectively manipulating and measuring similarity levels for conflicts, as well as other high-level cognitive processes, which are inherently abstract. The use of an experimental paradigm that permits parametric manipulation of conflict similarity provides a way to systematically investigate the organization of cognitive control, as well as its influence on adaptive behaviors.

[2] The work by Ritz & Shenhav (2023) indeed applied multivariate analyses, but they did not test the representational similarity across different levels of task difficulty in a similar way as our investigation into different levels of conflict types, neither did they manipulated conflict types as our study. They first estimated univariate brain activations that were parametrically scaled by task difficulty (e.g., target coherence), yielding one map of parameter estimates (i.e., encoding subspace) for each of the target coherence and distractor congruence. The multivoxel patterns from the above maps were correlated to test whether the target coherence and distractor congruence share the similar neural encoding. It is noteworthy that the encoding of task difficulty in their study is estimated at the univariate level, like the univariate parametric modulation analysis in our study. The representational similarity across target coherence and distractor congruence was the second-order test and did not reflect the similarity across different difficulty levels. Though, we have found another study (Wen & Egner, 2023) that has directly tested the representational similarity across different levels of task difficulty, and they observed a higher representational similarity between conditions with similar difficulty levels within a wide range of brain regions.

Reference:

Wen, T., & Egner, T. (2023). Context-independent scaling of neural responses to task difficulty in the multiple-demand network. Cerebral Cortex, 33(10), 6013-6027. https://doi.org/10.1093/cercor/bhac479

Fu, Z., Beam, D., Chung, J. M., Reed, C. M., Mamelak, A. N., Adolphs, R., & Rutishauser, U. (2022). The geometry of domain-general performance monitoring in the human medial frontal cortex. Science (New York, N.Y.), 376(6593), eabm9922. https://doi.org/10.1126/science.abm9922

Ritz, H., & Shenhav, A. (2023). Orthogonal neural encoding of targets and distractors supports multivariate cognitive control. https://doi.org/10.1101/2022.12.01.518771 Another issue is suggesting mixtures between two types of conflict may be many independent sources of conflict. Again, this feels like the strawman. There's a difference between infinite combinations of stimuli on the one hand, and levels of feature on the other hand. The issue of infinite stimuli is why people have proposed feature-based accounts, which are often parametric, eg color, size, orientation, spatial frequency. Mixing two forms of conflict is interesting, but the task limitations (i.e., highly correlated features) prevent an analysis of whether these are truly mixed (or eg reflect variations on just one of the conflict types). Without being able to compare a mixture between types vs levels of only one type, it's not clear what you can draw from these results re: how these are combined (and not clear how it reconciles the debate between general and specific).

Response: As the reviewer pointed out, a feature (or a parameterization) is an efficient way to encode potentially infinite stimuli. This is the same idea as our hypothesis: different conflict types are represented in a cognitive space akin to concrete features such as a color spectrum. This concept can be illustrated in the figure below.

Author response image 1.

We would like to clarify that in our study we have manipulated five levels of conflict types, but they all originated from two fundamental sources: vertically spatial Stroop and horizontally Simon conflicts. We agree that the mixture of these two sources does not inherently generate additional conflict sources. However, this mixture does influence the similarity among different conflict conditions, which provides essential variability that is crucial for testing the core hypotheses (i.e., continuity and similarity modulation, see the response above) of the cognitive space view. This clarification is crucial as the reviewer’s impression might have been influenced by our introduction, where we repeatedly emphasized multiple sources of conflicts. Our aim in the introduction was to outline a broader conceptual framework, which might not directly reflect the specific design of our current study. Recognizing the possibility of misinterpretation, we have adjusted our introduction and discussion to place less emphasis on the variety of possible conflict sources. For example, we have removed the expression “The large variety of conflict sources implies that there may be innumerable number of conflict conditions” from the introduction. As we have addressed in the previous response, the observed conflict similarity effect could not be attributed to merely task difficulty. Similarly, the mixture of spatial Stroop and Simon conflicts should not be attributed to one conflict source only; doing so would oversimplify it to an issue of task difficulty, as it would imply that our manipulation of conflict types merely represented varying levels of a single conflict, akin to manipulating task difficulty when everything else being equal. Importantly, the mixed conditions differ from variations along a single conflict source in that they also incorporate components of the other conflict source, thereby introducing difference beyond that would be found within variances of a single conflict source. There are a few additional evidence challenging the single dimension assumption. In our previous revisions, we compared model fittings between the Cognitive-Space model and the Stroop-/Simon-only models, and results showed that the CognitiveSpace model (BIC = 5377093) outperformed the Stroop-Only (BIC = 5377122) and Simon-Only (BIC = 5377096) models. This suggests that mixed conflicts might not be solely reflective of either Stroop or Simon sources, although we did not include these results due to concerns raised by reviewers about the validity of such comparisons, given the high anticorrelation between the two dimensions. Furthermore, Fu et al. (2022) demonstrated that the mixture of Simon and Flanker conflicts (the sf condition) is represented as the vector sum of the Flanker and Simon dimensions within their space model, indicating a compositional nature. Similarly, our mixed conditions are combinations of Stroop and Simon conflicts, and it is plausible that these mixtures represent a fusion of both Stroop and Simon components, rather than just one. Thus, we disagree that the mixture of conflicts is a strawman. In response to this concern, we have included a statement in our limitation section: “Another limitation is that in our design, the spatial Stroop and Simon effects are highly anticorrelated. This constraint may make the five conflict types represented in a unidimensional space (e.g., a circle) embedded in a 2D space. This limitation also means we cannot conclusively rule out the possibility of a real unidimensional space driven solely by spatial Stroop or Simon conflicts. However, this appears unlikely, as it would imply that our manipulation of conflict types merely represented varying levels of a single conflict, akin to manipulating task difficulty when everything else being equal. If task difficulty were the primary variable, we would expect to see greater representational similarity between task conditions of similar difficulty, such as the Stroop and Simon conditions, which demonstrates comparable congruency effects (see Fig. S1). Contrary to this, our findings reveal that the Stroop-only and Simon-only conditions exhibit the lowest representational similarity (Fig. S4). Furthermore, Fu et al. (2022) has shown that the representation of mixtures of Simon and Flanker conflicts was compositional, rather than reflecting single dimension, which also applies to our cases.”

My recommendation would be to dramatically rewrite to reduce the framing of this providing critical evidence in favor of cognitive maps, and being more overt about the limitations of this task. However, the authors are not required to make further revisions in eLife's new model, and it's not clear how my scores would change if they made those revisions (ie the conceptual limitations would remain, the claims would just now match the more limited scope).

Response: With the above rationales and the adjustments we have made in the manuscripts, we believe that we have thoroughly acknowledged and articulated the limitations of our study. Therefore, we have decided against a complete rewrite of the manuscript.

Public Review:

2) The representations within DLPFC appear to treat 100% Stoop and (to a lesser extent) 100% Simon differently than mixed trials. Within mixed trials, the RDM within this region don't strongly match the predictions of the conflict similarity model. It appears that there may be a more complex relationship encoded in this region.

Suggestion:

2) RSMs in the key region of interest. I don't really understand the authors response here either. e.g,. 'It is essential to clarify that our conclusions were based on the significant similarity modulation effect identified in our statistical analysis using the cosine similarity model, where we did not distinguish between the within-Stroop condition and the other four within-conflict conditions (Fig. 7A, now Fig. 8A). This means that the representation of conflict type was not biased by the seemingly disparities in the values shown here'. In Figure 1C, it does look like they are testing this model.

It seems like a stronger validation would test just the mixture trials (i.e., ignoring Simon-only and stroop-only). However, simon/stroop-only conditions being qualitatively different does beg the question of whether these are being represented parametrically vs categorically.

Response: We apologize for the confusion caused by our previous response. To clarify, our conclusions have been drawn based on the robust conflict similarity effect.

The conflict similarity regressor is defined by higher values in the diagonal cells (representing within-conflict similarity) than the off-diagonal cells (indicating between-conflict similarity), as illustrated in Fig. 1C and Fig. 8A (now Fig. 4B). It is important to note that this regressor may not be particularly sensitive to the variations within the diagonal cells. Our previous response aimed to emphasize that the inconsistencies observed along the diagonal do not contradict our core hypothesis regarding the conflict similarity effect.

We recognized that since the visualization in Fig. S4, based on the raw RSM (i.e., Pearson correlation), may have been influenced by other regressors in our model than the conflict similarity effect. To reflect pattern similarity with confounding factors controlled for, we have visualized the RSM by including only the fixed effect of the conflict similarity and the residual while excluding all other factors. As shown in the revised Figure S4, the difference between the within-Stroop and other diagonal cells was greatly reduced. Instead, it revealed a clear pattern where that the diagonal values were higher than the off-diagonal values in the incongruent condition, aligning with our hypothesis regarding the conflict similarity modulator. Although some visual distinctions persist within the five diagonal cells (e.g., in the incongruent condition, the Stroop, Simon, and StMSmM conditions appear slightly lower than StHSmL and StLSmM conditions), follow-up one-way ANOVAs among these five diagonal conditions showed no significant differences. This held true for both incongruent and congruent conditions, with Fs < 1. Thus, we conclude that there is no strong evidence supporting the notion that Simon- and spatial Stroop-only conditions are systematically different from other conflict types. As a result, we decided not to exclude these two conflict types from analysis.

Author response image 2.

The stronger conflict type similarity effect in incongruent versus congruent conditions. Shown are the summary representational similarity matrices for the right 8C region in incongruent (left) and congruent (right) conditions, respectively. Each cell represents the averaged Pearson correlation (after regressing out all factors except the conflict similarity) of cells with the same conflict type and congruency in the 1400×1400 matrix. Note that the seemingly disparities in the values of withinconflict cells (i.e., the diagonal) did not reach significance for either incongruent or congruent trials, Fs < 1.

Public Review:

3) To orthogonalized their variables, the authors need to employ a complex linear mixed effects analysis, with a potential influence of implementation details (e.g., high-level interactions and inflated degrees of freedom).

Suggestion:

3) The DF for a mixed model should not be the number of observations minus the number of fixed effects. The gold standard is to use satterthwaite correction (e.g. in Matlab, fixedEffects(lme,'DFMethod','satterthwaite')), or number of subjects - number of fixed effects (i.e. you want to generalize to new subjects, not just new samples from the same subjects). Honestly, running a 4-way interaction probably is probably using more degrees of freedom than are appropriate given the number of subjects.

Response: We concur with the reviewer’s comment that our previous estimation of degrees of freedom (DFs) was inaccurate. Following your suggestion, we have now applied the “Satterthwaite” approach to approximate the DFs for all our linear mixed effect model analyses. This adjustment has led to the correction of both DFs and p values. In the Methods section, we have mentioned this revision.

“We adjusted the t and p values with the degrees of freedom calculated through the Satterthwaite approximation method (Satterthwaite, 1946). Of note, this approach was applied to all the mixed-effect model analyses in this study.”

The application of this method has indeed resulted in a reduction of our statistical significance. However, our overall conclusions remained robust. Instead of the highly stringent threshold used in our previous version (Bonferonni corrected p < .0001), we have now adopted a relatively more lenient threshold of Bonferonni correction at p < 0.05, which is commonly employed in the literature. Furthermore, it is worth noting that the follow-up criteria 2 and 3 are inherently second-order analyses. Criterion 2 involves examining the interaction effect (conflict similarity effect difference between incongruent and congruent conditions), and criterion 3 involves individual correlation analyses. Due to their second-order nature, these criteria inherently have lower statistical power compared to criterion 1 (Blake & Gangestad, 2020). We thus have applied a more lenient but still typically acceptable false discovery rate (FDR) correction to criteria 2 and 3. This adjustment helps maintain the rigor of our analysis while considering the inherent differences in statistical power across the various criteria. We have mentioned this revision in our manuscript:

“We next tested whether these regions were related to cognitive control by comparing the strength of conflict similarity effect between incongruent and congruent conditions (criterion 2) and correlating the strength to behavioral similarity modulation effect (criterion 3). Given these two criteria pertain to second-order analyses (interaction or individual analyses) and thus might have lower statistical power (Blake & Gangestad, 2020), we applied a more lenient threshold using false discovery rate (FDR) correction (Benjamini & Hochberg, 1995) on the above-mentioned regions.”

With these adjustments, we consistently identified similar brain regions as observed in our previous version. Specifically, we found that only the right 8C region met the three criteria in the conflict similarity analysis. In addition, the regions meeting the criteria for the orientation effect included the FEF and IP2 in left hemisphere, and V1, V2, POS1, and PF in the right hemisphere. We have thoroughly revised the description of our results, updated the figures and tables in both the revised manuscript and supplementary material to accurately reflect these outcomes.

Reference:

Blake, K. R., & Gangestad, S. (2020). On Attenuated Interactions, Measurement Error, and Statistical Power: Guidelines for Social and Personality Psychologists. Pers Soc Psychol Bull, 46(12), 1702-1711. https://doi.org/10.1177/0146167220913363

Minor:

1. Figure 8 should come much earlier (e.g, incorporated into Figure 1), and there should be consistent terms for 'cognitive map' and 'conflict similarity'.

Response: We appreciate this suggestion. Considering that Figure 7 (“The crosssubject RSA model and the rationale”) also describes the models, we have merged Figure 7 and 8 and moved the new figure ahead, before we report the RSA results. Now you could find it in the new Figure 4, see below. We did not incorporate them into Figure 1 since Figure 1 is already too crowded.

Author response image 3.

Fig. 4. Rationale of the cross-subject RSA model and the schematic of key RSMs. A) The RSM is calculated as the Pearson’s correlation between each pair of conditions across the 35 subjects. For 17 subjects, the stimuli were displayed on the top-left and bottom-right quadrants, and they were asked to respond with left hand to the upward arrow and right hand to the downward arrow. For the other 18 subjects, the stimuli were displayed on the top-right and bottom-left quadrants, and they were asked to respond with left hand to the downward arrow and right hand to the upward arrow. Within each subject, the conflict type and orientation regressors were perfectly covaried. For instance, the same conflict type will always be on the same orientation. To de-correlate conflict type and orientation effects, we conducted the RSA across subjects from different groups. For example, the bottom-right panel highlights the example conditions that are orthogonal to each other on the orientation, response, and Simon distractor, whereas their conflict type, target and spatial Stroop distractor are the same. The dashed boxes show the possible target locations for different conditions. (B) and (C) show the orthogonality between conflict similarity and orientation RSMs. The within-subject RSMs (e.g., Group1-Group1) for conflict similarity and orientation are all the same, but the cross-group correlations (e.g., Group2-Group1) are different. Therefore, we can separate the contribution of these two effects when including them as different regressors in the same linear regression model. (D) and (E) show the two alternative models. Like the cosine model (B), within-group trial pairs resemble betweengroup trial pairs in these two models. The domain-specific model is an identity matrix. The domaingeneral model is estimated from the absolute difference of behavioral congruency effect, but scaled to 0 (lowest similarity) – 1 (highest similarity) to aid comparison. The plotted matrices in B-E include only one subject each from Group 1 and Group 2. Numbers 1-5 indicate the conflict type conditions, for spatial Stroop, StHSmL, StMSmM, StLSmH, and Simon, respectively. The thin lines separate four different sub-conditions, i.e., target arrow (up, down) × congruency (incongruent, congruent), within each conflict type.

In our manuscript, the term “cognitive map/space” was used when explaining the results in a theoretical perspective, whereas the “conflict similarity” was used to describe the regressor within the RSA. These terms serve distinct purposes in our study and cannot be interchangeably substituted. Therefore, we have retained them in their current format. However, we recognize that the initial introduction of the “Cognitive-Space model” may have appeared somewhat abrupt. To address this, we have included a brief explanatory note: “The model described above employs the cosine similarity measure to define conflict similarity and will be referred to as the Cognitive-Space model.”

Author Response

The following is the authors’ response to the original reviews.

Reviewer #1:

People can perform a wide variety of different tasks, and a long-standing question in cognitive neuroscience is how the properties of different tasks are represented in the brain. The authors develop an interesting task that mixes two different sources of difficulty, and find that the brain appears to represent this mixture on a continuum, in the prefrontal areas involved in resolving task difficulty. While these results are interesting and in several ways compelling, they overlap with previous findings and rely on novel statistical analyses that may require further validation.

Strengths

1) The authors present an interesting and novel task for combining the contributions of stimulus-stimulus and stimulus-response conflict. While this mixture has been measured in the multi-source interference task (MSIT), this task provides a more graded mixture between these two sources of difficulty

2) The authors do a good job triangulating regions that encoding conflict similarity, looking for the conjunction across several different measures of conflict encoding

3) The authors quantify several salient alternative hypothesis and systematically distinguish their core results from these alternatives

4) The question that the authors tackle is of central theoretical importance to cognitive control, and they make an interesting an interesting contribution to this question

We would like to thank the reviewer for the positive evaluation of our manuscript and the constructive comments and suggestions. Your feedback has been invaluable in our efforts to enhance the accessibility of our manuscript and strengthen our findings. In response to your suggestion, we reanalyzed our data using the approach proposed by Chen et al.’s (2017, NeuroImage) and applied stricter multiple comparison correction thresholds in our reporting. This reanalysis largely replicated our previous results, thereby reinforcing the robustness of our findings. We also have examined several alternative models and results supported the integration of the spatial Stroop and Simon conflicts within the cognitive space. In addition, we enriched the theoretical framework of our manuscript by connecting the cognitive space with other important theories such as the “Expected Value of Control” theory. We have incorporated your feedback, revisions and additional analyses into the manuscript. As a result, we firmly believe that these changes have significantly improved the quality of our work. We have provided detailed responses to your comments below.

1) It's not entirely clear what the current task can measure that is not known from the MSIT, such as the additive influence of conflict sources in Fu et al. (2022), Science. More could be done to distinguish the benefits of this task from MSIT.

We agree that the MSIT task incorporates Simon and Eriksen Flanker conflict tasks and can efficiently detect the additivity of conflict effects across orthogonal tasks. Like the MSIT, our task incorporates Simon with spatial Stroop conflicts and can test the same idea. For example, a previous study from our lab (Li et al., 2014) used the combined spatial Stroop-Simon condition with the arrows displayed on diagonal corners and found evidence for the additive hypothesis. However, the MSIT cannot be used to test whether/how different conflicts are parametrically represented in a low-dimensional space, a question that is important to address the debate of domain-general and domain-specific cognitive control.

To this end, our current study adopted the spatial Stroop-Simon task for the unique purpose of parametrically modulating conflict similarity. As far as we know, there is no way to define the similarity between the combined Simon_Flanker conflict condition and the Simon/Flanker conditions in the MSIT. In contrast, with the spatial Stroop-Simon paradigm, we can define the similarity with the cosine of the angle difference across the two conditions in question.

We have added the following texts in the discussion part to emphasize the 51 difference between our paradigm and other studies.

"The use of an experimental paradigm that permits parametric manipulation of conflict similarity provides a way to systematically investigate the organization of cognitive control, as well as its influence on adaptive behaviors. This approach extends traditional paradigms, such as the multi-source interference task (Fu et al., 2022), color Stroop-Simon task (Liu et al., 2010) and similar paradigms that do not afford a quantifiable metric of conflict source similarity."

References:

Li, Q., Nan, W., Wang, K., & Liu, X. (2014). Independent processing of stimulus-stimulus and stimulus-response conflicts. PloS One, 9(2), e89249.

2) The evidence from this previous work for mixtures between different conflict sources make the framing of 'infinite possible types of conflict' feel like a strawman. The authors cite classic work (e.g., Kornblum et al., 1990) that develops a typology for conflict which is far from infinite, and I think few people would argue that every possible source of difficulty will have to be learned separately. Such an issue is addressed in theories like 'Expected Value of Control', where optimization of control policies can address unique combinations of task demands.

The notion that there might be infinite conflicts arises when we consider the quantitative feature of cognitive control. If each combination of the Stroop-Simon combination is regarded as a conflict condition, there would be infinite combinations, and it is our major goal to investigate how these infinite conflict conditions are represented effectively in a space with finite dimensions. We agree that it is unnecessary to dissociate each of these conflict conditions into a unique conflict type, since they may not differ substantially. However, we argue that understanding variant conflicts within a purely categorical framework (e.g., Simon and Flanker conflict in MSIT) is insufficient, especially because it leads to dichotomic conclusions that do not capture how combinations of conflicts are organized in the brain, as our study addresses.

There could be different perspectives on how our cognitive control system flexibly encodes and resolves multiple conflicts. The cognitive space assumption we held provides a principle by which we can represent multiple conflicts in a lower dimensional space efficiently. While the “Expected Value of Control” theory addresses when and how much cognitive control to apply based on control demand, the “cognitive space” view seeks to explain how the conflict, which defines cognitive control demand, is encoded in the brain. Thus, we argue that these two lines of work are different yet complementary. The geometry of cognitive space of conflict can benefit the adjustment of cognitive control for upcoming conflicts. For example, our brain may evaluate the similarity/distance (and thus cost) between the consecutive conflict conditions, and selects the path with best cost-benefit tradeoff to switch from one state to another. This idea is conceptually similar to a recent study by Grahek et al. (2022) demonstrating that more frequently switching states were encoded as closer together than less frequently switching states in a “drift-threshold” space.

Nevertheless, Grahek et al (2022) investigated how cognitive control changes based on the expected value of control theory within the same conflict, whereas our study aims to examine organization of different conflict.

We have added the implications of cognitive space view in the discussion to indicate the potential values of our finding to understand the EVC account and the difference between the two theories.

“Previous researchers have proposed an “expected value of control (EVC)” theory, which posits that the brain can evaluate the cost and benefit associated with executing control for a demanding task, such as the conflict task, and specify the optimal control strength (Shenhav et al., 2013). For instance, Grahek et al. (2022) found that more frequently switching goals when doing a Stroop task were achieved by adjusting smaller control intensity. Our work complements the EVC theory by further investigating the neural representation of different conflict conditions and how these representations can be evaluated to facilitate conflict resolution. We found that different conflict conditions can be efficiently represented in a cognitive space encoded by the right dlPFC, and participants with stronger cognitive space representation have also adjusted their conflict control to a greater extent based on the conflict similarity (Fig 4C). The finding suggests that the cognitive space organization of conflicts guides cognitive control to adjust behavior. Previous studies have shown that participants may adopt different strategies to represent a task, with the model-based strategies benefitting goal-related behaviors more than the model-free strategies (Rmus et al., 2022). Similarly, we propose that cognitive space could serve as a mental model to assist fast learning and efficient organization of cognitive control settings. Specifically, the cognitive space representation may provide a principle for how our brain evaluates the expected cost of switching and the benefit of generalization between states and selects the path with the best cost-benefit tradeoff (Abrahamse et al., 2016; Shenhav et al., 2013). The proximity between two states in cognitive space could reflect both the expected cognitive demand required to transition and the useful mechanisms to adapt from. The closer the two conditions are in cognitive space, the lower the expected switching cost and the higher the generalizability when transitioning between them. With the organization of a cognitive space, a new conflict can be quickly assigned a location in the cognitive space, which will facilitate the development of cognitive control settings for this conflict by interpolating nearby conflicts and/or projecting the location to axes representing different cognitive control processes, thus leading to a stronger CSE when following a more similar conflict condition. On the other hand, without a cognitive space, there would be no measure of similarity between conflicts on different trials, hence limiting the ability of fast learning of cognitive control setting from similar trials.”

Reference:

Grahek, I., Leng, X., Fahey, M. P., Yee, D., & Shenhav, A. Empirical and Computational Evidence for Reconfiguration Costs During Within-Task Adjustments in Cognitive Control. CogSci.

3) Wouldn't a region that represented each conflict source separately still show the same pattern of results? The degree of Stroop vs Simon conflict is perfectly negatively correlated across conditions, so wouldn't a region that just tracks Stoop conflict show these RSA patterns? The authors show that overall congruency is not represented in DLPFC (which is surprising), but they don't break it down by whether this is due to Stroop or Simon congruency (I'm not sure their task allows for this).

To estimate the unique contributions of the spatial Stroop and Simon conflicts, we performed a model-comparison analysis. We constructed a Stroop-Only model and a Simon-Only model, with each conflict type projected onto the Stroop (vertical) axis or Simon (horizontal) axis, respectively. The similarity between any two conflict types was defined using the Jaccard similarity index (Jaccard, P., 1901), that is, their intersection divided by their union. By replacing the cognitive spacebased conflict similarity regressor with the Stroop-Only and Simon-Only regressors, we calculated their BICs. Results showed that the BIC was larger for Stroop-Only (5377122) and Simon-Only (5377096) than for the Cognitive-Space model (5377094). An additional Stroop+Simon model, including both Stroop-Only and Simon-Only regressors, also showed a poorer model fitting (BIC = 5377118) than the Cognitive-Space model. Considering that the pattern of conflict representations is more manifested when the conflict is present (i.e., on incongruent trials) than not (i.e., on congruent trials), we also conducted the model comparison using the incongruent trials only. Results showed that Stroop-Only (1344128), Simon-Only (1344120), and Stroop+Simon (1344157) models all showed higher BIC values than the CognitiveSpace model (1344104). These results indicate that the right 8C encodes an integrated cognitive space for resolving Stroop and Simon conflicts. Therefore, we believe the cognitive space has incorporated both dimensions. We added these additional analyses and results to the revised manuscript.

“To examine if the right 8C specifically encodes the cognitive space rather than the domain-general or domain-specific organizations, we tested several additional models (see Methods). Model comparison showed a lower BIC in the Cognitive-Space model (BIC = 5377094) than the Domain-General (BIC = 537127) or Domain-Specific (BIC = 537127) models. Further analysis showed the dimensionality of the representation in the right 8C was 1.19, suggesting the cognitive space was close to 1D. We also tested if the observed conflict similarity effect was driven solely by spatial Stroop or Simon conflicts, and found larger BICs for the models only including the Stroop similarity (i.e., the Stroop-Only model, BIC = 5377122) or Simon similarity (i.e., the Simon-Only model, BIC = 5377096). An additional Stroop+Simon model, including both StroopOnly and Simon-Only regressors, also showed a worse model fitting (BIC = 5377118). Moreover, we replicated the results with only incongruent trials, considering that the pattern of conflict representations is more manifested when the conflict is present (i.e., on incongruent trials) than not (i.e., on congruent trials). We found a poorer fitting in Domain-general (BIC = 1344129), Domain-Specific (BIC = 1344129), Stroop-Only (BIC = 1344128), Simon-Only (BIC = 1344120), and Stroop+Simon (BIC = 1344157) models than the Cognitive-Space model (BIC = 1344104). These results indicate that the right 8C encodes an integrated cognitive space for resolving Stroop and Simon conflicts. The more detailed model comparison results are listed in Table 2.”

We reason that we did not observe an overall congruency effect in the RSA results is because our definition of congruency here differed from traditional definitions (i.e., contrast between incongruent and congruent conditions). In the congruency regressor of our RSA model, we defined representational similarity as 1 if calculated between two incongruent, or two congruent trials, and 0 if between incongruent and congruent trials. Thus, our definition of the congruency regressor reflects whether multivariate patterns differ between incongruent and congruent trials, rather than whether activity strengths differ. Indeed, we did observe the latter form of congruency effects, with stronger univariate activities in pre-SMA for incongruent versus congruent conditions. We have added this in the Note S6 (“The multivariate representations of conflict type and orientation are different from the congruency effect”):

“Neither did we observe a multivariate congruency effect (i.e., the pattern difference between incongruent and congruent conditions compared to that within each condition) in the right 8C or any other regions. Note the definition of congruency here differed from traditional definitions (i.e., contrast between activity strength of incongruent and congruent conditions), with which we found stronger univariate activities in pre-SMA for incongruent versus congruent conditions.”

We could not determine whether the null effect of the congruency regressor was due to Stroop or Simon congruency alone, because congruency levels of the two types always covary. On all trials of the compound conditions (Conf 2-4), whenever the Stroop dimension was incongruent, the Simon dimension was also incongruent, and vice versa for the congruent condition. Thus, the contribution of spatial Stroop or Simon alone to the congruency effect could not be tested using compound conditions. Although we have pure spatial Stroop or Simon conditions, within-Stroop and withinSimon trial pairs constituted only 8% of cells in the representational similarity matrix. This was insufficient to determine whether the null congruency effect was due to solely Stroop or Simon.

Overall, with the added analysis we found that the data in the right 8C area supports conflict representations that are organized based on both Simon and spatial Stroop conflict. Although the current experimental design does not allow us to identify whether the null effect of the congruency regressor was driven by either conflict or both, we clarified that the congruency regressor did not test the 205 conventional congruency effect and the null finding does not contradict previous 206 research.

Reference:

Jaccard, P. (1901). Étude comparative de la distribution florale dans une portion des Alpes et des Jura. Bull Soc Vaudoise Sci Nat(37), 547-579.

4) The authors use a novel form of RSA that concatenates patterns across conditions, runs and subjects into a giant RSA matrix, which is then used for linear mixed effects analysis. This appears to be necessary because conflict type and visual orientation are perfectly confounded within the subject (although, if I understand, the conflict type x congruence interaction wouldn't have the same concern about visual confounds, which shouldn't depend on congruence). This is an interesting approach but should be better justified, preferably with simulations validating the sensitivity and specificity of this method and comparing it to more standard methods.

The confound exists for both the conflict type and the conflict type × congruence interaction in our design, since both incongruent and congruent conditions include stimuli from the full orientation space. For example, for the spatial Stroop type, the congruent condition could be either an up arrow at the top or a down arrow at the bottom. Similarly, the incongruent condition could be either an up arrow at the bottom or a down arrow at the top. Therefore, both the congruent and incongruent conditions are perfectly confounded with the orientation.

We reanalyzed the data using the well-documented approach by Chen et al. (2017, Neuroimage), as suggested by the reviewer. The new analysis replicated our previously reported results (Fig. 4-5, S4-S7). As Chen et al (2017) has provided abundant simulations to validate this approach, we did not run any further simulations.

5) A chief concern is that the same pattern contributes to many entries in the DV, which has been addressed in previous work using row-wise and column-wise random effects (Chen et al., 2017, Neuroimage). It would also be informative to know whether the results hold up to removing within-run similarity, which can bias similarity measures (Walther et al., 2016, Neuroimage).

Thank you for the comment. In our revised manuscript, we followed your suggestion and adopted the approach proposed by Chen et al. (2017). Specifically, we included both the upper and lower triangle of the representational similarity matrix (excluding the diagonal). Moreover, we also removed all the within-subject similarity (thus also excluding the within-run similarity as suggested by Walther et al. (2016)) to minimize the bias of the potentially strong within-subject similarity. In addition, we added both the row-wise and column-wise random effects to capture the dependence of cells within each column and each row, respectively (Chen et al., 2017).

Results from this approach largely replicated our previous results. The right 8C again showed significant conflict similarity representation, with greater representational strength in incongruent than congruent condition, and positively correlated to behavioral performance. The orientation effect was also identified in the visual (e.g., right V1) and oculomotor (e.g., left FEF) regions.

We have revised the methodology and the results in the revised manuscript:

"Representational similarity analysis (RSA).

For each cortical region, we calculated the Pearson’s correlations between fMRI activity patterns for each run and each subject, yielding a 1400 (20 conditions × 2 runs × 35 participants) × 1400 RSM. The correlations were calculated in a cross297 voxel manner using the fMRI activation maps obtained from GLM3 described in the previous section. We excluded within-subject cells from the RSM (thus also excluding the within-run similarity as suggested by Walther et al., (2016)), and the remaining cells were converted into a vector, which was then z-transformed and submitted to a linear mixed effect model as the dependent variable. The linear mixed effect model also included regressors of conflict similarity and orientation similarity. Importantly, conflict similarity was based on how Simon and spatial Stroop conflict are combined and hence was calculated by first rotating all subject’s stimulus location to the top right and bottom-left quadrants, whereas orientation was calculated using original stimulus locations. As a result, the regressors representing conflict similarity and orientation similarity were de-correlated. Similarity between two conditions was measured as the cosine value of the angular difference. Other regressors included a target similarity regressor (i.e., whether the arrow directions were identical), a response similarity regressor (i.e., whether the correct responses were identical); a spatial Stroop distractor regressor (i.e., vertical distance between two stimulus locations); a Simon distractor regressor (i.e., horizontal distance between two stimulus locations). Additionally, we also included a regressor denoting the similarity of Group (i.e., whether two conditions are within the same subject group, according to the stimulus-response mapping). We also added two regressors including ROI316 mean fMRI activations for each condition of the pair to remove the possible uni-voxel influence on the RSM. A last term was the intercept. To control the artefact due to dependence of the correlation pairs sharing the same subject, we included crossed random effects (i.e., row-wise and column-wise random effects) for the intercept, conflict similarity, orientation and the group factors (G. Chen et al., 2017)."

Reference:

Walther, A., Nili, H., Ejaz, N., Alink, A., Kriegeskorte, N., & Diedrichsen, J. (2016). Reliability of dissimilarity measures for multi-voxel pattern analysis. Neuroimage, 137, 188-200. doi:10.1016/j.neuroimage.2015.12.012

6) Another concern is the extent to which across-subject similarity will only capture consistent patterns across people, making this analysis very similar to a traditional univariate analysis (and unlike the traditional use of RSA to capture subject-specific patterns).

With proper normalization, we assume voxels across different subjects should show some consistent localizations, although individual differences can be high. J. Chen et al. (2017) has demonstrated that consistent multi-voxel activation patterns exist across individuals. Previous studies have also successfully applied cross-subject RSA (see review by Freund et al, 2021) and cross-subject decoding approaches (e.g., Jiang et al., 2016; Tusche et al., 2016), so we believe cross-subject RSA should be feasible to capture distributed activation patterns shared at the group level. We added this argument in the revised manuscript:

"Previous studies (e.g., J. Chen et al., 2017) have demonstrated that consistent multivoxel activation patterns exist across individuals, and successful applications of cross-subject RSA (see review by Freund, Etzel, et al., 2021) and cross-subject decoding approaches (Jiang et al., 2016; Tusche et al., 2016) have also been reported."

In the revised manuscript, we also tested whether the representation in right 8C held for within-subject data. We reasoned that the conflict similarity effects identified by cross-subject RSA should be replicable in within-subject data, although the latter is not able to dissociate the conflict similarity effect from the orientation effect. We performed similar RSA for within-subject RSMs, excluding the within-run cells. We replaced the perfectly confounded factors of conflict similarity and orientation with a common factor called similarity_orientation. Other confounding factor pairs were addressed similarly. Results showed a significant effect of similarity_orientation, t(13993) = 3.270, p = .0005, 1-tailed. Given the specific representation of conflict similarity identified by the cross-subject RSA, we believe that the within-subject data of right 8C probably showed similar conflict similarity modulation effects as the cross-subject data, although future research that orthogonalizes conflict type and orientation is needed to fully answer this question. We added this result in the revised section Note S7.

"Note S7. The cross-subject RSA captures similar effects with the within-subject RSA Considering the variability in voxel-level functional localizations among individuals, one may question whether the cross-subject RSA results were biased by the consistent multi-voxel patterns across subjects, distinct from the more commonly utilized withinsubject RSA. We reasoned that the cross-subject RSA should have captured similar effects as the within-subject RSA if we observe the conflict similarity effect in right 8C with the latter analysis. Therefore, we tested whether the representation in right 8C held for within-subject data. Specifically, we performed similar RSA for withinsubject RSMs, excluding the within-run cells. We replaced the perfectly confounded factors of conflict similarity and orientation with a common factor called similarity_orientation. Other confounding factor pairs (i.e., target versus response, and Stroop distractor versus Simon distractor) were addressed similarly. Results showed a significant effect of similarity_orientation, t(13993) = 3.270, p = .0005, 1tailed. Given the specific representation of conflict similarity identified by the crosssubject RSA, the within-subject data of right 8C may show similar conflict similarity modulation effects as the cross-subject data. Further research is needed to fully dissociate the representation of conflict and the representation of visual features such as orientation."

Reference:

Chen, J., Leong, Y. C., Honey, C. J., Yong, C. H., Norman, K. A., & Hasson, U. (2017). Shared memories reveal shared structure in neural activity across individuals. Nature Neuroscience, 20(1), 115-125.

Freund, M. C., Etzel, J. A., & Braver, T. S. (2021). Neural Coding of Cognitive Control: The Representational Similarity Analysis Approach. Trends in Cognitive Sciences, 25(7), 622-638.

Jiang, J., Summerfield, C., & Egner, T. (2016). Visual Prediction Error Spreads Across Object Features in Human Visual Cortex. J Neurosci, 36(50), 12746-12763.

Tusche, A., Bockler, A., Kanske, P., Trautwein, F. M., & Singer, T. (2016). Decoding the Charitable Brain: Empathy, Perspective Taking, and Attention Shifts Differentially Predict Altruistic Giving. Journal of Neuroscience, 36(17), 4719-4732.

7) Finally, the authors should confirm all their results are robust to less liberal methods of multiplicity correction. For univariate analysis, they should report the effects from the standard p < .001 cluster forming threshold for univariate analysis (or TFCE). For multivariate analyses, FDR can be quite liberal. The authors should consider whether their mixed-effects analyses allow for group-level randomization, and consider (relatively powerful) Max-Stat randomization tests (Nichols & Holmes, 2002, Hum Brain Mapp).

In our revised manuscript, we have corrected the univariate results using the probabilistic TFCE (pTFCE) approach by Spisak et al. (2019). This approach estimates the conditional probability of cluster extent based on Bayes’ rule. Specifically, we applied pTFCE on our univariate results (i.e., the z-maps of our contrasts). This returned enhanced Z-score maps, which were then thresholded based on simulated cluster size thresholds using 3dClustSim. A cluster-forming threshold of p < .001 was employed. Results showed only the pre-SMA was activated in the incongruent > congruent contrast, and right IPS and right dmPFC were activated in the linear Simon modulation effect. Further tests also showed these regions were not correlated with the behavioral performance, uncorrected ps >.28. These results largely replicated our previous results. We have revised the method and results accordingly.

Methods:

"Results were corrected with the probabilistic threshold-free cluster enhancement(pTFCE) and then thresholded by 3dClustSim function in AFNI (Cox & Hyde, 1997) with voxel-wise p < .001 and cluster-wize p < .05, both 1-tailed."

Results:

"In the fMRI analysis, we first replicated the classic congruency effect by searching for brain regions showing higher univariate activation in incongruent than congruent conditions (GLM1, see Methods). Consistent with the literature (Botvinick et al., 2004; Fu et al., 2022), this effect was observed in the pre-supplementary motor area (preSMA) (Fig. 3, Table S1). We then tested the encoding of conflict type as a cognitive space by identifying brain regions with activation levels parametrically covarying with the coordinates (i.e., axial angle relative to the horizontal axis) in the hypothesized cognitive space. As shown in Fig. 1B, change in the angle corresponds to change in spatial Stroop and Simon conflicts in opposite directions. Accordingly, we found the right inferior parietal sulcus (IPS) and the right dorsomedial prefrontal cortex (dmPFC) displayed positive correlation between fMRI activation and the Simon conflict (Fig. 3, Fig. S3, Table S1)."

We appreciate the reviewer’s suggestion to apply the Max-Stat randomization tests (Nichols & Holmes, 2002) for the multivariate analyses. However, the representational similarity matrix was too large (1400×1400) to be tested with a balanced randomization approach (i.e., the Max-Stat), due to (1) running even 1000 times for all ROIs cost very long time; (2) the distribution generated from normal times of randomization (e.g., 5000 iterations) would probably be unbalanced, since the full range of possible samples that could be generated by a complete randomization is not adequately represented. Instead, we adopted a very strict Bonferroni correction p < 0.0001/360 when reporting the regression results from RSA. Notebally, Chen et al (2017) has shown that their approach could control the FDR at an acceptable level.

Reference:

Spisák, T., Spisák, Z., Zunhammer, M., Bingel, U., Smith, S., Nichols, T., & Kincses,T. (2019). Probabilistic TFCE: A generalized combination of cluster size and voxel intensity to increase statistical power. NeuroImage, 185, 12-26.

Chen, G., Taylor, P. A., Shin, Y.-W., Reynolds, R. C., & Cox, R. W. J. N. (2017). Untangling the relatedness among correlations, Part II: Inter-subject correlation group analysis through linear mixed-effects modeling. 147, 825-840.

Minor concerns:

8) I appreciate the authors wanting to present the conditions in a theory-agnostic way, but the framing of 5 conflict types was confusing. I think framing the conditions as a mixture of 2 conflict types (Stroop and Simon) makes more sense, especially given the previous work on MSIT.

We have renamed the Type1-5 as spatial Stroop, StHSmL, StMSmM, StLSmH, and Simon conditions, respectively. H, L, and M indicate high, low andmedium similarity with the corresponding conflict, respectively. This is alsoconsistent with the naming of our previous work (Yang et al., 2021).

Reference:

Yang, G., Xu, H., Li, Z., Nan, W., Wu, H., Li, Q., & Liu, X. (2021). The congruency sequence effect is modulated by the similarity of conflicts. Journal of Experimental Psychology: Learning, Memory, and Cognition, 47(10), 1705-1719.

9) It would be helpful to have more scaffolding for the key conflict & orientation analyses. A schematic in the main text that outlines these contrasts would be very helpful (e.g. similar to S4).

We have inserted Figure 7 in the revised manuscript. In this figure, we plotted the schematic of the difference between the conflict similarity 467 and orientation regressors according to their cross-group representational similarity 468 matrices.

10) Figure 4D could be clearer, both in labeling and figure caption. 'Modeled similarity' could be relabelled to something more informative, like 'conflict type (or mixture) similarity'. Alternatively, it would be helpful to show a summary RDM for region r-8C. For example, breaking it down by just conflict type and congruence.

We have relabeled the x-axis to “Conflict type similarity” and y-axis to “Neural similarity” for Figure 4D in the revised manuscript.

We have also added a summary RSM figure in Fig. S5 to show the different similarity patterns between incongruent and congruent conditions.

11) It may be helpful to connect your work to how people have discussed multiple forms of conflict monitoring and control with respect to target and distractor features e.g., Lindsay & Jacoby, 1994, JEP:HPP; Mante, Sussillo et al., 2013, Nature; Soutschek et al., 2015, JoCN; Jackson et al., 2021, Comm Bio; Ritz & Shenhav, 2022, bioRxiv

We have added an analysis to examine how cognitive control modulates target and distractor representation. To this end, we selected the left V4, a visual region showing joint representation of target, Stroop distractor and Simon distractor, as the region of interest. We tested whether these representation strengths differed between incongruent and congruent conditions, finding the representation of target was stronger and representations of both distractors were weaker in the incongruent condition. This suggests that cognitive control modulates the stimuli in both directions. We added the results in Note S10 and Fig. S8, and also added discussion of it in “Methodological implications”.

“Note S10. Cognitive control enhances target representation and suppresses distractor representation Using the separability of confounding factors afforded by the cross-subject RSA, we examined how representations of targets and distractors are modulated by cognitive control. The key assumption is that exerting cognitive control may enhance target representation and suppress distractor representation. We hypothesized that stimuli are represented in visual areas, so we chose a visual ROI from the main RSA results showing joint representation of target, spatial Stroop distractor and Simon distractor (p < .005, 1-tail, uncorrected). Only the left V4 met this criterion. We then tested representations with models similar to the main text for incongruent only trials, congruent only trials, and the incongruent – congruent contrast. The contrast model additionally used interaction between the congruency and target, Stroop distractor and Simon distractor terms. Results showed that in the incongruent condition, when we employ more cognitive control, the target representation was enhanced (t(237990) = 2.59, p = .029, Bonferroni corrected) and both spatial Stroop (t(237990) = –4.18, p < .001, Bonferroni corrected) and Simon (t(237990) = –3.14, p = .005, Bonferroni corrected) distractor representations were suppressed (Fig. S8). These are consistent with the idea that the top-down control modulates the stimuli in both directions (Polk et al., 2008; Ritz & Shenhav, 2022).”

Discussion:

“Moreover, the cross-subject RSA provides high sensitivity to the variables of interest and the ability to separate confounding factors. For instance, in addition to dissociating conflict type from orientation, we dissociated target from response, and spatial Stroop distractor from Simon distractor. We further showed cognitive control can both enhance the target representation and suppress the distractor representation (Note S10, Fig. S8), which is in line with previous studies (Polk et al., 2008; Ritz & Shenhav, 2022)."

12) For future work, I would recommend placing stimuli along the whole circumference, to orthogonalize Stroop and Simon conflict within-subject.

We thank the reviewer for this highly helpful suggestion. Expanding the 547 conflict conditions to a full conflict space and replicating our current results could 548 provide stronger evidence for the cognitive space view.

In the revised manuscript, we added this as a possible future design:

“A possible improvement to our current design would be to include left, right, up, and down arrows presented in a grid formation across four spatially separate quadrants, with each arrow mapped to its own response button. However, one potential confounding factor would be that these conditions have different levels of difficulty (i.e., different magnitude of conflict), which may affect the CSE results and their representational similarity."

Reviewer #2:

Summary, general appraisal

This study examines the construct of "cognitive spaces" as they relate to neural coding schemes present in response conflict tasks. The authors utilize a novel paradigm, in which subjects must map the direction of a vertically oriented arrow to either a left or right response. Different types of conflict (spatial Stroop, Simon) are parametrically manipulated by varying the spatial location of the arrow (a taskirrelevant feature). The vertical eccentricity of the arrow either agrees or conflicts with the arrow's direction (spatial Stroop), while the horizontal eccentricity of the arrow agrees or conflicts with the side of the response (Simon). A neural coding model is postulated in which the stimuli are embedded in a cognitive space, organized by distances that depend only on the similarity of congruency types (i.e., where conditions with similar relative proportions of spatial-Stroop versus Simon congruency are represented with similar activity patterns). The authors conduct a behavioral and fMRI study to provide evidence for such a representational coding scheme. The behavioral findings replicate the authors' prior work in demonstrating that conflict-related cognitive control adjustments (the congruency sequence effect) shows strong modulation as a function of the similarity between conflict types. With the fMRI neural activity data, the authors report univariate analyses that identified activation in left prefrontal and dorsomedial frontal cortex modulated by the amount of Stroop or Simon conflict present, and multivariate representational similarity analyses (RSA) that identified right lateral prefrontal activity encoding conflict similarity and correlated with the behavioral effects of conflict similarity.

This study tackles an important question regarding how distinct types of conflict, which have been previously shown to elicit independent forms of cognitive control adjustments, might be encoded in the brain within a computationally efficient representational format. The ideas postulated by the authors are interesting ones and the utilized methods are rigorous.

We would like to express our sincere appreciation for the reviewer’s positive evaluation of our manuscript and the constructive comments and suggestions. Through careful consideration of your feedback, we have endeavored to make our manuscript more accessible to readers and further strengthened our findings. In response to your suggestion, we reanalyzed our data with the approach proposed by Chen et al.’s (2017, NeuroImage). This reanalysis largely replicated our previous results, reinforcing the validity of our findings. Additionally, we conducted tests with several alternative models and found that the cognitive space hypothesis best aligns with our observed data. We have incorporated these revisions and additional analyses into the manuscript based on your valuable feedback. As a result, we believe that these changes and additional analyses have significantly enhanced the quality of our manuscript. We have provided detailed responses to your comments below.

However, the study has critical limitations that are due to a lack of clarity regarding theoretical hypotheses, serious confounds in the experimental design, and a highly non-standard (and problematic) approach to RSA. Without addressing these issues it is hard to evaluate the contribution of the authors findings to the computational cognitive neuroscience literature.

1) The primary theoretical question and its implications are unclear. The paper would greatly benefit from more clearly specifying potential alternative hypotheses and discussing their implications. Consider, for example, the case of parallel conflict monitors. Say that these conflict monitors are separately tuned for Stroop and Simon conflict, and are located within adjacent patches of cortex that are both contained within a single cortical parcel (e.g., as defined by the Glasser atlas used by the authors for analyses). If RSA was conducted on the responses of such a parcel to this task, it seems highly likely that an activation similarity matrix would be observed that is quite similar (if not identical) to the hypothesized one displayed in Figure 1. Yet it would seem like the authors are arguing that the "cognitive space" representation is qualitatively and conceptually distinct from the "parallel monitor" coding scheme. Thus, it seems that the task and analytic approach is not sufficient to disambiguate these different types of coding schemes or neural architectures.

The authors also discuss a fully domain-general conflict monitor, in which different forms of conflict are encoded within a single dimension. Yet this alternative hypothesis is also not explicitly tested nor discussed in detail. It seems that the experiment was designed to orthogonalize the "domain-general" model from the "cognitive space" model, by attempting to keep the overall conflict uniform across the different stimuli (i.e., in the design, the level of Stroop congruency parametrically trades off with the level of Simon congruency). But in the behavioral results (Fig. S1), the interference effects were found to peak when both Stroop and Simon congruency are present (i.e., Conf 3 and 4), suggesting that the "domain-general" model may not be orthogonal to the "cognitive space" model. One of the key advantages of RSA is that it provides the ability to explicitly formulate, test and compare different coding models to determine which best accounts for the pattern of data. Thus, it would seem critical for the authors to set up the design and analyses so that an explicit model comparison analysis could be conducted, contrasting the domain-general, domain-specific, and cognitive space accounts.

We appreciate the reviewer pointing out the need to formally test alternative models. In the revised manuscript, we have added and compared a few alternative models, finding the Cognitive-Space model (the one with graded conflict similarity levels as we reported) provided the best fit to our data. Specifically, we tested the following five models against the Cognitive-Space model:

(1) Domain-General model. This model treats each conflict type as equivalent, so each two conflict types only differ in the magnitude of their conflict. Therefore, we defined the domain-general matrix as the difference in their effects indexed by the group-averaged RT in Experiment 2. Then the z-scored model vector was sign-flipped to reflect similarity instead of distance. This model showed non-significant conflict type effects (t(951989) = 0.92, p = .179) and poorer fit (BIC = 5377126) than the Cognitive-Space model (BIC = 5377094).

(2) Domain-Specific model. This model treats each conflict type differently, so we used a diagonal matrix, with within-conflict type similarities being 1 and all crossconflict type similarities being 0. This model also showed non-significant effects (t(951989) = 0.84, p = .201) and poorer fit (BIC = 5377127) than the Cognitive-Space model.

(3) Stroop-Only model. This model assumes that the right 8C only encodes the spatial Stroop conflict. We projected each conflict type to the Stroop (vertical) axis and calculated the similarity between any two conflict types as the Jaccard similarity index (Jaccard, 1901), that is, their intersection divided by their union. This model also showed non-significant effects (t(951989) = 0.20, p = .423) and poorer fit (BIC = 5377122) than the Cognitive-Space model.

(4) Simon-Only model. This model assumes that the right 8C only encodes the Simon conflict. We projected each conflict type to the Simon (horizontal) axis and calculated the similarity like the Stroop-Only model. This model showed significant effects (t(951989) = 4.19, p < .001) but still quantitatively poorer fit (BIC = 5377096) than the Cognitive-Space model.

(5) Stroop+Simon model. This model assumes the spatial Stroop and Simon conflicts are parallelly encoded in the brain, similar to the "parallel monitor" hypothesis suggested by the reviewer. It includes both Stroop-Only and Simon-Only regressors. This model showed nonsignificant effect for the Stroop regressor (t(951988) = 0.06, p = .478) and significant effect for the Simon regressor (t(951988) = 3.30, p < .001), but poorer fit (BIC = 5377118) than the Cognitive-Space model.

“Moreover, we replicated these results with only incongruent trials (i.e., when conflict is present), considering that the pattern of conflict representations is more manifested when the conflict is present (i.e., on incongruent trials) than not (i.e., on congruent trials). We found a poorer fitting in Domain-general (BIC = 1344129), Domain-Specific (BIC = 1344129), Stroop-Only (BIC = 1344128), Simon-Only (BIC = 1344120), and Stroop+Simon (BIC = 1344157) models than the Cognitive-Space model (BIC = 1344104).”

In summary, these results indicate that the right 8C encodes an integrated cognitive space for resolving Stroop and Simon conflicts. We added the above results to the revised manuscript.

The above analysis approach was added to the method “Model comparison and representational dimensionality”, and the results were added to the “Multivariate patterns of the right dlPFC encodes the conflict similarity” in the revised manuscript.

Methods:

“Model comparison and representational dimensionality To estimate if the right 8C specifically encodes the cognitive space, rather than the domain-general or domain-specific structures, we conducted two more RSAs. We replaced the cognitive space-based conflict similarity matrix in the RSA we reported above (hereafter referred to as the Cognitive-Space model) with one of the alternative model matrices, with all other regressors equal. The domain-general model treats each conflict type as equivalent, so each two conflict types only differ in the magnitude of their conflict. Therefore, we defined the domain-general matrix as the difference in their congruency effects indexed by the group-averaged RT in Experiment 2. Then the zscored model vector was sign-flipped to reflect similarity instead of distance. The domain-specific model treats each conflict type differently, so we used a diagonal matrix, with within-conflict type similarities being 1 and all cross-conflict type similarities being 0.

Moreover, to examine if the cognitive space is driven solely by the Stroop or Simon conflicts, we tested a spatial Stroop-Only (hereafter referred to as “Stroop-Only”) and a Simon-Only model, with each conflict type projected onto the spatial Stroop (vertical) axis or Simon (horizontal) axis, respectively. The similarity between any two conflict types was defined using the Jaccard similarity index (Jaccard, 1901), that is, their intersection divided by their union. We also included a model assuming the Stroop and Simon dimensions are independently represented in the brain, adding up the StroopOnly and Simon-Only regressors (hereafter referred to as the Stroop+Simon model). We conducted similar RSAs as reported above, replacing the original conflict similarity regressor with the Strrop-Only, Simon-Only, or both regressors (for the Stroop+Simon model), and then calculated their Bayesian information criterions (BICs).”

Results:

“To examine if the right 8C specifically encodes the cognitive space rather than the domain-general or domain-specific organizations, we tested several additional models (see Methods). Model comparison showed a lower BIC in the Cognitive-Space model (BIC = 5377094) than the Domain-General (BIC = 537127) or Domain-Specific (BIC = 537127) models. Further analysis showed the dimensionality of the representation in the right 8C was 1.19, suggesting the cognitive space was close to 1D. We also tested if the observed conflict similarity effect was driven solely by spatial Stroop or Simon conflicts, and found larger BICs for the models only including the Stroop similarity (i.e., the Stroop-Only model, BIC = 5377122) or Simon similarity (i.e., the Simon-Only model, BIC = 5377096). An additional Stroop+Simon model, including both StroopOnly and Simon-Only regressors, also showed a worse model fitting (BIC = 5377118). Moreover, we replicated the results with only incongruent trials, considering that the pattern of conflict representations is more manifested when the conflict is present (i.e., on incongruent trials) than not (i.e., on congruent trials). We found a poorer fitting in Domain-general (BIC = 1344129), Domain-Specific (BIC = 1344129), Stroop-Only (BIC = 1344128), Simon-Only (BIC = 1344120), and Stroop+Simon (BIC = 1344157) models than the Cognitive-Space model (BIC = 1344104). These results indicate that the right 8C encodes an integrated cognitive space for resolving Stroop and Simon conflicts. The more detailed model comparison results are listed in Table 2.”

Reference:

Jaccard, P. (1901). Étude comparative de la distribution florale dans une portion des Alpes et des Jura. Bull Soc Vaudoise Sci Nat(37), 547-579.

2a) Relatedly, the reasoning for the use of the term "cognitive space" is unclear. The mere presence of graded coding for two types of conflict seems to be a low bar for referring to neural activity patterns as encoding a "cognitive space". It is discussed that cognitive spaces/maps allow for flexibility through inference and generalization. But no links were made between these cognitive abilities and the observed representational structure.

In the revised manuscript, we have clarified that we tested a specific prediction of the cognitive space hypothesis: the geometry of the cognitive space predicts that more similar conflict types will have more similar neural representations,leading to the CSE and RSA patterns tested in this study. These results add to the literature by providing empirical evidence on how different conflict types are encoded in the brain. We agree that this study is not a comprehensive test of the cognitive space hypothesis. Thus, in the revised manuscript we explicitly clarified that this study is a test of the geometry of the cognitive space hypothesis.

Critically, the cognitive space view holds that the representations of different abstract information are organized continuously and the representational geometry in the cognitive space are determined by the similarity among the represented information (Bellmund et al., 2018).

"The present study aimed to test the geometry of cognitive space in conflict representation. Specifically, we hypothesize that different types of conflict are represented as points in a cognitive space. Importantly, the distance between the points, which reflects the geometry of the cognitive space, scales with the difference in the sources of the conflicts being represented by the points."

We have also discussed the limitation of the results and stressed the need for more research to fully test the cognitive space hypothesis.

“Additionally, our study is not a comprehensive test of the cognitive space hypothesis but aimed primarily to provide original evidence for the geometry of cognitive space in representing conflict information in cognitive control. Future research should examine other aspects of the cognitive space such as its dimensionality, its applicability to other conflict tasks such as Eriksen Flanker task, and its relevance to other cognitive abilities, such as cognitive flexibility and learning.

2b) Additionally, no explicit tests of generality (e.g., via cross-condition generalization) were provided.

To examine the generality of cognitive space across conditions, we conducted a leave-one-out prediction analysis. We used the behavioral data from Experiment 1 for this test, due to its larger amount of data than Experiment 2. Specifically, we removed data from one of the five similarity levels (as illustrated by the θs in Fig. 1C) and used the remaining data to perform the same mixed-effect model as reported in the main text (i.e., the two-stage analysis). This yielded one pair of beta coefficients including the similarity regressor and the intercept for each subject, with which we predicted the CSE for the removed similarity level for each subject. We repeated this process for each similarity level once. The predicted results were highly correlated with the original data, with r = .87 for the RT and r = .84 for the ER, ps < .001. We have added this analysis and result to the “Conflict type 706 similarity modulated behavioral congruency sequence effect (CSE)” section.

“Moreover, to test the continuity and generalizability of the similarity modulation, we conducted a leave-one-out prediction analysis. Specifically, we removed data from one of the five similarity levels (as illustrated by the θs in Fig. 1C) and used the remaining data to perform the same mixed-effect model (i.e., the two-stage analysis). This yielded one pair of beta coefficients including the similarity regressor and the intercept for each subject, with which we predicted the CSE for the removed similarity level for each subject. We repeated this process for each similarity level once. The predicted results were highly correlated with the original data, with r = .87 for the RT and r = .84 for the ER, ps < .001."

2c) Finally, although the design elicits strong CSE effects, it seems somewhat awkward to consider CSE behavioral patterns as a reflection of the kind of abilities supported by a cognitive map (if this is indeed the implication that was intended). In fact, CSE effects are well-modeled by simpler "model-free" associative learning processes, that do not require elaborate representations of abstract structures.

We argue the conflict similarity modulation of CSEs we observed cannot be explained by the “model-free” stimulus-driven associative learning process. This mainly refers to the feature integration account proposed by Hommel et al. (2004), which explains poorer performance in CI and IC trials (compared with CC and II trials) with the partial repetition cost caused by the breaking of stimulus-response binding. Although we cannot remove its influence on the within-type trials (similarity level 5, θ = 0), it should not affect the cross-type trials (similarity level 1-4, θ = 90°, 67.5°, 45° and 22.5°, respectively), because the CC, CI, IC, II trials had equal probabilities of partially repeated and fully switched trials (see the Author response image 1 for an example of trials across Conf 1 and Conf 3 conditions). Thus, feature integration cannot explain the gradual CSE decrease from similarity level 1 to 4, which sufficiently reproduce the full effect, as suggested by the leave-one-out prediction analysis mentioned above. We thus conclude that the similarity modulation of CSE cannot be explained by the stimulus-driven associative learning.

Author response image 1.

Notably, however, our findings are aligned with an associative learning account of cognitive control (Abrahamse et al., 2016), which extends association learning from stimulus/response level to cognitive control. In other words, abstract cognitive control state can be learned and generalized like other sensorimotor features. This view explicitly proposes that “transfer occurs to the extent that two tasks overlap”, a hypothesis directly supported by our CSE results (see also Yang et al., 2021). Extending this, our fMRI results provide the neural basis of how cognitive control can generalize through a representation of cognitive space. The cognitive space view complements associative learning account by providing a fundamental principle for the learning and generalization of control states. Given the widespread application of CSE as indicator of cognitive control generalization (Braem et al., 2014), we believe that it can be recognized as a kind of ability supported by the cognitive space. This was further supported by the brain-behavioral correlation: stronger encoding of cognitive space was associated with greater bias of trial-wise behavioral adjustment by the consecutive conflict similarity.

We have incorporated these ideas into the discussion:

“Similarly, we propose that cognitive space could serve as a mental model to assist fast learning and efficient organization of cognitive control settings. Specifically, the cognitive space representation may provide a principle for how our brain evaluates the expected cost of switching and the benefit of generalization between states and selects the path with the best cost-benefit tradeoff (Abrahamse et al., 2016; Shenhav et al., 2013). The proximity between two states in cognitive space could reflect both the expected cognitive demand required to transition and the useful mechanisms to adapt from. The closer the two conditions are in cognitive space, the lower the expected switching cost and the higher the generalizability when transitioning between them. With the organization of a cognitive space, a new conflict can be quickly assigned a location in the cognitive space, which will facilitate the development of cognitive control settings for this conflict by interpolating nearby conflicts and/or projecting the location to axes representing different cognitive control processes, thus leading to a stronger CSE when following a more similar conflict condition.”

References:

Hommel, B., Proctor, R. W., & Vu, K. P. (2004). A feature-integration account of sequential effects in the Simon task. Psychological Research, 68(1), 1-17. Abrahamse, E., Braem, S., Notebaert, W., & Verguts, T. (2016). Grounding cognitive control in associative learning. Psychological Bulletin, 142(7), 693-728.

Yang, G., Xu, H., Li, Z., Nan, W., Wu, H., Li, Q., & Liu, X. (2021). The congruency sequence effect is modulated by the similarity of conflicts. Journal of 770 Experimental Psychology: Learning, Memory, and Cognition, 47(10), 1705-1719.

Braem, S., Abrahamse, E. L., Duthoo, W., & Notebaert, W. (2014). What determines the specificity of conflict adaptation? A review, critical analysis, and proposed synthesis. Frontiers in Psychology, 5, 1134.

3) More generally, it seems problematic that Stroop and Simon conflict in the paradigm parametrically trade-off against each other. A more powerful design would have de-confounded Stroop and Simon conflict so that each could be separately estimation via (potentially orthogonal) conflict axes. Additionally, incorporating more varied stimulus sets, locations, or responses might have enabled various tests of generality, as implied by a cognitive space account.

We thank the reviewer for these valuable suggestions. We argue that the current design is adequate to test the prediction that more similar conflict types have more similar neural representations. That said, we agree that further examination using more powerful experimental designs are needed to fully test the cognitive space account of cognitive control. We also agree that employing more varied stimulus sets,locations and responses would further extend our findings. We have included this as a future research direction in the revised manuscript.

We have revised our discussion about the limitation as:

“A few limitations of this study need to be noted. To parametrically manipulate the conflict similarity levels, we adopted the spatial Stroop-Simon paradigm that enables parametrical combinations of spatial Stroop and Simon conflicts. However, since this paradigm is a two-alternative forced choice design, the behavioral CSE is not a pure measure of adjusted control but could be partly confounded by bottom-up factors such as feature integration (Hommel et al., 2004). Future studies may replicate our findings with a multiple-choice design (including more varied stimulus sets, locations and responses) with confound-free trial sequences (Braem et al., 2019). Another limitation is that in our design, the spatial Stroop and Simon effects are highly anticorrelated. This constraint may make the five conflict types represented in a unidimensional space (e.g., a circle) embedded in a 2D space. Future studies may test the 2D cognitive space with fully independent conditions. A possible improvement to our current design would be to include left, right, up, and down arrows presented in a grid formation across four spatially separate quadrants, with each arrow mapped to its own response button. However, one potential confounding factor would be that these conditions have different levels of difficulty (i.e., different magnitude of conflict), which may affect the CSE results and their representational similarity.”

4) Serious confounds in the design render the results difficult to interpret. As much prior neuroimaging and behavioral work has established, "conflict" per se is perniciously correlated with many conceptually different variables. Consequently, it is very difficult to distinguish these confounding variables within aggregate measures of neural activity like fMRI. For example, conflict is confounded with increased time-on-task with longer RT, as well as conflict-driven increases in coding of other task variables (e.g., task-set related coding; e.g., Ebitz et al. 2020 bioRxiv). Even when using much higher resolution invasive measures than fMRI (i.e., eCoG), researchers have rightly been wary of making strong conclusions about explicit encoding of conflict (Tang et al, 2019; eLife). As such, the researchers would do well to be quite cautious and conservative in their analytic approach and interpretation of results.

We acknowledge the findings showing that encoding of conflicts may not be easily detected in the brain. However, recent studies have shown that the representational similarity analysis can effectively detect representations of conflict tasks (e.g., the color Stroop) using factorial designs (Freund et al., 2021a; 2021b).

In our analysis, we are aware of the potential impact of time-on-task (e.g., RT) on univariate activation levels and subsequent RSA patterns. To address this issue, we added univariate fMRI activation levels as nuisance regressors to the RSA. To de confound conflict from other factors such as orientation of stimuli related to the center of the screen, we also applied the cross-subject RSA approach. Furthermore, we were cautious about determining regions that encoded conflict control. We set three strict criteria: (1) Regions must show a conflict similarity modulation effect; (2) regions must show higher representational strength in the incongruent condition compared with the congruent condition; and (3) regions must correlate with behavioral performance. With these criteria, we believe that the results we reported are already conservative. We would be happy to implement any additional criteria the reviewer recommends.

Reference:

Freund, M. C., Etzel, J. A., & Braver, T. S. (2021a). Neural Coding of Cognitive Control: The Representational Similarity Analysis Approach. Trends in Cognitive Sciences, 25(7), 622-638.

Freund, M. C., Bugg, J. M., & Braver, T. S. (2021b). A Representational Similarity 823 Analysis of Cognitive Control during Color-Word Stroop. Journal of 824 Neuroscience, 41(35), 7388-7402.

5) This issue is most critical in the interpretation of the fMRI results as reflecting encoding of conflict types. A key limitation of the design, that is acknowledged by the authors is that conflict is fully confounded within-subject by spatial orientation. Indeed, the limited set of stimulus-response mappings also cast doubt on the underlying factors that give rise to the CSE modulations observed by the authors in their behavioral results. The CSE modulations are so strong - going from a complete absence of current x previous trial-type interaction in the cos(90) case all the way to a complete elimination of any current trial conflict when the prior trial was incongruent in the cos(0) case - that they cause suspicion that they are actually driven by conflict-related control adjustments rather than sequential dependencies in the stimulus-response mappings that can be associatively learned.

Unlike the fMRI data, we cannot tease apart the effects of conflict similarity and orientation in a similar manner as the cross-subject RSA for behavioral CSEs. However, we have a few reasons that the orientation and other bottom-up factors should not be the factors driving the similarity modulation effect.

First, we did not find any correlation between the regions showing orientation effects and behavioral CSEs. This suggests that orientation does not directly contribute to the CSE modulation.

Second, if the CSE modulation is purely driven by the association learning of the stimulus-response mapping, we should observe a stronger modulation effect after more extensive training. However, our results do not support this prediction. Using data from Experiment 1, we found that the modulation effect remained constant across the three sessions (see Note S3).

“Note S3. Modulation of conflict similarity on behavioral CSEs does not change across time We tested if the conflict similarity modulation on the CSE is susceptible to training. We collected the data of Experiment 1 across three sessions, thus it is possible to examine if the conflict similarity modulation effect changes across time. To this end, we added conflict similarity, session and their interaction into a mixed-effect linear model, in which the session was set as a categorical variable. With a post-hoc analysis of variance (ANOVA), we calculated the statistical significance of the interaction term. This approach was applied to both the RT and ER. Results showed no interaction effect in either RT, F(2,1479) = 1.025, p = .359, or ER, F(2,1479) = 0.789, p = .455. This result suggests that the modulation effect does not change across time. “

Third, the observed similarity modulation on the CSE, particularly for similarity levels 1-4, should not be attributed to the stimulus-response associations, such as feature integration, as have been addressed in response to comment 2.c.

Finally, other bottom-up factors, such as the spatial location proximity did not drive the CSE modulation results, which we have addressed in the original manuscript in Note S2.

"Note S2. Modulation of conflict similarity on behavioral CSEs cannot be explained by the physical proximity

In our design, the conflict similarity might be confounded by the physical proximity between stimulus (i.e., the arrow) of two consecutive trials. That is, when arrows of the two trials appear at the same quadrant, a higher conflict similarity also indicates a higher physical proximity (Fig. 1A). Although the opposite is true if arrows of the two trials appear at different quadrants, it is possible the behavioral effects can be biased by the within quadrant trials. To examine if the physical distance has confounded the conflict similarity modulation effect, we conducted an additional analysis.

We defined the physical angular difference across two trials as the difference of their polar angles relative to the origin. Therefore, the physical angular difference could vary from 0 to 180°. For each CSE conditions (i.e., CC, CI, IC and II), we grouped the trials based on their physical angular distances, and then averaged trials with the same previous by current conflict type transition but different orders (e.g., StHSmL−StLSmH and StLSmH−StHSmL) within each subject. The data were submitted to a mixed-effect model with the conflict similarity, physical proximity (i.e., the opposite of the physical angular difference) as fixed-effect predictors, and subject and CSE condition as random effects. Results showed significant conflict similarity modulation effects in both Experiment 1 (RT: β = 0.09 ± 0.01, t(7812) = 13.74, p < .001, ηp2 = .025; 875 ER: β = 0.09 ± 0.01, t(7812) = 7.66, p < .001, ηp2 = .018) and Experiment 2 (RT: β = 876 0.21 ± 0.02, t(3956) = 9.88, p < .001, ηp2 = .043; ER: β = 0.20 ± 0.03, t(4201) = 6.11, 877 p < .001, ηp2 = .038). Thus, the observed modulation of conflict similarity on behavioral 878 CSEs cannot be explained by physical proximity."

6) To their credit, the authors recognize this confound, and attempt to address it analytically through the use of a between-subject RSA approach. Yet the solution is itself problematic, because it doesn't actually deconfound conflict from orientation. In particular, the RSA model assumes that whatever components of neural activity encode orientation produce this encoding within the same voxellevel patterns of activity in each subject. If they are not (which is of course likely), then orthogonalization of these variables will be incomplete. Similar issues underlie the interpretation target/response and distractor coding. Given these issues, perhaps zooming out to a larger spatial scale for the between-subject RSA might be warranted. Perhaps whole-brain at the voxel level with a high degree of smoothing, or even whole-brain at the parcel level (averaging per parcel). For this purpose, Schaefer atlas parcels might be more useful than Glasser, as they more strongly reflect functional divisions (e.g., motor strip is split into mouth/hand divisions; visual cortex is split into central/peripheral visual field divisions). Similarly, given the lateralization of stimuli, if a within-parcel RSA is going to be used, it seems quite sensible to pool voxels across hemispheres (so effectively using 180 parcels instead of 360).

Doing RSA at the whole-brain level is an interesting idea. However, it does not allow the identification of specific brain regions representing the cognitive space. Additionally, increasing the spatial scale would include more voxels that are not involved in representing the information of interest and may increase the noise level of data. Given these concerns, we did not conduct the whole-brain level RSA.

We agree that smoothing data can decrease cross-subject variance in voxel distribution and may increase the signal-noise ratio. We reanalyzed the results for the right 8C region using RSA on smoothed beta maps (6-mm FWHM Gaussian kernel). This yielded a significant conflict similarity effect, t(951989) = 5.55, p < .0001, replicating the results on unsmoothed data (t(951989) = 5.60, p < .0001). Therefore, we retained the results from unsmoothed data in the main text, and added the results based on smoothed data to the supplementary material (Note S9).

“Note S9. The cross-subject pattern similarity is robust against individual differences Due to individual differences, the multivoxel patterns extracted from the same brain mask may not reflect exactly the same brain region for each subject. To reduce the influence of individual difference, we conducted the same cross-subject RSA using data smoothed with a 6-mm FWHM Gaussian kernel. Results showed a significant conflict similarity effect, t(951989) = 5.55, p < .0001, replicating the results on unsmoothed data (t(951989) = 5.60, p < .0001). “

We also used the bilateral 8C area as a single mask and conducted the same RSA. We found a significant conflict type similarity effect, t(951989) = 4.36, p < .0001. However, the left 8C alone showed no such representation, t(951989) = 0.38, p = .351, consistent with the right lateralized representation of cognitive space we reported in Note S8. Therefore, we used ROIs from each hemisphere separately.

“Note S8. The lateralization of conflict type representation

We observed the right 8C but not the left 8C represented the conflict type similarity. A further test is to show if there is a lateralization. We tested several regions of the left dlPFC, including the i6-8, 8Av, 8C, p9-46v, 46, 9-46d, a9-46v (Freund, Bugg, et al., 2021). We found that none of these regions show the representation of conflict type, all uncorrected ps > .35. These results indicate that the conflict type is specifically represented in the right dlPFC. “

We have also discussed the lateralization in the manuscript:

“In addition, we found no such representation in the left dlPFC (Note S8), indicating a possible lateralization. Previous studies showed that the left dlPFC was related to the expectancy-related attentional set up-regulation, while the right dlPFC was related to the online adjustment of control (Friehs et al., 2020; Vanderhasselt et al., 2009), which is consistent with our findings. Moreover, the right PFC also represents a composition of single rules (Reverberi et al., 2012), which may explain how the spatial Stroop and Simon types can be jointly encoded in a single space.”

7) The strength of the results is difficult to interpret due to the non-standard analysis method. The use of a mixed-level modeling approach to summarize the empirical similarity matrix is an interesting idea, but nevertheless is highly non-standard within RSA neuroimaging methods. More importantly, the way in which it was implemented makes it potentially vulnerable to a high degree of inaccuracy or bias. In this case, this bias is likely to be overly optimistic (high false positive rate). No numerical or formal defense was provided for this mixed-level model approach. As a result, the use of this method seems quite problematic, as it renders the strength of the observed results difficult to interpret. Instead, the authors are encouraged using a previously published method of conducting inference with between-subject RSA, such as the bootstrapping methods illustrated in Kragel et al. (2018; Nat Neurosci), or in potentially adopting one of the Chen et al. methods mentioned above, that have been extensively explored in terms of statistical properties.

No numerical or formal defense was provided for this mixed-level model approach. As a result, the use of this method seems quite problematic, as it renders the strength of the observed results difficult to interpret. Instead, the authors are encouraged using a previously published method of conducting inference with between-subject RSA, such as the bootstrapping methods illustrated in Kragel et al. (2018; Nat Neurosci), or in potentially adopting one of the Chen et al. methods mentioned above, that have been extensively explored in terms of statistical properties.

In our revised manuscript, we have adopted the approach proposed by Chen et al. (2017). Specifically, we included both the upper and lower triangle of the representational similarity matrix (excluding the diagonal). Moreover, we also removed all the within-subject similarity (thus also excluding the within-run similarity) to minimize the bias of the potentially strong within-subject similarity (note we also analyzed the within-subject data and found significant effects for the similarity modulation, though this effect cannot be attributed to the conflict similarity or orientation alone. We added this part in Note S7, see below). In addition, we added both the row-wise and column-wise random effects to capture the dependence of cells within each column/row (Chen et al., 2017). We have revised the method part as:

“We excluded within-subject cells from the RSM (thus also excluding the withinrun similarity as suggested by Walther et al., (2016)), and the remaining cells were converted into a vector, which was then z-transformed and submitted to a linear mixed effect model as the dependent variable. The linear mixed effect model also included regressors of conflict similarity and orientation similarity. Importantly, conflict similarity was based on how Simon and spatial Stroop conflicts are combined and hence was calculated by first rotating all subject’s stimulus location to the topright and bottom-left quadrants, whereas orientation was calculated using original stimulus locations. As a result, the regressors representing conflict similarity and orientation similarity were de-correlated. Similarity between two conditions was measured as the cosine value of the angular difference. Other regressors included a target similarity regressor (i.e., whether the arrow directions were identical), a response similarity regressor (i.e., whether the correct responses were identical); a spatial Stroop distractor regressor (i.e., vertical distance between two stimulus locations); a Simon distractor regressor (i.e., horizontal distance between two stimulus locations). Additionally, we also included a regressor denoting the similarity of Group (i.e., whether two conditions are within the same subject group, according to the stimulus-response mapping). We also added two regressors including ROImean fMRI activations for each condition of the pair to remove the possible uni-voxel influence on the RSM. A last term was the intercept. To control the artefact due to dependence of the correlation pairs sharing the same subject, we included crossed random effects (i.e., row-wise and column-wise random effects) for the intercept, conflict similarity, orientation and the group factors (G. Chen et al., 2017).”

Results from this approach highly replicated our original results. Specifically, we found the right 8C again showed a strong conflict similarity effect, a higher representational strength in the incongruent condition compared to the congruent condition, and a significant correlation with the behavioral CSE. The orientation effect was also identified in the visual (e.g., right V1) and oculomotor (e.g., left FEF) regions.

We revised the results accordingly:

For the conflict type effect:

“The first criterion revealed several cortical regions encoding the conflict similarity, including the Brodmann 8C area (a subregion of dlPFC(Glasser et al., 2016)) and a47r in the right hemisphere, and the superior frontal language (SFL) area, 6r, 7Am, 24dd, and ventromedial visual area 1 (VMV1) areas in the left hemisphere (Bonferroni corrected ps < 0.0001, one-tailed, Fig. 4A). We next tested whether these regions were related to cognitive control by comparing the strength of conflict similarity effect between incongruent and congruent conditions (criterion 2). Results revealed that the left SFL, left VMV1, and right 8C met this criterion, Bonferroni corrected ps < .05, one-tailed, suggesting that the representation of conflict type was strengthened when conflict was present (e.g., Fig. 4D). The intersubject brain-behavioral correlation analysis (criterion 3) showed that the strength of conflict similarity effect on RSM scaled with the modulation of conflict similarity on the CSE (slope in Fig. S2C) in right 8C (r = .52, Bonferroni corrected p = .002, onetailed, Fig. 4C, Table 1) but not in the left SFL and VMV1 (all Bonferroni corrected ps > .05, one-tailed). “

For the orientation effect:

“We observed increasing fMRI representational similarity between trials with more similar orientations of stimulus location in the occipital cortex, such as right V1, right V2, right V4, and right lateral occipital 2 (LO2) areas (Bonferroni corrected ps < 0.0001). We also found the same effect in the oculomotor related region, i.e., the left 997 frontal eye field (FEF), and other regions including the right 5m, left 31pv and right parietal area F (PF) (Fig. 5A). Then we tested if any of these brain regions were related to the conflict representation by comparing their encoding strength between incongruent and congruent conditions. Results showed that the right V1, right V2, left FEF, and right PF encoded stronger orientation effect in the incongruent than the congruent condition, Bonferroni corrected ps < .05, one-tailed (Table1, Fig. 5B). We then tested if any of these regions was related to the behavioral performance, and results showed that none of them positively correlated with the behavioral conflict similarity modulation effect, all uncorrected ps > .45, one-tailed. Thus all regions are consistent with the criterion 3.”

“Note S7. The cross-subject RSA captures similar effects with the within-subject RSA Considering the variability in voxel-level functional localizations among individuals, one may question whether the cross-subject RSA results were biased by the consistent multi-voxel patterns across subjects, distinct from the more commonly utilized withinsubject RSA. We reasoned that the cross-subject RSA should have captured similar effects as the within-subject RSA if we observe the conflict similarity effect in right 8C with the latter analysis. Therefore, we tested whether the representation in right 8C held for within-subject data. Specifically, we performed similar RSA for withinsubject RSMs, excluding the within-run cells. We replaced the perfectly confounded factors of conflict similarity and orientation with a common factor called similarity_orientation. Other confounding factor pairs (i.e., target versus response, and Stroop distractor versus Simon distractor) were addressed similarly. Results showed a significant effect of similarity_orientation, t(13993) = 3.270, p = .0005, 1tailed. Given the specific representation of conflict similarity identified by the crosssubject RSA, the within-subject data of right 8C may show similar conflict similarity modulation effects as the cross-subject data. Further research is needed to fully dissociate the representation of conflict and the representation of visual features such as orientation.”

8) Another potential source of bias is in treating the subject-level random effect coefficients (as predicted by the mixed-level model) as independent samples from a random variable (in the t-tests). The more standard method for inference would be to use test statistics derived from the mixed-model fixed effects, as those have degrees of freedom calculations that are calibrated based on statistical theory.

In our revised manuscript, we reported the statistical p values calculated from the mixed-effect models. Note that because we used the Chen et al. (2017) method, which includes data from the symmetric matrix, we corrected the degrees of freedom and estimated the true p values based on the t statistics of model results. For the I versus C comparison results, we calculated the p values by combining I and C RSMs into a larger model and then adding the condition type, as well as the interaction between the regressors of interest (conflict similarity and orientation) and the condition type. We made the statistical inference based on the interaction effect.

We have revised the corresponding methods as:

“The statistical significance of these beta estimates was based on the outputs of the mixed-effect model estimated with the “fitlme” function in Matlab 2022a. Since symmetric cells from the RSM matrix were included in the mixed-effect model, we adjusted the t and p values with the true degree of freedom, which is half of the cells included minus the number of fixed regressors. Multiple comparison correction was applied with the Bonferroni approach across all cortical regions at the p < 0.0001 level. To test if the representation strengths are different between congruent and incongruent conditions, we also conducted the RSA using only congruent (RDM_C) and incongruent (RDM_I) trials separately. The contrast analysis was achieved by an additional model with both RDM_C and RDM_I included, adding the congruency and the interaction between conflict type (and orientation) and congruency as both fixed and random factors. The difference between incongruent and congruent representations was indicated by a significant interaction effect.”

Reviewer #3:

Yang and colleagues investigated whether information on two task-irrelevant features that induce response conflict is represented in a common cognitive space. To test this, the authors used a task that combines the spatial Stroop conflict and the Simon effect. This task reliably produces a beautiful graded congruency sequence effect (CSE), where the cost of congruency is reduced after incongruent trials. The authors measured fMRI to identify brain regions that represent the graded similarity of conflict types, the congruency of responses, and the visual features that induce conflicts.

Using several theory-driven exclusion criteria, the authors identified the right dlPFC (right 8C), which shows 1) stronger encoding of graded similarity of conflicts in incongruent trials and 2) a positive correlation between the strength of conflict similarity type and the CSE on behavior. The dlPFC has been shown to be important for cognitive control tasks. As the dlPFC did not show a univariate parametric modulation based on the higher or lower component of one type of conflict (e.g., having more spatial Stroop conflict or less Simon conflict), it implies that dissimilarity of conflicts is represented by a linear increase or decrease of neural responses. Therefore, the similarity of conflict is represented in multivariate neural responses that combine two sources of conflict.

The strength of the current approach lies in the clear effect of parametric modulation of conflict similarity across different conflict types. The authors employed a clever cross-subject RSA that counterbalanced and isolated the targeted effect of conflict similarity, decorrelating orientation similarity of stimulus positions that would otherwise be correlated with conflict similarity. A pattern of neural response seems to exist that maps different types of conflict, where each type is defined by the parametric gradation of the yoked spatial Stroop conflict and the Simon conflict on a similarity scale. The similarity of patterns increases in incongruent trials and is correlated with CSE modulation of behavior.

We would like to thank the reviewer for the positive evaluation of our manuscript and for providing constructive comments. By addressing these comments, we believe that we have made our manuscript more accessible for the readers while also strengthening our findings. In particular, we have tested a few alternative models and confirmed that the cognitive space hypothesis best fits the data. We have also demonstrated the geometric properties of the cognitive space by examining the continuity and dimensionality of the space, further supporting our main arguments. We have incorporated revisions and additional analyses to the manuscript based on your feedback. Overall, we believe that these changes and additional analyses have significantly improved the manuscript. Please find our detailed responses below.

However, several potential caveats need to be considered.

1) One caveat to consider is that the main claim of recruitment of an organized "cognitive space" for conflict representation is solely supported by the exclusion criteria mentioned earlier. To further support the involvement of organized space in conflict representation, other pieces of evidence need to be considered. One approach could be to test the accuracy of out-of-sample predictions to examine the continuity of the space, as commonly done in studies on representational spaces of sensory information. Another possible approach could involve rigorously testing the geometric properties of space, rather than fitting RSM to all conflict types. For instance, in Fig 6, both the organized and domain-specific cognitive maps would similarly represent the similarity of conflict types expressed in Fig1c (as evident from the preserved order of conflict types). The RSM suggests a low-dimensional embedding of conflict similarity, but the underlying dimension remains unclear.

Following the reviewer’s first suggestion, we conducted a leave-one-out prediction approach to examine the continuity of the cognitive space. We used the behavioral data from Experiment 1 for this test, due to its larger amount of data than Experiment 2. Specifically, we removed data from one of the five similarity levels (as illustrated by the θs in Fig. 1C) and used the remaining data to perform the same mixed-effect model as reported in the main text (i.e., the two-stage analysis). This yielded one pair of beta coefficients including the similarity regressor and the intercept for each subject, with which we predicted the CSE for the removed similarity level at subject level. We repeated this process for each similarity level once. The predicted results were highly correlated with the original data, with r = .87 for the RT and r = .84 for the ER, ps < .001. We have added this analysis and result to the “Conflict type similarity modulated behavioral congruency sequence effect (CSE)” 1079 section:

“Moreover, to test the continuity and generalizability of the similarity modulation, we conducted a leave-one-out prediction analysis. We used the behavioral data from Experiment 1 for this test, due to its larger amount of data than Experiment 2. Specifically, we removed data from one of the five similarity levels (as illustrated by the θs in Fig. 1C) and used the remaining data to perform the same mixed-effect model (i.e., the two-stage analysis). This yielded one pair of beta coefficients including the similarity regressor and the intercept for each subject, with which we predicted the CSE for the removed similarity level for each subject. We repeated this process for each similarity level once. The predicted results were highly correlated with the original data, with r = .87 for the RT and r = .84 for the ER, ps < .001.”

To estimate if the domain-specific model could explain the results we observed in right 8C, we conducted a model-comparison analysis. The domain-specific model treats each conflict type differently, so we used a diagonal matrix, with within-conflict type similarities being 1 and all cross-conflict type similarities being 0. This model showed non-significant effects (t(951989) = 0.84, p = .201) and poorer fit (BIC = 5377127) than the cognitive space model (t(951989) = 5.60, p = 1.1×10−8, BIC = 5377094). We also compared other alternative models and found the cognitive space model best fitted the data. We have included these results in the revised manuscript:

“To examine if the right 8C specifically encodes the cognitive space rather than the domain-general or domain-specific organizations, we tested several additional models (see Methods). Model comparison showed a lower BIC in the Cognitive-Space model (BIC = 5377094) than the Domain-General (BIC = 537127) or Domain-Specific (BIC = 537127) models. Further analysis showed the dimensionality of the representation in the right 8C was 1.19, suggesting the cognitive space was close to 1D. We also tested if the observed conflict similarity effect was driven solely by spatial Stroop or Simon conflicts, and found larger BICs for the models only including the Stroop similarity (i.e., the Stroop-Only model, BIC = 5377122) or Simon similarity (i.e., the Simon-Only model, BIC = 5377096). An additional Stroop+Simon model, including both StroopOnly and Simon-Only regressors, also showed a worse model fitting (BIC = 5377118). Moreover, we replicated the results with only incongruent trials, considering that the pattern of conflict representations is more manifested when the conflict is present (i.e., on incongruent trials) than not (i.e., on congruent trials). We found a poorer fitting in Domain-general (BIC = 1344129), Domain-Specific (BIC = 1344129), Stroop-Only (BIC = 1344128), Simon-Only (BIC = 1344120), and Stroop+Simon (BIC = 1344157) models than the Cognitive-Space model (BIC = 1344104). These results indicate that the right 8C encodes an integrated cognitive space for resolving Stroop and Simon conflicts. The more detailed model comparison results are listed in Table 2.”

We also estimated the dimensionality of the right 8C with the averaged RSM and found the dimensionality of the cognitive space was ~ 1.19, very close to a 1D space. This result is consistent with our experimental design, as the only manipulated variable is the angular distance between conflict types. We have added these results and the methods to the revised manuscript.

Results:

“Further analysis showed the dimensionality of the representation in the right 8C was 1.19, suggesting the cognitive space was close to 1D.”

Methods:

“To better capture the dimensionality of the representational space, we estimated its dimensionality using the participation ratio (Ito & Murray, 2023). Since we excluded the within-subject cells from the whole RSM, the whole RSM is an incomplete matrix and could not be used. To resolve this issue, we averaged the cells corresponding to each pair of conflict types to obtain an averaged 5×5 RSM matrix, similar to the matrix shown in Fig. 1C. We then estimated the participation ratio using the formula:

where λi is the eigenvalue of the RSM and m is the number of eigenvalues.

2) Another important factor to consider is how learning within the confined task space, which always negatively correlates the two types of conflicts within each subject, may have influenced the current results. Is statistical dependence of conflict information necessary to use the organized cognitive space to represent conflicts from multiple sources? Answering this question would require a paradigm that can adjust multiple sources of conflicts parametrically and independently. Investigating such dependencies is crucial in order to better understand the adaptive utility of the observed cognitive space of conflict similarity.

As the central goal of our design was to test the geometry of neural representations of conflict, we manipulated the conflict similarity. The anticorrelated Simon and spatial Stroop conflict aimed to make the overall magnitude of conflict similar among different conflict types. We agree that with the current design the likely cognitive space is not a full 2D space with Simon and spatial Stroop being two dimensions. Instead, the likely cognitive space is a subspace (e.g., a circle) embedded in the 2D space, due to the constraint of anticorrelated Simon and spatial Stroop conflict across conflict types. Nevertheless, the subspace can also be used to test the geometry that similar conflict types share similar neural representations.

To test the full 2D cognitive space, a possible revision of our current design is to have multiple hybrid conditions (like Type 2-4) that cover the whole space. For instance, imagine arrow locations in the first quadrant space. We could have a 3×3 design with 9 conflict conditions, where their horizontal/vertical coordinates could be one of the combinations of 0, 0.5 and 1. This way, the spatial Stroop and Simon conditions would be independent of each other. Notably, however, one potential confounding factor would be that these conditions have different levels of difficulty (i.e., different magnitude of conflict), which may affect the CSE results and their representational similarity.<br /> We have added the above limitations and future designs to the revised 1156 manuscript.

“Another limitation is that in our design, the spatial Stroop and Simon effects are highly anticorrelated. This constraint may make the five conflict types represented in a unidimensional space (e.g., a circle) embedded in a 2D space. Future studies may test the 2D cognitive space with fully independent conditions. A possible improvement to our current design would be to include left, right, up, and down arrows presented in a grid formation across four spatially separate quadrants, with each arrow mapped to its own response button. However, one potential confounding factor would be that these conditions have different levels of difficulty (i.e., different magnitude of conflict), which may affect the CSE results and their representational similarity.”

Major comments:

3) The RSM result (and the absence of univariate effect) seem to be a good first step to claim the use of cognitive space of conflict. Yet, the presence of an organized (unidimensional; Fig. 6) and continuous cognitive space should be further tested and backed up.

We thank the reviewer for recognizing the methods and results of our current work. Indeed, the utilization of a parametric design and RSA to examine organization of neural representations is a widely embraced methodology in the field of cognitive neuroscience (e.g., Freund et al., 2021; Ritz et al., 2022). Our current study aimed primarily to provide original evidence for whether similar conflicts are represented similarly in the brain, which reflects the geometry of conflict representations (i.e., the structure of differences between conflict representations). We have used multiple criteria to back up the findings by showing the representation is sensitive to the presence of conflict and has behavioral relevance.

We agree that the cognitive space account of cognitive control requires further validation. Therefore, in the revised manuscript, we have added several additional tests to strengthen the evidence supporting the organized cognitive space representation. Firstly, we tested five alternative models (Domain-General, Domain Specific, Stroop-Only, Simon-Only and Stroop+Simon models), and found that the Cognitive-Space model best fitted our data. Secondly, we explicitly calculated the dimensionality of the representation and observed a low dimensionality (1.19D). We have added these results to the “Multivariate patterns of the right dlPFC encodes the conflict similarity” section in the revised manuscript (see also the response to Comment 1).

Furthermore, we utilized data from Experiment 1 to demonstrate the continuity of the cognitive space by showing its ability to predict out-of-sample data. We have included this result to the “Conflict type similarity modulated behavioral congruency sequence effect (CSE)” section in the revised manuscript:

“Moreover, to test the continuity and generalizability of the similarity modulation, we conducted a leave-one-out prediction analysis. We used the behavioral data from Experiment 1 for this test, due to its larger amount of data than Experiment 2. Specifically, we removed data from one of the five similarity levels (as illustrated by the θs in Fig. 1C) and used the remaining data to perform the same mixed-effect model (i.e., the two-stage analysis). This yielded one pair of beta coefficients including the similarity regressor and the intercept for each subject, with which we predicted the CSE for the removed similarity level for each subject. We repeated this process for each similarity level once. The predicted results were highly correlated with the original data, with r = .87 for the RT and r = .84 for the ER, ps < .001.”

References:

Freund, M. C., Bugg, J. M., & Braver, T. S. (2021). A Representational Similarity Analysis of Cognitive Control during Color-Word Stroop. Journal of Neuroscience, 41(35), 7388-7402.

Ritz, H., & Shenhav, A. (2022). Humans reconfigure target and distractor processing to address distinct task demands. bioRxiv. doi:10.1101/2021.09.08.459546

4) Is the conflict similarity effect not driven by either coding of the weak to strong gradient of the spatial Stroop conflict or the Simon conflict? For example, would simply identifying brain regions that selectively tuned to the Simon conflict continuously enough to create a graded similarity in Fig. C.

We recognize that our current design and analyzing approach cannot fully exclude the possibility that the current results are driven solely by either Stroop or Simon conflicts, since their gradients are correlated to the conflict similarity gradient we defined. To estimate their unique contributions, we performed a model-comparison analysis. We constructed a Stroop-Only model and a Simon-Only model, with each conflict type projected onto the Stroop (vertical) axis or Simon (horizontal) axis, respectively. The similarity between any two conflict types was defined using the Jaccard similarity index (Jaccard, P., 1901), that is, their intersection divided by their union. By replacing the cognitive space-based conflict similarity regressor with the Stroop-Only and Simon-Only regressors, we calculated their BICs. Results showed that the BIC was larger for Stroop-Only (5377122) and Simon-Only (5377096) than for the cognitive space model (5377094). An additional Stroop+Simon model, including both Stroop-Only and Simon-Only regressors, also 1220 showed a poorer model fitting (BIC = 5377118) than the cognitive space model.

Moreover, we replicated the results with only incongruent trials. We found a poorer fitting in Stroop-Only (BIC = 1344128), Simon-Only (BIC = 1344120), and Stroop+Simon (BIC = 1344157) models than the Cognitive-Space model (BIC = 1344104). These results indicate that the right 8C encodes an integrated cognitive space for resolving Stroop and Simon conflicts. Therefore, we believe the cognitive space has incorporated both dimensions. We added these additional analyses and results to the revised manuscript (see also the response to the above Comment 1).

5) Is encoding of conflict similarity in the unidimensional organized space driven by specific requirements of the task or is this a general control strategy? Specifically, is the recruitment of organized space something specific to the task that people are trained to work with stimuli that negatively correlate the spatial Stroop conflict and the Simon conflict?

We argue that this encoding is a general control strategy. In our task design, we asked the participants to respond to the target arrow and ignore the location that appeared randomly for them. So, they were not trained to deal with the stimuli in any certain way. We also found the conflict similarity modulation on CSE did not change with more training (We added this result in Note S3), indicating that the cognitive space did not depend on strategies that could be learned through training.

“Note S3. Modulation of conflict similarity on behavioral CSEs does not change across time We tested if the conflict similarity modulation on the CSE is susceptible to training. We collected the data of Experiment 1 across three sessions, thus it is possible to examine if the conflict similarity modulation effect changes across time. To this end, we added conflict similarity, session and their interaction into a mixed-effect linear model, in which the session was set as a categorical variable. With a post-hoc analysis of variance (ANOVA), we calculated the statistical significance of the interaction term.

This approach was applied to both the RT and ER. Results showed no interaction effect in either RT, F(2,1479) = 1.025, p = .359, or ER, F(2,1479) = 0.789, p = .455. This result suggests that the modulation effect does not change across time."

Instead, the cognitive space should be determined by the intrinsic similarity structure of the task design. A previous study (Freitas et al., 2015) has found that the CSE across different versions of spatial Stroop and flanker tasks was stronger than that across either of the two conflicts and Simon. In their designs, the stimulus similarity was controlled at the same level, so the difference in CSE was only attributable to the similar dimensional overlap between Stroop and flanker tasks, in contrast to the Simon task. Furthermore, recent studies showed that the cognitive space generally exists to represent structured latent states (e.g., Vaidya et al., 2022), mental strategy cost (Grahek et al., 2022), and social hierarchies (Park et al., 2020). Therefore, we argue that cognitive space is likely a universal strategy that can be applied to different scenarios.

We added this argument in the discussion:

“Although the spatial orientation information in our design could be helpful to the construction of cognitive space, the cognitive space itself was independent of the stimulus-level representation of the task. We found the conflict similarity modulation on CSE did not change with more training (see Note S3), indicating that the cognitive space did not depend on strategies that could be learned through training. Instead, the cognitive space should be determined by the intrinsic similarity structure of the task design. For example, a previous study (Freitas et al, 2015) has found that the CSE across different versions of spatial Stroop and flanker tasks was stronger than that across either of the two conflicts and Simon. In their designs, the stimulus similarity was controlled at the same level, so the difference in CSE was only attributable to the similar dimensional overlap between Stroop and flanker tasks, in contrast to the Simon task. Furthermore, recent studies showed that the cognitive space generally exists to represent structured latent states (e.g., Vaidya et al., 2022), mental strategy cost (Grahek et al., 2022), and social hierarchies (Park et al., 2020). Therefore, cognitive space is likely a universal strategy that can be applied to different scenarios."

Reference:

Freitas, A. L., & Clark, S. L. (2015). Generality and specificity in cognitive control: conflict adaptation within and across selective-attention tasks but not across selective-attention and Simon tasks. Psychological Research, 79(1), 143-162.

Vaidya, A. R., Jones, H. M., Castillo, J., & Badre, D. (2021). Neural representation of 1280 abstract task structure during generalization. Elife, 10, 1-26.

Grahek, I., Leng, X., Fahey, M. P., Yee, D., & Shenhav, A. Empirical and 1282 Computational Evidence for Reconfiguration Costs During Within-Task 1283 Adjustments in Cognitive Control. CogSci.

Park, S. A., Miller, D. S., Nili, H., Ranganath, C., & Boorman, E. D. (2020). Map 1285 Making: Constructing, Combining, and Inferring on Abstract Cognitive Maps. 1286 Neuron, 107(6), 1226-1238 e1228. doi:10.1016/j.neuron.2020.06.030

6) The observed pattern seems to suggest that there is conflict similarity space that is defined by the combination of the conflict similarity (i.e., the strength of conflicts) and the sources of conflict (i.e., the Simon vs the spatial Stroop). What are the rational reasons to separate conflicts of different sources (beyond detecting incongruence)? And how are they used for better conflict resolutions?

The necessity of separating conflicts of different sources lies in that the spatial Stroop and the Simon effects are resolved with different mechanisms. The behavioral congruency effects of a combined conflict from two different sources were shown to be the summation of the two conflict sources (Liu et al., 2010), suggesting that the conflicts are resolved independently. Moreover, previous studies have shown that different sources of conflict are resolved with different brain regions (Egner, 2008; Li et al., 2017), and at different processing stages (Wang et al., 2013). Therefore, when multiple sources of conflict occur simultaneously or sequentially, it should be more efficient to resolve the conflict by identifying the sources.

We have added this argument to the revised manuscript:

“The rationale behind defining conflict similarity based on combinations of different conflict sources, such as spatial-Stroop and Simon, stems from the evidence that these sources undergo independent processing (Egner, 2008; Li et al., 2014; Liu et al., 2010; Wang et al., 2014). Identifying these distinct sources is critical in efficiently resolving potentially infinite conflicts."

Reference:

Egner, T. (2008). Multiple conflict-driven control mechanisms in the human brain. Trends in Cognitive Sciences, 12(10), 374-380.

Li, Q., Yang, G., Li, Z., Qi, Y., Cole, M. W., & Liu, X. (2017). Conflict detection and 1307 resolution rely on a combination of common and distinct cognitive control networks. Neuroscience and Biobehavioral Reviews, 83, 123-131.

Wang, K., Li, Q., Zheng, Y., Wang, H., & Liu, X. (2014). Temporal and spectral 1310 profiles of stimulus-stimulus and stimulus-response conflict processing. NeuroImage, 89, 280-288.

Liu, X., Park, Y., Gu, X., & Fan, J. (2010). Dimensional overlap accounts for independence and integration of stimulus-response compatibility effects. Attention, Perception, & Psychophysics, 72(6), 1710-1720.

7) The congruency effect is larger in conflict type 2, 3, 4 consistently compared to conflict 1 and 5. Are these expected under the hypothesis of unified cognitive space of conflict similarity? Is the pattern of similarity modeled in RSA?

Yes, this is expected. The spatial Stroop and Simon effects have been shown to be additive and independent (Li et al., 2014). Therefore, the congruency effects of conflict type 2, 3 and 4 would be the weighted sum of the spatial Stroop and Simon effects. The weights can be defined by the sine and cosine of the polar angle.

For instance, in Type 2, wy = sin(67.5°) and wx = cos(67.5°). The sum of the two 1321 weight values (i.e., 1.31) is larger than 1, leading to a larger congruency effect than 1322 the pure spatial Stroop (Conf 1) and Simon (Conf 5) conditions.

Note that this hypothesis underlies the Stroop+Simon model, which assumes the Stroop and Simon dimensions are independently represented in the brain and drive the behavior in an additive fashion. Moreover, the observed difference of behavioral congruency effects may have reflected the variance in the Domain-General model, which treats all conflict types as equivalent, with the only difference between each two conflict types in the magnitude of their conflict. Therefore, we did not model the behavioral congruency effects as a covariance regressor in the major RSA. Instead, we conducted a model comparison analysis by comparing these models and the Cognitive-Space model. Results showed worse model fitting of both the Domain-general and Stroop+Simon models. Specially, the regressor of congruency effect difference in the Domain-General model was not significant (p = .575), which also suggests that the higher congruency effect in conflict type 2, 3 and 4 should not influence the Cognitive-Space model results. We have added these methods and results to the revised manuscript (see also our response to Comment 1):

Methods:

“Model comparison and representational dimensionality

To estimate if the right 8C specifically encodes the cognitive space, rather than the domain-general or domain-specific structures, we conducted two more RSAs. We replaced the cognitive space-based conflict similarity matrix in the RSA we reported above (hereafter referred to as the Cognitive-Space model) with one of the alternative model matrices, with all other regressors equal. The domain-general model treats each conflict type as equivalent, so each two conflict types only differ in the magnitude of their conflict. Therefore, we defined the domain-general matrix as the difference in their congruency effects indexed by the group-averaged RT in Experiment 2. Then the z scored model vector was sign-flipped to reflect similarity instead of distance. The domain-specific model treats each conflict type differently, so we used a diagonal matrix, with within-conflict type similarities being 1 and all cross-conflict type similarities being 0.

Moreover, to examine if the cognitive space is driven solely by the Stroop or Simon conflicts, we tested a spatial Stroop-Only (hereafter referred to as “Stroop-Only”) and a Simon-Only model, with each conflict type projected onto the spatial Stroop (vertical) axis or Simon (horizontal) axis, respectively. The similarity between any two conflict types was defined using the Jaccard similarity index (Jaccard, 1901), that is, their intersection divided by their union. We also included a model assuming the Stroop and Simon dimensions are independently represented in the brain, adding up the Stroop Only and Simon-Only regressors. We conducted similar RSAs as reported above, replacing the original conflict similarity regressor with the Strrop-Only, Simon-Only, or both regressors, and then calculated their Bayesian information criterions (BICs)."

Reference:

Li, Q., Nan, W., Wang, K., & Liu, X. (2014). Independent processing of stimulus stimulus and stimulus-response conflicts. PloS One, 9(2), e89249.

8) Please clarify the observed patterns of CSE effects in relation to the hypothesis of common cognitive space of conflict. In particular, right 8C shows that the patterns become dissimilar in incongruent trials compared to congruent trials. How does this direction of the effect fit to the common unidimensional cognitive space account? And how does such a representation contribute to the CES effects?

The behavioral CSE patterns provide initial evidence for the cognitive space hypothesis. Previous studies have debated whether cognitive control relies on domain-general or domain-specific representations, with much evidence gathered from behavioral CSE patterns. A significant CSE across two conflict conditions typically suggests domain-general representations of cognitive control, while an absence of CSE suggests domain-specific representations. The cognitive space view proposes that conflict representations are neither purely domain-general nor purely domain-specific, but rather exist on a continuum. This view predicts that the CSE across two conflict conditions should depend on the representational distance between them within this cognitive space. Our finding that CSE values systematically vary with conflict similarity level support this hypothesis. We have added this point in the discussion of the revised manuscript:

“Previous research on this topic often adopts a binary manipulation of conflict(Braem et al., 2014) (i.e., each domain only has one conflict type) and gathered evidence for the domain-general/specific view with presence/absence of CSE, respectively. Here, we parametrically manipulated the similarity of conflict types and found the CSE systematically vary with conflict similarity level, demonstrating that cognitive control is neither purely domain-general nor purely domain-specific, but can be reconciled as a cognitive space(Bellmund et al., 2018) (Fig. 6, middle).

Fig. 4D was plotted to show the steeper slope of the conflict similarity effect for incongruent versus congruent conditions. Note the y-aixs displays z-scored Pearson correlation values, so the grand mean of each condition was 0. The values for the first two similarity levels (level 1 and 2) were lower for incongruent than congruent conditions, seemingly indicating lower average similarity. However, this was not the case. The five similarity levels contained different numbers of data points (see Fig. 1C), so levels 4 and 5 should be weighted more heavily than levels 1 and 2. When comparing the grand mean of raw Pearson correlation values, the incongruent condition (0.0053) showed a tendency toward higher similarity than the congruent condition (0.0040), t(475998) = 1.41, p = .079. We have also plotted another version of Fig. 4D in Fig. S5, in which the raw Pearson correlation values were used.

The greater representation of conflict type in incongruent condition compared to congruent condition (as evidenced by a steeper slope) suggests that the conflict representation was driven by the incongruent condition. This is probably due to the stronger involvement of cognitive control in incongruent condition (than congruent condition), which in turn leads to more distinct patterns across different conflict types. This is consistent with the fact that the congruent condition is typically a baseline, where any conflict related effects should be weaker.

The representation of cognitive space may contribute to the CSE as a mental model. This model allows our brain to evaluate the cost and benefit associated with transitioning between different conflict conditions. When two consecutive trials are characterized by more similar conflict types, their representations in the cognitive space will be closer, resulting in a less costly transition. As a consequence, stronger CSEs are observed. We revised the corresponding discussion part as:

“Similarly, we propose that cognitive space could serve as a mental model to assist fast learning and efficient organization of cognitive control settings. Specifically, the cognitive space representation may provide a principle for how our brain evaluates the expected cost of switching and the benefit of generalization between states and selects the path with the best cost-benefit tradeoff (Abrahamse et al., 2016; Shenhav et al., 2013). The proximity between two states in cognitive space could reflect both the expected cognitive demand required to transition and the useful mechanisms to adapt from. The closer the two conditions are in cognitive space, the lower the expected switching cost and the higher the generalizability when transitioning between them. With the organization of a cognitive space, a new conflict can be quickly assigned a location in the cognitive space, which will facilitate the development of cognitive control settings for this conflict by interpolating nearby conflicts and/or projecting the location to axes representing different cognitive control processes, thus leading to a stronger CSE when following a more similar conflict condition.”

Minor comments:

9) Some of the labels of figure axes are unclear (e.g., Fig4C) about what they represent.

In Fig. 4C, the x-axis label is “neural representational strength”, which refers to the beta coefficient of the conflict type effect computed from the main RSA, denoting the strength of the conflict type representation in neural patterns. The y-axis label is “behavioral representational strength”, which refers to the beta coefficient obtained from the behavioral linear model using conflict similarity to predict the CSE in Experiment 2; it reflects how strong the conflict similarity modulates the behavioral 1440 CSE. We apologize for any confusion from the brief axis labels. We have added expanded descriptions to the figure caption of Fig. 4C.

Author response:

The following is the authors’ response to the previous reviews.

To the Senior Editor and the Reviewing Editor:

We sincerely appreciate the valuable comments provided by the reviewers, the reviewing editor, and the senior editor. Based on our last response and revision, we are confused by the two limitations noted in the eLife assessment. 

(1) benchmarking against comparable methods is limited.

In our last revision, we added the comparison experiments with TNDM, as the reviewers requested. Additionally, it is crucial to emphasize that our evaluation of decoding capabilities of behaviorally relevant signals has been benchmarked against the performance of the ANN on raw signals, which, as Reviewer #1 previously noted, nearly represents the upper limit of performance. Consequently, we believe that our benchmarking methods are sufficiently strong.

(2) some observations may be a byproduct of their method, and may not constitute new scientific observations.

We believe that our experimental results are sufficient to demonstrate that our conclusions are not byproducts of d-VAE based on three reasons:

(1) The d-VAE, as a latent variable model, adheres to the population doctrine, which posits that latent variables are responsible for generating the activities of individual neurons. The goal of such models is to maximize the explanation of the raw signals. At the signal level, the only criterion we can rely on is neural reconstruction performance, in which we have achieved unparalleled results. Thus, it is inappropriate to focus on the mixing process during the model's inference stage while overlooking the crucial de-mixing process during the generation stage and dismissing the significance of our neural reconstruction results. For more details, please refer to the first point in our response to Q4 from Reviewer #4.

(2) The criterion that irrelevant signals should contain minimal information can effectively demonstrate that our conclusions are not by-products of d-VAE. Unfortunately, the reviewers seem to have overlooked this criterion. For more details, please refer to the third point in our response to Q4 from Reviewer #4

(3) Our synthetic experimental results also substantiate that our conclusions are not byproducts of d-VAE. However, it appears the reviewers did not give these results adequate consideration. For more details, please refer to the fourth point in our response to Q4 from Reviewer #4.

Furthermore, our work presents not just "a useful method" but a comprehensive framework. Our study proposes, for the first time, a framework for defining, extracting, and validating behaviorally relevant signals. In our current revision, to clearly distinguish between d-VAE and other methods, we have formalized the extraction of behaviorally relevant signals into a mathematical optimization problem. To our knowledge, current methods have not explicitly proposed extracting behaviorally relevant signals, nor have they identified and addressed the key challenges of extracting relevant signals. Similarly, existing research has not yet defined and validated behaviorally relevant signals. For more details, please refer to our response to Q1 from Reviewer #4.

Based on these considerations, we respectfully request that you reconsider the eLife assessment of our work. We greatly appreciate your time and attention to this matter.

The main revisions made to the manuscript are as follows:

(1) We have formalized the extraction of behaviorally relevant signals into a mathematical optimization problem, enabling a clearer distinction between d-VAE and other models.

(2) We have moderated the assertion about linear readout to highlight its conjectural nature and have broadened the discussion regarding this conclusion. 

(3) We have elaborated on the model details of d-VAE and have removed the identifiability claim.

To Reviewer #1

Q1: “As reviewer 3 also points out, I would, however, caution to interpret this as evidence for linear read-out of the motor system - your model performs a non-linear transformation, and while this is indeed linearly decodable, the motor system would need to do something similar first to achieve the same. In fact to me it seems to show the opposite, that behaviour-related information may not be generally accessible to linear decoders (including to down-stream brain areas).”

Thank you for your comments. It's important to note that the conclusions we draw are speculative and not definitive. We use terms like "suggest" to reflect this uncertainty. To further emphasize the conjectural nature of our conclusions, we have deliberately moderated our tone.

The question of whether behaviorally-relevant signals can be accessed by linear decoders or downstream brain regions hinges on the debate over whether the brain employs a strategy of filtering before decoding. If the brain employs such a strategy, the brain can probably access these signals. In our opinion, it is likely that the brain utilizes this strategy.

Given the existence of behaviorally relevant signals, it is reasonable to assume that the brain has intrinsic mechanisms to differentiate between relevant and irrelevant signals. There is growing evidence suggesting that the brain utilizes various mechanisms, such as attention and specialized filtering, to suppress irrelevant signals and enhance relevant signals [1-3]. Therefore, it is plausible that the brain filters before decoding, thereby effectively accessing behaviorally relevant signals.

Thank you for your valuable feedback.

(1) Sreenivasan, Sameet, and Ila Fiete. "Grid cells generate an analog error-correcting code for singularly precise neural computation." Nature neuroscience 14.10 (2011): 1330-1337.

(2) Schneider, David M., Janani Sundararajan, and Richard Mooney. "A cortical filter that learns to suppress the acoustic consequences of movement." Nature 561.7723 (2018): 391-395.

(3) Nakajima, Miho, L. Ian Schmitt, and Michael M. Halassa. "Prefrontal cortex regulates sensory filtering through a basal ganglia-to-thalamus pathway." Neuron 103.3 (2019): 445-458.

Q2: “As in my initial review, I would also caution against making strong claims about identifiability although this work and TNDM seem to show that in practise such methods work quite well. CEBRA, in contrast, offers some theoretical guarantees, but it is not a generative model, so would not allow the type of analysis done in this paper. In your model there is a para,eter \alpha to balance between neural and behaviour reconstruction. This seems very similar to TNDM and has to be optimised - if this is correct, then there is manual intervention required to identify a good model.”

Thank you for your comments. 

Considering your concerns about our identifiability claims and the fact that identifiability is not directly relevant to the core of our paper, we have removed content related to identifiability.

Firstly, our model is based on the pi-VAE, which also has theoretical guarantees. However, it is important to note that all such theoretical guarantees (including pi-VAE and CEBRA) are based on certain assumptions that cannot be validated as the true distribution of latent variables remains unknown.

Secondly, it is important to clarify that the identifiability of latent variables does not impact the conclusions of this paper, nor does this paper make specific conclusions about the model's latent variables. Identifiability means that distinct latent variables correspond to distinct observations. If multiple latent variables can generate the same observation, it becomes impossible to determine which one is correct given the observation, which leads to the issue of nonidentifiability. Notably, our analysis focuses on the generated signals, not the latent variables themselves, and thus the identifiability of these variables does not affect our findings. 

Our approach, dedicated to extracting these signals, distinctly differs from methods such as TNDM, which focuses on extracting behaviorally relevant latent dynamics. To clearly set apart d-VAE from other models, we have framed the extraction of behaviorally relevant signals as the following mathematical optimization problem:

where 𝑥# denotes generated behaviorally-relevant signals, 𝑥 denotes raw noisy signals, 𝐸(⋅,⋅) demotes reconstruction loss, and 𝑅(⋅) denotes regularization loss. It is important to note that while both d-VAE and TNDM employ reconstruction loss, relying solely on this term is insufficient for determining the optimal degree of similarity between the generated and raw noisy signals. The key to accurately extracting behaviorally relevant signals lies in leveraging prior knowledge about these signals to determine the optimal similarity degree, encapsulated by 𝑅(𝒙𝒓).  Other studies have not explicitly proposed extracting behaviorally-relevant signals, nor have they identified and addressed the key challenges involved in extracting relevant signals. Consequently, our approach is distinct from other methods.

Thank you for your valuable feedback.

Q3: “Somewhat related, I also found that the now comprehensive comparison with related models shows that the using decoding performance (R2) as a metric for model comparison may be problematic: the R2 values reported in Figure 2 (e.g. the MC_RTT dataset) should be compared to the values reported in the neural latent benchmark, which represent well-tuned models (e.g. AutoLFADS). The numbers (difficult to see, a table with numbers in the appendix would be useful, see: https://eval.ai/web/challenges/challenge-page/1256/leaderboard) seem lower than what can be obtained with models without latent space disentanglement. While this does not necessarily invalidate the conclusions drawn here, it shows that decoding performance can depend on a variety of model choices, and may not be ideal to discriminate between models. I'm also surprised by the low neural R2 for LFADS I assume this is condition-averaged) - LFADS tends to perform very well on this metric.”

Thank you for your comments. The dataset we utilized is not from the same day as the neural latent benchmark dataset. Notably, there is considerable variation in the length of trials within the RTT paradigm, and the dataset lacks explicit trial information, rendering trial-averaging unsuitable. Furthermore, behaviorally relevant signals are not static averages devoid of variability; even behavioral data exhibits variability. We computed the neural R2 using individual trials rather than condition-averaged responses. 

Thank you for your valuable feedback.

Q4: “One statement I still cannot follow is how the prior of the variational distribution is modelled. You say you depart from the usual Gaussian prior, but equation 7 seems to suggest there is a normal prior. Are the parameters of this distribution learned? As I pointed out earlier, I however suspect this may not matter much as you give the prior a very low weight. I also still am not sure how you generate a sample from the variational distribution, do you just draw one for each pass?”

Thank you for your questions.

The conditional distribution of prior latent variables 𝑝%(𝒛|𝒚) is a Gaussian distribution, but the distribution of prior latent variables 𝑝(𝒛) is a mixture Gaussian distribution. The distribution of prior latent variables 𝑝(𝒛) is:

where denotes the empirical distribution of behavioral variables

𝒚, and 𝑁 denotes the number of samples, 𝒚(𝒊) denotes the 𝒊th sample, δ(⋅) denotes the Dirac delta function, and 𝑝%(𝒛|𝒚) denotes the conditional distribution of prior latent variables given the behavioral variables parameterized by network 𝑚. Based on the above equation, we can see that 𝑝(𝒛) is not a Gaussian distribution, it is a Gaussian mixture model with 𝑁 components, which is theoretically a universal approximator of continuous probability densities.

Learning this prior is important, as illustrated by our latent variable visualizations, which are not a Gaussian distribution. Upon conducting hypothesis testing for both latent variables and behavioral variables, neither conforms to Gaussian distribution (Lilliefors test and Kolmogorov-Smirnov test). Consequently, imposing a constraint on the latent variables towards N(0,1) is expected to affect performance adversely.

Regarding sampling, during training process, we draw only one sample from the approximate posterior distribution . It is worth noting that drawing multiple samples or one sample for each pass does not affect the experimental results. After training, we can generate a sample from the prior by providing input behavioral data 𝒚(𝒊) and then generating corresponding samples via and . To extract behaviorally-relevant signals from raw signals, we use and .

Thank you for your valuable feedback.

Q5: “(1) I found the figures good and useful, but the text is, in places, not easy to follow. I think the manuscript could be shortened somewhat, and in some places more concise focussed explanations would improve readability.

(2) I would not call the encoding "complex non-linear" - non-linear is a clear term, but complex can mean many things (e.g. is a quadratic function complex?) ”

Thank you for your recommendation. We have revised the manuscript for enhanced clarity.  We call the encoding “complex nonlinear” because neurons encode information with varying degrees of nonlinearity, as illustrated in Fig. 3b, f, and Fig. S3b.

Thank you for your valuable feedback.

To Reviewer #2

Q1: “I still remain unconvinced that the core findings of the paper are "unexpected". In the response to my previous Specific Comment #1, they say "We use the term 'unexpected' due to the disparity between our findings and the prior understanding concerning neural encoding and decoding." However, they provide no citations or grounding for why they make those claims. What prior understanding makes it unexpected that encoding is more complex than decoding given the entropy, sparseness, and high dimensionality of neural signals (the "encoding") compared to the smoothness and low dimensionality of typical behavioural signals (the "decoding")?” 

Thank you for your comments. We believe that both the complexity of neural encoding and the simplicity of neural decoding in motor cortex are unexpected.

The Complexity of Neural Encoding: As noted in the Introduction, neurons with small R2 values were traditionally considered noise and consequently disregarded, as detailed in references [1-3]. However, after filtering out irrelevant signals, we discovered that these neurons actually contain substantial amounts of behavioral information, previously unrecognized. Similarly, in population-level analyses, neural signals composed of small principal components (PCs) are often dismissed as noise, with analyses typically utilizing only between 6 and 18 PCs [4-10]. Yet, the discarded PC signals nonlinearly encode significant amounts of information, with practically useful dimensions found to range between 30 and 40—far exceeding the usual number analyzed. These findings underscore the complexity of neural encoding and are unexpected.

The Simplicity of Neural Decoding: In the motor cortex, nonlinear decoding of raw signals has been shown to significantly outperform linear decoding, as evidenced in references [11,12]. Interestingly, after separating behaviorally relevant and irrelevant signals, we observed that the linear decoding performance of behaviorally relevant signals is nearly equivalent to that of nonlinear decoding—a phenomenon previously undocumented in the motor cortex. This discovery is also unexpected.

Thank you for your valuable feedback.

(1) Georgopoulos, Apostolos P., Andrew B. Schwartz, and Ronald E. Kettner. "Neuronal population coding of movement direction." Science 233.4771 (1986): 1416-1419.

(2) Hochberg, Leigh R., et al. "Reach and grasp by people with tetraplegia using a neurally controlled robotic arm." Nature 485.7398 (2012): 372-375. 

(3) Inoue, Yoh, et al. "Decoding arm speed during reaching." Nature communications 9.1 (2018): 5243.

(4) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(5) Kaufman, Matthew T., et al. "Cortical activity in the null space: permitting preparation without movement." Nature neuroscience 17.3 (2014): 440-448.

(6) Elsayed, Gamaleldin F., et al. "Reorganization between preparatory and movement population responses in motor cortex." Nature communications 7.1 (2016): 13239.

(7) Sadtler, Patrick T., et al. "Neural constraints on learning." Nature 512.7515 (2014): 423426.

(8) Golub, Matthew D., et al. "Learning by neural reassociation." Nature neuroscience 21.4 (2018): 607-616.

(9) Gallego, Juan A., et al. "Cortical population activity within a preserved neural manifold underlies multiple motor behaviors." Nature communications 9.1 (2018): 4233.

(10) Gallego, Juan A., et al. "Long-term stability of cortical population dynamics underlying consistent behavior." Nature neuroscience 23.2 (2020): 260-270.

(11) Glaser, Joshua I., et al. "Machine learning for neural decoding." Eneuro 7.4 (2020).

(12) Willsey, Matthew S., et al. "Real-time brain-machine interface in non-human primates achieves high-velocity prosthetic finger movements using a shallow feedforward neural network decoder." Nature Communications 13.1 (2022): 6899.

Q2: “I still take issue with the premise that signals in the brain are "irrelevant" simply because they do not correlate with a fixed temporal lag with a particular behavioural feature handchosen by the experimenter. In the response to my previous review, the authors say "we employ terms like 'behaviorally-relevant' and 'behaviorally-irrelevant' only regarding behavioral variables of interest measured within a given task, such as arm kinematics during a motor control task.". This is just a restatement of their definition, not a response to my concern, and does not address my concern that the method requires a fixed temporal lag and continual decoding/encoding. My example of reward signals remains. There is a huge body of literature dating back to the 70s on the linear relationships between neural and activity and arm kinematics; in a sense, the authors have chosen the "variable of interest" that proves their point. This all ties back to the previous comment: this is mostly expected, not unexpected, when relating apparently-stochastic, discrete action potential events to smoothly varying limb kinematics.”

Thank you for your comments. 

Regarding the experimenter's specification of behavioral variables of interest, we followed common practice in existing studies [1, 2]. Regarding the use of fixed temporal lags, we followed the same practice as papers related to the dataset we use, which assume fixed temporal lags [3-5]. Furthermore, many studies in the motor cortex similarly use fixed temporal lags [68].

Concerning the issue of rewards, in the paper you mentioned [9], the impact of rewards occurs after the reaching phase. It's important to note that in our experiments, we analyze only the reaching phase, without any post-movement phase. 

If the impact of rewards can be stably reflected in the signals in the reaching phase of the subsequent trial, and if the reward-induced signals do not interfere with decoding—since these signals are harmless for decoding and beneficial for reconstruction—our model is likely to capture these signals. If the signals induced by rewards during the reaching phase are randomly unstable, our model will likely be unable to capture them.

If the goal is to extract post-movement neural activity from both rewarded and unrewarded trials, and if the neural patterns differ between these conditions, one could replace the d-VAE's regression loss, used for continuous kinematics decoding, with a classification loss tailored to distinguish between rewarded and unrewarded conditions.

To clarify the definition, we have revised it in the manuscript. Specifically, before a specific definition, we briefly introduce the relevant signals and irrelevant signals. Behaviorally irrelevant signals refer to those not directly associated with the behavioral variables of interest and may include noise or signals from variables of no interest. In contrast, behaviorally relevant signals refer to those directly related to the behavioral variables of interest. For instance, rewards in the post-movement phase are not directly related to behavioral variables (kinematics) in the reaching movement phase.

It is important to note that our definition of behaviorally relevant signals not only includes decoding capabilities but also specific requirement at the signal level, based on two key requirements:

(1) they should closely resemble raw signals to preserve the underlying neuronal properties without becoming so similar that they include irrelevant signals. (encoding requirement), and  (2) they should contain behavioral information as much as possible (decoding requirement). Signals that meet both requirements are considered effective behaviorally relevant signals. In our study, we assume raw signals are additively composed of behaviorally-relevant and irrelevant signals. We define irrelevant signals as those remaining after subtracting relevant signals from raw signals. Therefore, we believe our definition is clearly articulated. 

Thank you for your valuable feedback.

(1) Sani, Omid G., et al. "Modeling behaviorally relevant neural dynamics enabled by preferential subspace identification." Nature Neuroscience 24.1 (2021): 140-149.

(2) Buetfering, Christina, et al. "Behaviorally relevant decision coding in primary somatosensory cortex neurons." Nature neuroscience 25.9 (2022): 1225-1236.

(3) Wang, Fang, et al. "Quantized attention-gated kernel reinforcement learning for brain– machine interface decoding." IEEE transactions on neural networks and learning systems 28.4 (2015): 873-886.

(4) Dyer, Eva L., et al. "A cryptography-based approach for movement decoding." Nature biomedical engineering 1.12 (2017): 967-976.

(5) Ahmadi, Nur, Timothy G. Constandinou, and Christos-Savvas Bouganis. "Robust and accurate decoding of hand kinematics from entire spiking activity using deep learning." Journal of Neural Engineering 18.2 (2021): 026011.

(6) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(7) Kaufman, Matthew T., et al. "Cortical activity in the null space: permitting preparation without movement." Nature neuroscience 17.3 (2014): 440-448.

(8) Elsayed, Gamaleldin F., et al. "Reorganization between preparatory and movement population responses in motor cortex." Nature communications 7.1 (2016): 13239.

(9) Ramkumar, Pavan, et al. "Premotor and motor cortices encode reward." PloS one 11.8 (2016): e0160851.

Q3: “The authors seem to have missed the spirit of my critique: to say "linear readout is performed in motor cortex" is an over-interpretation of what their model can show.”

Thank you for your comments. It's important to note that the conclusions we draw are speculative and not definitive. We use terms like "suggest" to reflect this uncertainty. To further emphasize the conjectural nature of our conclusions, we have deliberately moderated our tone.

The question of whether behaviorally-relevant signals can be accessed by downstream brain regions hinges on the debate over whether the brain employs a strategy of filtering before decoding. If the brain employs such a strategy, the brain can probably access these signals. In our view, it is likely that the brain utilizes this strategy.

Given the existence of behaviorally relevant signals, it is reasonable to assume that the brain has intrinsic mechanisms to differentiate between relevant and irrelevant signals. There is growing evidence suggesting that the brain utilizes various mechanisms, such as attention and specialized filtering, to suppress irrelevant signals and enhance relevant signals [1-3]. Therefore, it is plausible that the brain filters before decoding, thereby effectively accessing behaviorally relevant signals.

Regarding the question of whether the brain employs linear readout, given the limitations of current observational methods and our incomplete understanding of brain mechanisms, it is challenging to ascertain whether the brain employs a linear readout. In many cortical areas, linear decoders have proven to be sufficiently accurate. Consequently, numerous studies [4, 5, 6], including the one you referenced [4], directly employ linear decoders to extract information and formulate conclusions based on the decoding results. Contrary to these approaches, our research has compared the performance of linear and nonlinear decoders on behaviorally relevant signals and found their decoding performance is comparable. Considering both the decoding accuracy and model complexity, our results suggest that the motor cortex may utilize linear readout to decode information from relevant signals. Given the current technological limitations, we consider it reasonable to analyze collected data to speculate on the potential workings of the brain, an approach that many studies have also embraced [7-10]. For instance, a study [7] deduces strategies the brain might employ to overcome noise by analyzing the structure of recorded data and decoding outcomes for new stimuli.

Thank you for your valuable feedback.

(1) Sreenivasan, Sameet, and Ila Fiete. "Grid cells generate an analog error-correcting code for singularly precise neural computation." Nature neuroscience 14.10 (2011): 1330-1337.

(2) Schneider, David M., Janani Sundararajan, and Richard Mooney. "A cortical filter that learns to suppress the acoustic consequences of movement." Nature 561.7723 (2018): 391-395.

(3) Nakajima, Miho, L. Ian Schmitt, and Michael M. Halassa. "Prefrontal cortex regulates sensory filtering through a basal ganglia-to-thalamus pathway." Neuron 103.3 (2019): 445-458.

(4) Jurewicz, Katarzyna, et al. "Irrational choices via a curvilinear representational geometry for value." bioRxiv (2022): 2022-03.

(5) Hong, Ha, et al. "Explicit information for category-orthogonal object properties increases along the ventral stream." Nature neuroscience 19.4 (2016): 613-622.

(6) Chang, Le, and Doris Y. Tsao. "The code for facial identity in the primate brain." Cell 169.6 (2017): 1013-1028.

(7) Ganmor, Elad, Ronen Segev, and Elad Schneidman. "A thesaurus for a neural population code." Elife 4 (2015): e06134.

(8) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(9) Gallego, Juan A., et al. "Cortical population activity within a preserved neural manifold underlies multiple motor behaviors." Nature communications 9.1 (2018): 4233.

(10) Gallego, Juan A., et al. "Long-term stability of cortical population dynamics underlying consistent behavior." Nature neuroscience 23.2 (2020): 260-270.

Q4: “Agreeing with my critique is not sufficient; please provide the data or simulations that provides the context for the reference in the fano factor. I believe my critique is still valid.”

Thank you for your comments. As we previously replied, Churchland's research examines the variability of neural signals across different stages, including the preparation and execution phases, as well as before and after the target appears. Our study, however, focuses exclusively on the movement execution phase. Consequently, we are unable to produce comparative displays similar to those in his research. Intuitively, one might expect that the variability of behaviorally relevant signals would be lower; however, since no prior studies have accurately extracted such signals, the specific FF values of behaviorally relevant signals remain unknown. Therefore, presenting these values is meaningful, and can provide a reference for future research. While we cannot compare FF across different stages, we can numerically compare the values to the Poisson count process. An FF of 1 indicates a Poisson firing process, and our experimental data reveals that most neurons have an FF less than 1, indicating that the variance in firing counts is below the mean.  Thank you for your valuable feedback.

To Reviewer #4

Q1: “Overall, studying neural computations that are behaviorally relevant or not is an important problem, which several previous studies have explored (for example PSID in (Sani et al. 2021), TNDM in (Hurwitz et al. 2021), TAME-GP in (Balzani et al. 2023), pi-VAE in (Zhou and Wei 2020), and dPCA in (Kobak et al. 2016), etc). However, this manuscript does not properly put their work in the context of such prior works. For example, the abstract states "One solution is to accurately separate behaviorally-relevant and irrelevant signals, but this approach remains elusive", which is not the case given that these prior works have done that. The same is true for various claims in the main text, for example "Furthermore, we found that the dimensionality of primary subspace of raw signals (26, 64, and 45 for datasets A, B, and C) is significantly higher than that of behaviorally-relevant signals (7, 13, and 9), indicating that using raw signals to estimate the neural dimensionality of behaviors leads to an overestimation" (line 321). This finding was presented in (Sani et al. 2021) and (Hurwitz et al. 2021), which is not clarified here. This issue of putting the work in context has been brought up by other reviewers previously but seems to remain largely unaddressed. The introduction is inaccurate also in that it mixes up methods that were designed for separation of behaviorally relevant information with those that are unsupervised and do not aim to do so (e.g., LFADS). The introduction should be significantly revised to explicitly discuss prior models/works that specifically formulated this behavior separation and what these prior studies found, and how this study differs.”  

Thank you for your comments. Our statement about “One solution is to accurately separate behaviorally-relevant and irrelevant signals, but this approach remains elusive” is accurate. To our best knowledge, there is no prior works to do this work--- separating accurate behaviorally relevant neural signals at both single-neuron and single-trial resolution. The works you mentioned have not explicitly proposed extracting behaviorally relevant signals, nor have they identified and addressed the key challenges of extracting relevant signals, namely determining the optimal degree of similarity between the generated relevant signals and raw signals. Those works focus on the latent neural dynamics, rather than signal level.

To clearly set apart d-VAE from other models, we have framed the extraction of behaviorally relevant signals as the following mathematical optimization problem:

where 𝒙𝒓 denotes generated behaviorally-relevant signals, 𝒙 denotes raw noisy signals, 𝐸(⋅,⋅) demotes reconstruction loss, and 𝑅(⋅) denotes regularization loss. It is important to note that while both d-VAE and TNDM employ reconstruction loss, relying solely on this term is insufficient for determining the optimal degree of similarity between the generated and raw noisy signals. The key to accurately extracting behaviorally relevant signals lies in leveraging prior knowledge about these signals to determine the optimal similarity degree, encapsulated by 𝑅(𝒙𝒓). All the works you mentioned did not have the key part 𝑅(𝒙𝒓).

Regarding the dimensionality estimation, the dimensionality of neural manifolds quantifies the degrees of freedom required to describe population activity without significant information loss.

There are two differences between our work and PSID and TNDM. 

First, the dimensions they refer to are fundamentally different from ours. The dimensionality we describe pertains to a linear subspace, where a neural dimension or neural mode or principal component basis, , with N representing the number of neurons. However, the vector length of a neural mode of PSID and our approach differs; PSID requires concatenating multiple time steps T, essentially making , TNDM, on the other hand, involves nonlinear dimensionality reduction, which is different from linear dimensionality reduction.

Second, we estimate neural dimensionality by explaining the variance of neural signals, whereas PSID and TNDM determine dimensionality through decoding performance saturation. It is important to note that the dimensionality at which decoding performance saturates may not accurately reflect the true dimensionality of neural manifolds, as some dimensions may contain redundant information that does not enhance decoding performance.

We acknowledge that while LFADS can generate signals that contain some behavioral information, it was not specifically designed to do so. Following your suggestion, we have removed this reference from the Introduction.

Thank you for your valuable feedback.

Q2: “Claims about linearity of "motor cortex" readout are not supported by results yet stated even in the abstract. Instead, what the results support is that for decoding behavior from the output of the dVAE model -- that is trained specifically to have a linear behavior readout from its embedding -- a nonlinear readout does not help. This result can be biased by the very construction of the dVAE's loss that encourages a linear readout/decoding from embeddings, and thus does not imply a finding about motor cortex.”

Thank you for your comments. We respectfully disagree with the notion that the ability of relevant signals to be linearly decoded is due to constraints that allow embedding to be linearly decoded. Embedding involves reorganizing or transforming the structure of original signals, and they can be linearly decoded does not mean the corresponding signals can be decoded linearly.

Let's clarify this with three intuitive examples:

Example 1: Image denoising is a well-established field. Whether employing supervised or blind denoising methods [1, 2], both can effectively recover the original image. This denoising process closely resembles the extraction of behaviorally relevant signals from raw signals. Consider if noisy images are not amenable to linear decoding (classification); would removing the noise enable linear decoding? The answer is no. Typically, the noise in images captured under normal conditions is minimal, yet even the clear images remain challenging to decode linearly.

Example 2: Consider the task of face recognition, where face images are set against various backgrounds, in this context, the pixels representing the face corresponds to relevant signals, while the background pixels are considered irrelevant. Suppose a network is capable of extracting the face pixels and the resulting embedding can be linearly decoded. Can the face pixels themselves be linearly decoded? The answer is no. If linear decoding of face pixels were feasible, the challenging task of face recognition could be easily resolved by merely extracting the face from the background and training a linear classifier.

Example 3: In the MNIST dataset, the background is uniformly black, and its impact is minimal. However, linear SVM classifiers used directly on the original pixels significantly underperform compared to non-linear SVMs.

In summary, embedding involves reorganizing the structure of the original signals through a feature transformation function. However, the reconstruction process can recover the structure of the original signals from the embedding. The fact that the structure of the embedding can be linearly decoded does not imply that the structure of the original signals can be linearly decoded in the same way. It is inappropriate to focus on the compression process without equally considering the reconstruction process.

Thank you for your valuable feedback.

(1) Mao, Xiao-Jiao, Chunhua Shen, and Yu-Bin Yang. "Image restoration using convolutional auto-encoders with symmetric skip connections." arXiv preprint arXiv:1606.08921 (2016).

(2) Lehtinen, Jaakko, et al. "Noise2Noise: Learning image restoration without clean data." International Conference on Machine Learning. International Machine Learning Society, 2018.

Q3: “Related to the above, it is unclear what the manuscript means by readout from motor cortex. A clearer definition of "readout" (a mapping from what to what?) in general is needed. The mapping that the linearity/nonlinearity claims refer to is from the *inferred* behaviorally relevant neural signals, which themselves are inferred nonlinearly using the VAE. This should be explicitly clarified in all claims, i.e., that only the mapping from distilled signals to behavior is linear, not the whole mapping from neural data to behavior. Again, to say the readout from motor cortex is linear is not supported, including in the abstract.” 

Thank you for your comments. We have revised the manuscript to make it more clearly. Thank you for your valuable feedback.

Q4: “Claims about individual neurons are also confounded. The d-VAE distilling processing is a population level embedding so the individual distilled neurons are not obtainable on their own without using the population data. This population level approach also raises the possibility that information can leak from one neuron to another during distillation, which is indeed what the authors hope would recover true information about individual neurons that wasn't there in the recording (the pixel denoising example). The authors acknowledge the possibility that information could leak to a neuron that didn't truly have that information and try to rule it out to some extent with some simulations and by comparing the distilled behaviorally relevant signals to the original neural signals. But ultimately, the distilled signals are different enough from the original signals to substantially improve decoding of low information neurons, and one cannot be sure if all of the information in distilled signals from any individual neuron truly belongs to that neuron. It is still quite likely that some of the improved behavior prediction of the distilled version of low-information neurons is due to leakage of behaviorally relevant information from other neurons, not the former's inherent behavioral information. This should be explicitly acknowledged in the manuscript.”

Thank you for your comments. We value your insights regarding the mixing process. However, we are confident in the robustness of our conclusions. We respectfully disagree with the notion that the small R2 values containing significant information are primarily due to leakage, and we base our disagreement on four key reasons.

(1) Neural reconstruction performance is a reliable and valid criterion.

The purpose of latent variable models is to explain neuronal activity as much as possible. Given the fact that the ground truth of behaviorally-relevant signals, the latent variables, and the generative model is unknow, it becomes evident that the only reliable reference at the signal level is the raw signals. A crucial criterion for evaluating the reliability of latent variable models (including latent variables and generated relevant signals) is their capability to effectively explain the raw signals [1]. Consequently, we firmly maintain the belief that if the generated signals closely resemble the raw signals to the greatest extent possible, in accordance with an equivalence principle, we can claim that these obtained signals faithfully retain the inherent properties of single neurons. 

Reviewer #4 appears to focus on the compression (mixing) process without giving equal consideration to the reconstruction (de-mixing) process. Numerous studies have demonstrated that deep autoencoders can reconstruct the original signal very effectively. For example, in the field of image denoising, autoencoders are capable of accurately restoring the original image [2, 3]. If one persistently focuses on the fact of mixing and ignores the reconstruction （demix） process, even if the only criterion that we can rely on at the signal level is high, one still won't acknowledge it. If this were the case, many problems would become unsolvable. For instance, a fundamental criterion for latent variable models is their ability to explain the original data. If the ground truth of the latent variables remains unknown and the reconstruction criterion is disregarded, how can we validate the effectiveness of the model, the validity of the latent variables, or ensure that findings related to latent variables are not merely by-products of the model? Therefore, we disagree with the aforementioned notion. We believe that as long as the reconstruction performance is satisfactory, the extracted signals have successfully retained the characteristics of individual neurons.

In our paper, we have shown in various ways that our generated signals sufficiently resemble the raw signals, including visualizing neuronal activity (Fig. 2m, Fig. 3i, and Fig. S5), achieving the highest performance among competitors (Fig. 2d, h, l), and conducting control analyses. Therefore, we believe our results are reliable. 

(1) Cunningham, J.P. and Yu, B.M., 2014. Dimensionality reduction for large-scale neural recordings. Nature neuroscience, 17(11), pp.1500-1509.

(2) Mao, Xiao-Jiao, Chunhua Shen, and Yu-Bin Yang. "Image restoration using convolutional auto-encoders with symmetric skip connections." arXiv preprint arXiv:1606.08921 (2016).

(3) Lehtinen, Jaakko, et al. "Noise2Noise: Learning image restoration without clean data." International Conference on Machine Learning. International Machine Learning Society, 2018.

(2) There is no reason for d-VAE to add signals that do not exist in the original signals.

(1) Adding signals that does not exist in the small R2 neurons would decrease the reconstruction performance. This is because if the added signals contain significant information, they will not resemble the irrelevant signals which contain no information, and thus, the generated signals will not resemble the raw signals. The model optimizes towards reducing the reconstruction loss, and this scenario deviates from the model's optimization direction. It is worth mentioning that when the model only has reconstruction loss without the interference of decoding loss, we believe that information leakage does not happen. Because the model can only be optimized in a direction that is similar to the raw signals; adding non-existent signals to the generated signals would increase the reconstruction loss, which is contrary to the objective of optimization. 

(2) Information carried by these additional signals is redundant for larger R2 neurons, thus they do not introduce new information that can enhance the decoding performance of the neural population, which does not benefit the decoding loss.

Based on these two points, we believe the model would not perform such counterproductive and harmful operations.

(3) The criterion that irrelevant signals should contain minimal information can effectively rule out the leakage scenario.

The criterion that irrelevant signals should contain minimal information is very important, but it seems that reviewer #4 has continuously overlooked their significance. If the model's reconstruction is insufficient, or if additional information is added (which we do not believe will happen), the residuals would decode a large amount of information, and this criterion would exclude selecting such signals. To clarify, if we assume that x, y, and z denote the raw, relevant, and irrelevant signals of smaller R2 neurons, with x=y+z, and the extracted relevant signals become y+m, the irrelevant signals become z-m in this case. Consequently, the irrelevant signals contain a significant amount of information.

We presented the decoding R2 for irrelevant signals in real datasets under three distillation scenarios: a bias towards reconstruction (alpha=0, an extreme case where the model only has reconstruction loss without decoding loss), a balanced trade-off, and a bias towards decoding (alpha=0.9), as detailed in Table 1. If significant information from small R2 neurons leaks from large R2 neurons, the irrelevant signals should contain a large amount of information. However, our results indicate that the irrelevant signals contain only minimal information, and their performance closely resembles that of the model training solely with reconstruction loss, showing no significant differences (P > 0.05, Wilcoxon rank-sum test). When the model leans towards decoding, some useful information will be left in the residuals, and irrelevant signals will contain a substantial amount of information, as observed in Table 1, alpha=0.9. Therefore, we will not choose these signals for analysis.

In conclusion, the criterion that irrelevant signals should contain minimal information is a very effective measure to exclude undesirable signals.

Author response table 1.

Decoding R2 of irrelevant signals

(4) Synthetic experiments can effectively rule out the leakage scenario.

In the absence of ground truth data, synthetic experiments serve as an effective method for validating models and are commonly employed [1-3]. 

Our experimental results demonstrate that d-VAE can effectively extract neural signals that more closely resemble actual behaviorally relevant signals (Fig. S2g).  If there were information leakage, it would decrease the similarity to the ground truth signals, hence we have ruled out this possibility. Moreover, in synthetic experiments with small R2 neurons (Fig. S10), results also demonstrate that our model could make these neurons more closely resemble ground truth relevant signals and recover their information. 

In summary, synthetic experiments strongly demonstrate that our model can recover obscured neuronal information, rather than adding signals that do not exist.

(1) Pnevmatikakis, Eftychios A., et al. "Simultaneous denoising, deconvolution, and demixing of calcium imaging data." Neuron 89.2 (2016): 285-299.

(2) Schneider, Steffen, Jin Hwa Lee, and Mackenzie Weygandt Mathis. "Learnable latent embeddings for joint behavioural and neural analysis." Nature 617.7960 (2023): 360-368.

(3) Zhou, Ding, and Xue-Xin Wei. "Learning identifiable and interpretable latent models of high-dimensional neural activity using pi-VAE." Advances in Neural Information Processing Systems 33 (2020): 7234-7247.

Based on these four points, we are confident in the reliability of our results. If Reviewer #4 considers these points insufficient, we would highly appreciate it if specific concerns regarding any of these aspects could be detailed.

Thank you for your valuable feedback.

Q5: “Given the nuances involved in appropriate comparisons across methods and since two of the datasets are public, the authors should provide their complete code (not just the dVAE method code), including the code for data loading, data preprocessing, model fitting and model evaluation for all methods and public datasets. This will alleviate concerns and allow readers to confirm conclusions (e.g., figure 2) for themselves down the line.”

Thanks for your suggestion.

Our codes are now available on GitHub at https://github.com/eric0li/d-VAE. Thank you for your valuable feedback.

Q6: “Related to 1) above, the authors should explore the results if the affine network h(.) (from embedding to behavior) was replaced with a nonlinear ANN. Perhaps linear decoders would no longer be as close to nonlinear decoders. Regardless, the claim of linearity should be revised as described in 1) and 2) above, and all caveats should be discussed.”

Thank you for your suggestion. We appreciate your feasible proposal that can be empirically tested. Following your suggestion, we have replaced the decoding of the latent variable z to behavior y with a nonlinear neural network, specifically a neural network with a single hidden layer. The modified model is termed d-VAE2. We applied the d-VAE2 to the real data, and selected the optimal alpha through the validation set. As shown in Table 1, results demonstrate that the performance of KF and ANN remains comparable. Therefore, the capacity to linearly decode behaviorally relevant signals does not stem from the linear decoding of embeddings.

Author response table 2.

Decoding R2 of behaviorally relevant signals obtained by d-VAE2

Additionally, it is worth noting that this approach is uncommon and is considered somewhat inappropriate according to the Information Bottleneck theory [1]. According to the Information Bottleneck theory, information is progressively compressed in multilayer neural networks, discarding what is irrelevant to the output and retaining what is relevant. This means that as the number of layers increases, the mutual information between each layer's embedding and the model input gradually decreases, while the mutual information between each layer's embedding and the model output gradually increases. For the decoding part, if the embeddings that is not closest to the output (behaviors) is used, then these embeddings might contain behaviorally irrelevant signals. Using these embeddings to generate behaviorally relevant signals could lead to the inclusion of irrelevant signals in the behaviorally relevant signals.

To demonstrate the above statement, we conducted experiments on the synthetic data. As shown in Table 2, we present the performance (neural R2 between the generated signals and the ground truth signals) of both models at several alpha values around the optimal alpha of dVAE (alpha=0.9) selected by the validation set. The experimental results show that at the same alpha value, the performance of d-VAE2 is consistently inferior to that of d-VAE, and d-VAE2 requires a higher alpha value to achieve performance comparable to d-VAE, and the best performance of d-VAE2 is inferior to that of d-VAE.

Author response table 3.

Neural R2 between generated signals and real behaviorally relevant signals

Thank you for your valuable feedback.

(1) Shwartz-Ziv, Ravid, and Naftali Tishby. "Opening the black box of deep neural networks via information." arXiv preprint arXiv:1703.00810 (2017).

Q7: “The beginning of the section on the "smaller R2 neurons" should clearly define what R2 is being discussed. Based on the response to previous reviewers, this R2 "signifies the proportion of neuronal activity variance explained by the linear encoding model, calculated using raw signals". This should be mentioned and made clear in the main text whenever this R2 is referred to.”

Thank you for your suggestion. We have made the modifications in the main text. Thank you for your valuable feedback.

Q8: “Various terms require clear definitions. The authors sometimes use vague terminology (e.g., "useless") without a clear definition. Similarly, discussions regarding dimensionality could benefit from more precise definitions. How is neural dimensionality defined? For example, how is "neural dimensionality of specific behaviors" (line 590) defined? Related to this, I agree with Reviewer 2 that a clear definition of irrelevant should be mentioned that clarifies that relevance is roughly taken as "correlated or predictive with a fixed time lag". The analyses do not explore relevance with arbitrary time lags between neural and behavior data.”

Thanks for your suggestion. We have removed the “useless” statements and have revised the statement of “the neural dimensionality of specific behaviors” in our revised manuscripts.

Regarding the use of fixed temporal lags, we followed the same practice as papers related to the dataset we use, which assume fixed temporal lags [1-3]. Furthermore, many studies in the motor cortex similarly use fixed temporal lags [4-6]. To clarify the definition, we have revised the definition in our manuscript. For details, please refer to the response to Q2 of reviewer #2 and our revised manuscript. We believe our definition is clearly articulated.

Thank you for your valuable feedback.

(1) Wang, Fang, et al. "Quantized attention-gated kernel reinforcement learning for brain– machine interface decoding." IEEE transactions on neural networks and learning systems 28.4 (2015): 873-886.

(2) Dyer, Eva L., et al. "A cryptography-based approach for movement decoding." Nature biomedical engineering 1.12 (2017): 967-976.

(3) Ahmadi, Nur, Timothy G. Constandinou, and Christos-Savvas Bouganis. "Robust and accurate decoding of hand kinematics from entire spiking activity using deep learning." Journal of Neural Engineering 18.2 (2021): 026011.

(4) Churchland, Mark M., et al. "Neural population dynamics during reaching." Nature 487.7405 (2012): 51-56.

(5) Kaufman, Matthew T., et al. "Cortical activity in the null space: permitting preparation without movement." Nature neuroscience 17.3 (2014): 440-448.

(6) Elsayed, Gamaleldin F., et al. "Reorganization between preparatory and movement population responses in motor cortex." Nature communications 7.1 (2016): 13239. 

Q9: “CEBRA itself doesn't provide a neural reconstruction from its embeddings, but one could obtain one via a regression from extracted CEBRA embeddings to neural data. In addition to decoding results of CEBRA (figure S3), the neural reconstruction of CEBRA should be computed and CEBRA should be added to Figure 2 to see how the behaviorally relevant and irrelevant signals from CEBRA compare to other methods.”

Thank you for your question. Modifying CEBRA is beyond the scope of our work. As CEBRA is not a generative model, it cannot obtain behaviorally relevant and irrelevant signals, and therefore it lacks the results presented in Fig. 2. To avoid the same confusion encountered by reviewers #3 and #4 among our readers, we have opted to exclude the comparison with CEBRA. It is crucial to note, as previously stated, that our assessment of decoding capabilities has been benchmarked against the performance of the ANN on raw signals, which almost represents the upper limit of performance. Consequently, omitting CEBRA does not affect our conclusions.

Thank you for your valuable feedback.

Q10: “Line 923: "The optimal hyperparameter is selected based on the lowest averaged loss of five-fold training data." => why is this explained specifically under CEBRA? Isn't the same criteria used for hyperparameters of other methods? If so, clarify.”

Thank you for your question. The hyperparameter selection for CEBRA follows the practice of the original CEBRA paper. The hyperparameter selection for generative models is detailed in the Section “The strategy for selecting effective behaviorally-relevant signals”.  Thank you for your valuable feedback.

Author Response

The following is the authors’ response to the previous reviews.

To the Senior Editor and the Reviewing Editor:

We sincerely appreciate the valuable comments provided by the reviewers, the reviewing editor, and the senior editor. After carefully reviewing and considering the comments, we have addressed the key concerns raised by the reviewers and made appropriate modifications to the article in the revised manuscript.

The main revisions made to the manuscript are as follows:

1) We have added comparison experiments with TNDM (see Fig. 2 and Fig. S2).

2) We conducted new synthetic experiments to demonstrate that our conclusions are not a by-product of d-VAE (see Fig. S2 and Fig. S11).

3) We have provided a detailed explanation of how our proposed criteria, especially the second criterion, can effectively exclude the selection of unsuitable signals.

4) We have included a semantic overview figure of d-VAE (Fig. S1) and a visualization plot of latent variables (Fig. S13).

5) We have elaborated on the model details of d-VAE, as well as the hyperparameter selection and experimental settings of other comparison models.

We believe these revisions have significantly improved the clarity and comprehensibility of the manuscript. Thank you for the opportunity to address these important points.

Reviewer #1

Q1: “First, the model in the paper is almost identical to an existing VAE model (TNDM) that makes use of weak supervision with behaviour in the same way [1]. This paper should at least be referenced. If the authors wish they could compare their model to TNDM, which combines a state space model with smoothing similar to LFADS. Given that TNDM achieves very good behaviour reconstructions, it may be on par with this model without the need for a Kalman filter (and hence may achieve better separation of behaviour-related and unrelated dynamics).”

Our model significantly differs from TNDM in several aspects. While TNDM also constrains latent variables to decode behavioral information, it does not impose constraints to maximize behavioral information in the generated relevant signals. The trade-off between the decoding and reconstruction capabilities of generated relevant signals is the most significant contribution of our approach, which is not reflected in TNDM. In addition, the backbone network of signal extraction and the prior distribution of the two models are also different.

It's worth noting that our method does not require a Kalman filter. Kalman filter is used for post hoc assessment of the linear decoding ability of the generated signals. Please note that extracting and evaluating relevant signals are two distinct stages.

Heeding your suggestion, we have incorporated comparison experiments involving TNDM into the revised manuscript. Detailed information on model hyperparameters and training settings can be found in the Methods section in the revised manuscripts.

Thank you for your valuable feedback.

Q2: “Second, in my opinion, the claims regarding identifiability are overstated - this matters as the results depend on this to some extent. Recent work shows that VAEs generally suffer from identifiability problems due to the Gaussian latent space [2]. This paper also hints that weak supervision may help to resolve such issues, so this model as well as TNDM and CEBRA may indeed benefit from this. In addition however, it appears that the relative weight of the KL Divergence in the VAE objective is chosen very small compared to the likelihood (0.1%), so the influence of the prior is weak and the model may essentially learn the average neural trajectories while underestimating the noise in the latent variables. This, in turn, could mean that the model will not autoencode neural activity as well as it should, note that an average R2 in this case will still be high (I could not see how this is actually computed). At the same time, the behaviour R2 will be large simply because the different movement trajectories are very distinct. Since the paper makes claims about the roles of different neurons, it would be important to understand how well their single trial activities are reconstructed, which can perhaps best be investigated by comparing the Poisson likelihood (LFADS is a good baseline model). Taken together, while it certainly makes sense that well-tuned neurons contribute more to behaviour decoding, I worry that the very interesting claim that neurons with weak tuning contain behavioural signals is not well supported.”

We don’t think our distilled signals are average neural trajectories without variability. The quality of reconstructing single trial activities can be observed in Figure 3i and Figure S4. Neural trajectories in Fig. 3i and Fig. S4 show that our distilled signals are not average neural trajectories. Furthermore, if each trial activity closely matched the average neural trajectory, the Fano Factor (FF) should theoretically approach 0. However, our distilled signals exhibit a notable departure from this expectation, as evident in Figure 3c, d, g, and f. Regarding the diminished influence of the KL Divergence: Given that the ground truth of latent variable distribution is unknown, even a learned prior distribution might not accurately reflect the true distribution. We found the pronounced impact of the KL divergence would prove detrimental to the decoding and reconstruction performance. As a result, we opt to reduce the weight of the KL divergence term. Even so, KL divergence can still effectively align the distribution of latent variables with the distribution of prior latent variables, as illustrated in Fig. S13. Notably, our goal is extracting behaviorally-relevant signals from given raw signals rather than generating diverse samples from the prior distribution. When aim to separating relevant signals, we recommend reducing the influence of KL divergence. Regarding comparing the Poisson likelihood: We compared Poisson log-likelihood among different methods (except PSID since their obtained signals have negative values), and the results show that d-VAE outperforms other methods.

Author response image 1.

Regarding how R2 is computed: , where and denote ith sample of raw signals, ith sample of distilled relevant signals, and the mean of raw signals. If the distilled signals exactly match the raw signals, the sum of squared error is zero, thus R2=1. If the distilled signals always are equal to R2=0. If the distilled signals are worse than the mean estimation, R2 is negative, negative R2 is set to zero.

Thank you for your valuable feedback.

Q3: “Third, and relating to this issue, I could not entirely follow the reasoning in the section arguing that behavioural information can be inferred from neurons with weak selectivity, but that it is not linearly decodable. It is right to test if weak supervision signals bleed into the irrelevant subspace, but I could not follow the explanations. Why, for instance, is the ANN decoder on raw data (I assume this is a decoder trained fully supervised) not equal in performance to the revenant distilled signals? Should a well-trained non-linear decoder not simply yield a performance ceiling? Next, if I understand correctly, distilled signals were obtained from the full model. How does a model perform trained only on the weakly tuned neurons? Is it possible that the subspaces obtained with the model are just not optimally aligned for decoding? This could be a result of limited identifiability or model specifics that bias reconstruction to averages (a well-known problem of VAEs). I, therefore, think this analysis should be complemented with tests that do not depend on the model.”

Regarding “Why, for instance, is the ANN decoder on raw data (I assume this is a decoder trained fully supervised) not equal in performance to the relevant distilled signals? Should a well-trained non-linear decoder not simply yield a performance ceiling?”: In fact, the decoding performance of raw signals with ANN is quite close to the ceiling. However, due to the presence of significant irrelevant signals in raw signals, decoding models like deep neural networks are more prone to overfitting when trained on noisy raw signals compared to behaviorally-relevant signals. Consequently, we anticipate that the distilled signals will demonstrate superior decoding generalization. This phenomenon is evident in Fig. 2 and Fig. S1, where the decoding performance of the distilled signals surpasses that of the raw signals, albeit not by a substantial margin.

Regarding “Next, if I understand correctly, distilled signals were obtained from the full model. How does a model perform trained only on the weakly tuned neurons? Is it possible that the subspaces obtained with the model are just not optimally aligned for decoding?”：Distilled signals (involving all neurons) are obtained by d-VAE. Subsequently, we use ANN to evaluate the performance of smaller and larger R2 neurons. Please note that separating and evaluating relevant signals are two distinct stages.

Regarding the reasoning in the section arguing that smaller R2 neurons encode rich information, we would like to provide a detailed explanation:

1) After extracting relevant signals through d-VAE, we specifically selected neurons characterized by smaller R2 values (Here, R2 signifies the proportion of neuronal activity variance explained by the linear encoding model, calculated using raw signals). Subsequently, we employed both KF and ANN to assess the decoding performance of these neurons. Remarkably, our findings revealed that smaller R2 neurons, previously believed to carry limited behavioral information, indeed encode rich information.

2) In a subsequent step, we employed d-VAE to exclusively distill the raw signals of these smaller R2 neurons (distinct from the earlier experiment where d-VAE processed signals from all neurons). We then employed KF and ANN to evaluate the distilled smaller R2 neurons. Interestingly, we observed that we could not attain the same richness of information solely through the use of these smaller R2 neurons.

3) Consequently, we put forth and tested two hypotheses: First, that larger R2 neurons introduce additional signals into the smaller R2 neurons that do not exist in the real smaller R2 neurons. Second, that larger R2 neurons aid in restoring the original appearance of impaired smaller R2 neurons. Our proposed criteria and synthetic experiments substantiate the latter scenario.

Thank you for your valuable feedback.

Q4: “Finally, a more technical issue to note is related to the choice to learn a non-parametric prior instead of using a conventional Gaussian prior. How is this implemented? Is just a single sample taken during a forward pass? I worry this may be insufficient as this would not sample the prior well, and some other strategy such as importance sampling may be required (unless the prior is not relevant as it weakly contributed to the ELBO, in which case this choice seems not very relevant). Generally, it would be useful to see visualisations of the latent variables to see how information about behaviour is represented by the model.”

Regarding "how to implement the prior?": Please refer to Equation 7 in the revised manuscript; we have added detailed descriptions in the revised manuscript.

Regarding "Generally, it would be useful to see visualizations of the latent variables to see how information about behavior is represented by the model.": Note that our focus is not on latent variables but on distilled relevant signals. Nonetheless, at your request, we have added the visualization of latent variables in the revised manuscript. Please see Fig. S13 for details.

Thank you for your valuable feedback.

Recommendations: “A minor point: the word 'distill' in the name of the model may be a little misleading - in machine learning the term refers to the construction of smaller models with the same capabilities.

It should be useful to add a schematic picture of the model to ease comparison with related approaches.”

In the context of our model's functions, it operates as a distillation process, eliminating irrelevant signals and retaining the relevant ones. Although the name of our model may be a little misleading, it faithfully reflects what our model does.

I have added a schematic picture of d-VAE in the revised manuscript. Please see Fig. S1 for details.

Thank you for your valuable feedback.

Reviewer #2

Q1: “Is the apparently increased complexity of encoding vs decoding so unexpected given the entropy, sparseness, and high dimensionality of neural signals (the "encoding") compared to the smoothness and low dimensionality of typical behavioural signals (the "decoding") recorded in neuroscience experiments? This is the title of the paper so it seems to be the main result on which the authors expect readers to focus. ”

We use the term "unexpected" due to the disparity between our findings and the prior understanding concerning neural encoding and decoding. For neural encoding, as we said in the Introduction, in previous studies, weakly-tuned neurons are considered useless, and smaller variance PCs are considered noise, but we found they encode rich behavioral information. For neural decoding, the nonlinear decoding performance of raw signals is significantly superior to linear decoding. However, after eliminating the interference of irrelevant signals, we found the linear decoding performance is comparable to nonlinear decoding. Rooted in these findings, which counter previous thought, we employ the term "unexpected" to characterize our observations.

Thank you for your valuable feedback.

Q2: “I take issue with the premise that signals in the brain are "irrelevant" simply because they do not correlate with a fixed temporal lag with a particular behavioural feature hand-chosen by the experimenter. As an example, the presence of a reward signal in motor cortex [1] after the movement is likely to be of little use from the perspective of predicting kinematics from time-bin to time-bin using a fixed model across trials (the apparent definition of "relevant" for behaviour here), but an entire sub-field of neuroscience is dedicated to understanding the impact of these reward-related signals on future behaviour. Is there method sophisticated enough to see the behavioural "relevance" of this brief, transient, post-movement signal? This may just be an issue of semantics, and perhaps I read too much into the choice of words here. Perhaps the authors truly treat "irrelevant" and "without a fixed temporal correlation" as synonymous phrases and the issue is easily resolved with a clarifying parenthetical the first time the word "irrelevant" is used. But I remain troubled by some claims in the paper which lead me to believe that they read more deeply into the "irrelevancy" of these components.”

In this paper, we employ terms like ‘behaviorally-relevant’ and ‘behaviorally-irrelevant’ only regarding behavioral variables of interest measured within a given task, such as arm kinematics during a motor control task. A similar definition can be found in the PSID[1].

Thank you for your valuable feedback.

[1] Sani, Omid G., et al. "Modeling behaviorally relevant neural dynamics enabled by preferential subspace identification." Nature Neuroscience 24.1 (2021): 140-149.

Q3: “The authors claim the "irrelevant" responses underpin an unprecedented neuronal redundancy and reveal that movement behaviors are distributed in a higher-dimensional neural space than previously thought." Perhaps I just missed the logic, but I fail to see the evidence for this. The neural space is a fixed dimensionality based on the number of neurons. A more sparse and nonlinear distribution across this set of neurons may mean that linear methods such as PCA are not effective ways to approximate the dimensionality. But ultimately the behaviourally relevant signals seem quite low-dimensional in this paper even if they show some nonlinearity may help.”

The evidence for the “useless” responses underpin an unprecedented neuronal redundancy is shown in Fig. 5a, d and Fig. S9a. Specifically, the sum of the decoding performance of smaller R2 neurons and larger R2 neurons is significantly greater than that of all neurons for relevant signals (red bar), demonstrating that movement parameters are encoded very redundantly in neuronal population. In contrast, we can not find this degree of neural redundancy in raw signals (purple bar).

The evidence for the “useless” responses reveal that movement behaviors are distributed in a higher-dimensional neural space than previously thought is shown in the left plot (involving KF decoding) of Fig. 6c, f and Fig. S9f. Specifically, the improvement of KF using secondary signals is significantly higher than using raw signals composed of the same number of dimensions as the secondary signals. These results demonstrate that these dimensions, spanning roughly from ten to thirty, encode much information, suggesting that behavioral information exists in a higher-dimensional subspace than anticipated from raw signals.

Thank you for your valuable feedback.

Q5: “there is an apparent logical fallacy that begins in the abstract and persists in the paper: "Surprisingly, when incorporating often-ignored neural dimensions, behavioral information can be decoded linearly as accurately as nonlinear decoding, suggesting linear readout is performed in motor cortex." Don't get me wrong: the equivalency of linear and nonlinear decoding approaches on this dataset is interesting, and useful for neuroscientists in a practical sense. However, the paper expends much effort trying to make fundamental scientific claims that do not feel very strongly supported. This reviewer fails to see what we can learn about a set of neurons in the brain which are presumed to "read out" from motor cortex. These neurons will not have access to the data analyzed here. That a linear model can be conceived by an experimenter does not imply that the brain must use a linear model. The claim may be true, and it may well be that a linear readout is implemented in the brain. Other work [2,3] has shown that linear readouts of nonlinear neural activity patterns can explain some behavioural features. The claim in this paper, however, is not given enough”

Due to the limitations of current observational methods and our incomplete understanding of brain mechanisms, it is indeed challenging to ascertain the specific data the brain acquires to generate behavior and whether it employs a linear readout. Conventionally, the neural data recorded in the motor cortex do encode movement behaviors and can be used to analyze neural encoding and decoding. Based on these data, we found that the linear decoder KF achieves comparable performance to that of the nonlinear decoder ANN on distilled relevant signals. This finding has undergone validation across three widely used datasets, providing substantial evidence. Furthermore, we conducted experiments on synthetic data to show that this conclusion is not a by-product of our model. In the revised manuscript, we added a more detailed description of this conclusion.

Thank you for your valuable feedback.

Q6: “Relatedly, I would like to note that the exercise of arbitrarily dividing a continuous distribution of a statistic (the "R2") based on an arbitrary threshold is a conceptually flawed exercise. The authors read too much into the fact that neurons which have a low R2 w.r.t. PDs have behavioural information w.r.t. other methods. To this reviewer, it speaks more about the irrelevance, so to speak, of the preferred direction metric than anything fundamental about the brain.”

We chose the R2 threshold in accordance with the guidelines provided in reference [1]. It's worth mentioning that this threshold does not exert any significant influence on the overall conclusions.

Thank you for your valuable feedback.

[1] Inoue, Y., Mao, H., Suway, S.B., Orellana, J. and Schwartz, A.B., 2018. Decoding arm speed during reaching. Nature communications, 9(1), p.5243.

Q7: “I am afraid I may be missing something, as I did not understand the fano factor analysis of Figure 3. In a sense the behaviourally relevant signals must have lower FF given they are in effect tied to the temporally smooth (and consistent on average across trials) behavioural covariates. The point of the original Churchland paper was to show that producing a behaviour squelches the variance; naturally these must appear in the behaviourally relevant components. A control distribution or reference of some type would possibly help here.”

We agree that including reference signals could provide more context. The Churchland paper said stimulus onset can lead to a reduction in neural variability. However, our experiment focuses specifically on the reaching process, and thus, we don't have comparative experiments involving different types of signals.

Thank you for your valuable feedback.

Q8: “The authors compare the method to LFADS. While this is a reasonable benchmark as a prominent method in the field, LFADS does not attempt to solve the same problem as d-VAE. A better and much more fair comparison would be TNDM [4], an extension of LFADS which is designed to identify behaviourally relevant dimensions.”

We have added the comparison experiments with TNDM in the revised manuscript (see Fig. 2 and Fig. S2). The details of model hyperparameters and training settings can be found in the Methods section in the revised manuscripts.

Thank you for your valuable feedback.

Reviewer #3

Q1.1: “TNDM: LFADS is not the best baseline for comparison. The authors should have compared with TNDM (Hurwitz et al. 2021), which is an extension of LFADS that (unlike LFADS) actually attempts to extract behaviorally relevant factors by adding a behavior term to the loss. The code for TNDM is also available on Github. LFADS is not even supervised by behavior and does not aim to address the problem that d-VAE aims to address, so it is not the most appropriate comparison. ”

We have added the comparison experiments with TNDM in the revised manuscript (see Fig. 2 and Fig. S2). The details of model hyperparameters and training settings can be found in the Methods section in the revised manuscripts.

Thank you for your valuable feedback.

Q1.2: “LFADS: LFADS is a sequential autoencoder that processes sections of data (e.g. trials). No explanation is given in Methods for how the data was passed to LFADS. Was the moving averaged smoothed data passed to LFADS or the raw spiking data (at what bin size)? Was a gaussian loss used or a poisson loss? What are the trial lengths used in each dataset, from which part of trials? For dataset C that has back-to-back reaches, was data chopped into segments? How long were these segments? Were the edges of segments overlapped and averaged as in (Keshtkaran et al. 2022) to avoid noisy segment edges or not? These are all critical details that are not explained. The same details would also be needed for a TNDM comparison (comment 1.1) since it has largely the same architecture as LFADS.

It is also critical to briefly discuss these fundamental differences between the inputs of methods in the main text. LFADS uses a segment of data whereas VAE methods just use one sample at a time. What does this imply in the results? I guess as long as VAEs outperform LFADS it is ok, but if LFADS outperforms VAEs in a given metric, could it be because it received more data as input (a whole segment)? Why was the factor dimension set to 50? I presume it was to match the latent dimension of the VAE methods, but is the LFADS factor dimension the correct match for that to make things comparable?

I am also surprised by the results. How do the authors justify LFADS having lower neural similarity (fig 2d) than VAE methods that operate on single time steps? LFADS is not supervised by behavior, so of course I don't expect it to necessarily outperform methods on behavior decoding. But all LFADS aims to do is to reconstruct the neural data so at least in this metric it should be able to outperform VAEs that just operate on single time steps? Is it because LFADS smooths the data too much? This is important to discuss and show examples of. These are all critical nuances that need to be discussed to validate the results and interpret them.”

Regarding “Was the moving averaged smoothed data passed to LFADS or the raw spiking data (at what bin size)? Was a gaussian loss used or a poisson loss?”: The data used by all models was applied to the same preprocessing procedure. That is, using moving averaged smoothed data with three bins, where the bin size is 100ms. For all models except PSID, we used a Poisson loss.

Regrading “What are the trial lengths used in each dataset, from which part of trials? For dataset C that has back-to-back reaches, was data chopped into segments? How long were these segments? Were the edges of segments overlapped and averaged as in (Keshtkaran et al. 2022) to avoid noisy segment edges or not?”:

For datasets A and B, a trial length of eighteen is set. Trials with lengths below the threshold are zero-padded, while trials exceeding the threshold are truncated to the threshold length from their starting point. In dataset A, there are several trials with lengths considerably longer than that of most trials. We found that padding all trials with zeros to reach the maximum length (32) led to poor performance. Consequently, we chose a trial length of eighteen, effectively encompassing the durations of most trials and leading to the removal of approximately 9% of samples. For dataset B (center-out), the trial lengths are relatively consistent with small variation, and the maximum length across all trials is eighteen. For dataset C, we set the trial length as ten because we observed the video of this paradigm and found that the time for completing a single trial was approximately one second. The segments are not overlapped.

Regarding “Why was the factor dimension set to 50? I presume it was to match the latent dimension of the VAE methods, but is the LFADS factor dimension the correct match for that to make things comparable?”: We performed a grid search for latent dimensions in {10,20,50} and found 50 is the best.

Regarding “I am also surprised by the results. How do the authors justify LFADS having lower neural similarity (fig 2d) than VAE methods that operate on single time steps? LFADS is not supervised by behavior, so of course I don't expect it to necessarily outperform methods on behavior decoding. But all LFADS aims to do is to reconstruct the neural data so at least in this metric it should be able to outperform VAEs that just operate on single time steps? Is it because LFADS smooths the data too much?”: As you pointed out, we found that LFADS tends to produce excessively smooth and consistent data, which can lead to a reduction in neural similarity.

Thank you for your valuable feedback.

Q1.3: “PSID: PSID is linear and uses past input samples to predict the next sample in the output. Again, some setup choices are not well justified, and some details are left out in the 1-line explanation given in Methods.

Why was a latent dimension of 6 chosen? Is this the behaviorally relevant latent dimension or the total latent dimension (for the use case here it would make sense to set all latent states to be behaviorally relevant)? Why was a horizon hyperparameter of 3 chosen? First, it is important to mention fundamental parameters such as latent dimension for each method in the main text (not just in methods) to make the results interpretable. Second, these hyperparameters should be chosen with a grid search in each dataset (within the training data, based on performance on the validation part of the training data), just as the authors do for their method (line 779). Given that PSID isn't a deep learning method, doing a thorough grid search in each fold should be quite feasible. It is important that high values for latent dimension and a wider range of other hyperparmeters are included in the search, because based on how well the residuals (x_i) for this method are shown predict behavior in Fig 2, the method seems to not have been used appropriately. I would expect ANN to improve decoding for PSID versus its KF decoding since PSID is fully linear, but I don't expect KF to be able to decode so well using the residuals of PSID if the method is used correctly to extract all behaviorally relevant information from neural data. The low neural reconstruction in Fid 2d could also partly be due to using too small of a latent dimension.

Again, another import nuance is the input to this method and how differs with the input to VAE methods. The learned PSID model is a filter that operates on all past samples of input to predict the output in the "next" time step. To enable a fair comparison with VAE methods, the authors should make sure that the last sample "seen" by PSID is the same as then input sample seen by VAE methods. This is absolutely critical given how large the time steps are, otherwise PSID might underperform simply because it stopped receiving input 300ms earlier than the input received by VAE methods. To fix this, I think the authors can just shift the training and testing neural time series of PSID by 1 sample into the past (relative to the behavior), so that PSID's input would include the input of VAE methods. Otherwise, VAEs outperforming PSID is confounded by PSID's input not including the time step that was provided to VAE.”

Thanks for your suggestions for letting PSID see the current neural observations. We did it per your suggestions and then performed a grid search for the hyperparameters for PSID. Specifically, we performed a grid search for the horizon hyperparameter in {2,3,4,5,6,7}. Since the relevant latent dimension should be lower than the horizon times the dimension of behavior variables (two-dimensional velocity in this paper) and increasing the dimension will reach performance saturation, we directly set the relevant latent dimensions as the maximum. The horizon number of datasets A, B, C, and synthetic datasets is 7, 6, 6 and 5, respectively.

And thus the latent dimension of datasets A, B, and C and the synthetic dataset is 14, 12, 12 and 10, respectively.

Our experiments show that KF can decode information from irrelevant signals obtained by PSID. Although PSID extracts the linear part of raw signals, KF can still use the linear part of the residuals for decoding. The low reconstruction performance of PSID may be because the relationship between latent variables and neural signals is linear, and the relationship between latent variables and behaviors is also linear; this is equivalent to the linear relationship between behaviors and neural signals, and linear models can only explain a small fraction of neural signals.

Thank you for your valuable feedback.

Q1.4: “CEBRA: results for CEBRA are incomplete. Similarity to raw signals is not shown. Decoding of behaviorally irrelevant residuals for CEBRA is not shown. Per Fig. S2, CEBRA does better or similar ANN decoding in datasets A and C, is only slightly worse in Dataset B, so it is important to show the other key metrics otherwise it is unclear whether d-VAE has some tangible advantage over CEBRA in those 2 datasets or if they are similar in every metric. Finally, it would be better if the authors show the results for CEBRA on Fig. 2, just as is done for other methods because otherwise it is hard to compare all methods.”

CEBRA is a non-generative model, this model cannot generate behaviorally-relevant signals. Therefore, we only compared the decoding performance of latent embeddings of CEBRA and signals of d-VAE.

Thank you for your valuable feedback.

Q2: “Given the fact that d-VAE infers the latent (z) based on the population activity (x), claims about properties of the inferred behaviorally relevant signals (x_r) that attribute properties to individual neurons are confounded.

The authors contrast their approach to population level approaches in that it infers behaviorally relevant signals for individual neurons. However, d-VAE is also a population method as it aggregates population information to infer the latent (z), from which behaviorally relevant part of the activity of each neuron (x_r) is inferred. The authors note this population level aggregation of information as a benefit of d-VAE, but only acknowledge it as a confound briefly in the context of one of their analyses (line 340): "The first is that the larger R2 neurons leak their information to the smaller R2 neurons, causing them contain too much behavioral information". They go on to dismiss this confounding possibility by showing that the inferred behaviorally relevant signal of each neuron is often most similar to its own raw signals (line 348-352) compared with all other neurons. They also provide another argument specific to that result section (i.e., residuals are not very behavior predictive), which is not general so I won't discuss it in depth here. These arguments however do not change the basic fact that d-VAE aggregates information from other neurons when extracting the behaviorally relevant activity of any given neuron, something that the authors note as a benefit of d-VAE in many instances. The fact that d-VAE aggregates population level info to give the inferred behaviorally relevant signal for each neuron confounds several key conclusions. For example, because information is aggregated across neurons, when trial to trial variability looks smoother after applying d-VAE (Fig 3i), or reveals better cosine tuning (Fig 3b), or when neurons that were not very predictive of behavior become more predictive of behavior (Fig 5), one cannot really attribute the new smoother single trial activity or the improved decoding to the same single neurons; rather these new signals/performances include information from other neurons. Unless the connections of the encoder network (z=f(x)) is zero for all other neurons, one cannot claim that the inferred rates for the neuron are truly solely associated with that neuron. I believe this a fundamental property of a population level VAE, and simply makes the architecture unsuitable for claims regarding inherent properties of single neurons. This confound is partly why the first claim in the abstract are not supported by data: observing that neurons that don't predict behavior very well would predict it much better after applying d-VAE does not prove that these neurons themselves "encode rich[er] behavioral information in complex nonlinear ways" (i.e., the first conclusion highlighted in the abstract) because information was also aggregated from other neurons. The other reason why this claim is not supported by data is the characterization of the encoding for smaller R2 neurons as "complex nonlinear", which the method is not well equipped to tease apart from linear mappings as I explain in my comment 3.”

We acknowledge that we cannot obtain the exact single neuronal activity that does not contain any information from other neurons. However, we believe our model can extract accurate approximation signals of the ground truth relevant signals. These signals preserve the inherent properties of single neuronal activity to some extent and can be used for analysis at the single-neuron level.

We believe d-VAE is a reasonable approach to extract effective relevant signals that preserve inherent properties of single neuronal activity for four key reasons:

1) d-VAE is a latent variable model that adheres to the neural population doctrine. The neural population doctrine posits that information is encoded within interconnected groups of neurons, with the existence of latent variables (neural modes) responsible for generating observable neuronal activity [1, 2]. If we can perfectly obtain the true generative model from latent variables to neuronal activity, then we can generate the activity of each neuron from hidden variables without containing any information from other neurons. However, without a complete understanding of the brain’s encoding strategies (or generative model), we can only get the approximation signals of the ground truth signals.

2) After the generative model is established, we need to infer the parameters of the generative model and the distribution of latent variables. During the inference process, inference algorithms such as variational inference or EM algorithms will be used. Generally, the obtained latent variables are also approximations of the real latent variables. When inferring the latent variables, it is inevitable to aggregation the information of the neural population, and latent variables are derived through weighted combinations of neuronal populations [3].

This inference process is consistent with that of d-VAE (or VAE-based models).

3) Latent variables are derived from raw neural signals and used to explain raw neural signals. Considering the unknown ground truth of latent variables and behaviorally-relevant signals, it becomes evident that the only reliable reference at the signal level is the raw signals. A crucial criterion for evaluating the reliability of latent variable models (including latent variables and generated relevant signals) is their capability to effectively explain the raw signals [3]. Consequently, we firmly maintain the belief that if the generated signals closely resemble the raw signals to the greatest extent possible, in accordance with an equivalence principle, we can claim that these obtained signals faithfully retain the inherent properties of single neurons. d-VAE explicitly constrains the generated signal to closely resemble the raw signals. These results demonstrate that d-VAE can extract effective relevant signals that preserve inherent properties of single neuronal activity.

Based on the above reasons, we hold that generating single neuronal activities with the VAE framework is a reasonable approach. The remaining question is whether our model can obtain accurate relevant signals in the absence of ground truth. To our knowledge, in cases where the ground truth of relevant signals is unknown, there are typically two approaches to verifying the reliability of extracted signals:

1) Conducting synthetic experiments where the ground truth is known.

2) Validation based on expert knowledge (Three criteria were proposed in this paper). Both our extracted signals and key conclusions have been validated using these two approaches.

Next, we will provide a detailed response to the concerns regarding our first key conclusion that smaller R2 neurons encode rich information.

We acknowledge that larger R2 neurons play a role in aiding the reconstruction of signals in smaller R2 neurons through their neural activity. However, considering that neurons are correlated rather than independent entities, we maintain the belief that larger R2 neurons assist damaged smaller R2 neurons in restoring their original appearance. Taking image denoising as an example, when restoring noisy pixels to their original appearance, relying solely on the noisy pixels themselves is often impractical. Assistance from their correlated, clean neighboring pixels becomes necessary.

The case we need to be cautious of is that the larger R2 neurons introduce additional signals (m) that contain substantial information to smaller R2 neurons, which they do not inherently possess. We believe this case does not hold for two reasons. Firstly, logically, adding extra signals decreases the reconstruction performance, and the information carried by these additional signals is redundant for larger R2 neurons, thus they do not introduce new information that can enhance the decoding performance of the neural population. Therefore, it seems unlikely and unnecessary for neural networks to engage in such counterproductive actions. Secondly, even if this occurs, our second criterion can effectively exclude the selection of these signals. To clarify, if we assume that x, y, and z denote the raw, relevant, and irrelevant signals of smaller R2 neurons, with x=y+z, and the extracted relevant signals become y+m, the irrelevant signals become z-m in this case. Consequently, the irrelevant signals contain a significant amount of information. It's essential to emphasize that this criterion holds significant importance in excluding undesirable signals.

Furthermore, we conducted a synthetic experiment to show that d-VAE can indeed restore the damaged information of smaller R2 neurons with the help of larger R2 neurons, and the restored neuronal activities are more similar to ground truth compared to damaged raw signals. Please see Fig. S11a,b for details.

Thank you for your valuable feedback.

[1] Saxena, S. and Cunningham, J.P., 2019. Towards the neural population doctrine. Current opinion in neurobiology, 55, pp.103-111.

[2] Gallego, J.A., Perich, M.G., Miller, L.E. and Solla, S.A., 2017. Neural manifolds for the control of movement. Neuron, 94(5), pp.978-984.

[3] Cunningham, J.P. and Yu, B.M., 2014. Dimensionality reduction for large-scale neural recordings. Nature neuroscience, 17(11), pp.1500-1509.

Q3: “Given the nonlinear architecture of the VAE, claims about the linearity or nonlinearity of cortical readout are confounded and not supported by the results.

The inference of behaviorally relevant signals from raw signals is a nonlinear operation, that is x_r=g(f(x)) is nonlinear function of x. So even when a linear KF is used to decode behavior from the inferred behaviorally relevant signals, the overall decoding from raw signals to predicted behavior (i.e., KF applied to g(f(x))) is nonlinear. Thus, the result that decoding of behavior from inferred behaviorally relevant signals (x_r) using a linear KF and a nonlinear ANN reaches similar accuracy (Fig 2), does not suggest that a "linear readout is performed in the motor cortex", as the authors claim (line 471). The authors acknowledge this confound (line 472) but fail to address it adequately. They perform a simulation analysis where the decoding gap between KF and ANN remains unchanged even when d-VAE is used to infer behaviorally relevant signals in the simulation. However, this analysis is not enough for "eliminating the doubt" regarding the confound. I'm sure the authors can also design simulations where the opposite happens and just like in the data, d-VAE can improve linear decoding to match ANN decoding. An adequate way to address this concern would be to use a fully linear version of the autoencoder where the f(.) and g(.) mappings are fully linear. They can simply replace these two networks in their model with affine mappings, redo the modeling and see if the model still helps the KF decoding accuracy reach that of the ANN decoding. In such a scenario, because the overall KF decoding from original raw signals to predicted behavior (linear d-VAE + KF) is linear, then they could move toward the claim that the readout is linear. Even though such a conclusion would still be impaired by the nonlinear reference (d-VAE + ANN decoding) because the achieved nonlinear decoding performance could always be limited by network design and fitting issues. Overall, the third conclusion highlighted in the abstract is a very difficult claim to prove and is unfortunately not supported by the results.”

We aim to explore the readout mechanism of behaviorally-relevant signals, rather than raw signals. Theoretically, the process of removing irrelevant signals should not be considered part of the inherent decoding mechanisms of the relevant signals. Assuming that the relevant signals we extracted are accurate, the conclusion of linear readout is established. On the synthetic data where the ground truth is known, our distilled signals show a significant improvement in neural similarity to the ground truth when compared to raw signals (refer to Fig. S2l). This observation demonstrates that our distilled signals are accurate approximations of the ground truth. Furthermore, on the three widely-used real datasets, our distilled signals meet the stringent criteria we have proposed (see Fig. 2), also providing strong evidence for their accuracy.

Regarding the assertion that we could create simulations in which d-VAE can make signals that are inherently nonlinearly decodable into linearly decodable ones: In reality, we cannot achieve this, as the second criterion can rule out the selection of such signals. Specifically,z=x+y=n^2+y, where z, x, y, and n denote raw signals, relevant signals, irrelevant signals and latent variables. If the relevant signals obtained by d-VAE are n, then these signals can be linear decoded accurately. However, the corresponding irrelevant signals are n^2-n+z; thus, irrelevant signals will have much information, and these extracted relevant signals will not be selected. Furthermore, our synthetic experiments offer additional evidence supporting the conclusion that d-VAE does not make inherently nonlinearly decodable signals become linearly decodable ones. As depicted in Fig. S11c, there exists a significant performance gap between KF and ANN when decoding the ground truth signals of smaller R2 neurons. KF exhibits notably low performance, leaving substantial room for compensation by d-VAE. However, following processing by d-VAE, KF's performance of distilled signals fails to surpass its already low ground truth performance and remains significantly inferior to ANN's performance. These results collectively confirm that our approach does not convert signals that are inherently nonlinearly decodable into linearly decodable ones, and the conclusion of linear readout is not a by-product by d-VAE.

Regarding the suggestion of using linear d-VAE + KF, as discussed in the Discussion section, removing the irrelevant signals requires a nonlinear operation, and linear d-VAE can not effectively separate relevant and irrelevant signals.

Thank you for your valuable feedback.

Q4: “The authors interpret several results as indications that "behavioral information is distributed in a higher-dimensional subspace than expected from raw signals", which is the second main conclusion highlighted in the abstract. However, several of these arguments do not convincingly support that conclusion.

4.1) The authors observe that behaviorally relevant signals for neurons with small principal components (referred to as secondary) have worse decoding with KF but better decoding with ANN (Fig. 6b,e), which also outperforms ANN decoding from raw signals. This observation is taken to suggest that these secondary behaviorally relevant signals encode behavior information in highly nonlinear ways and in a higher dimensions neural space than expected (lines 424 and 428). These conclusions however are confounded by the fact that A) d-VAE uses nonlinear encoding, so one cannot conclude from ANN outperforming KF that behavior is encoded nonlinearly in the motor cortex (see comment 3 above), and B) d-VAE aggregates information across the population so one cannot conclude that these secondary neurons themselves had as much behavior information (see comment 2 above).

4.2) The authors observe that the addition of the inferred behaviorally relevant signals for neurons with small principal components (referred to as secondary) improves the decoding of KF more than it improves the decoding of ANN (red curves in Fig 6c,f). This again is interpreted similarly as in 4.1, and is confounded for similar reasons (line 439): "These results demonstrate that irrelevant signals conceal the smaller variance PC signals, making their encoded information difficult to be linearly decoded, suggesting that behavioral information exists in a higher-dimensional subspace than anticipated from raw signals". This is confounded by because of the two reasons explained in 4.1. To conclude nonlinear encoding based on the difference in KF and ANN decoding, the authors would need to make the encoding/decoding in their VAE linear to have a fully linear decoder on one hand (with linear d-VAE + KF) and a nonlinear decoder on the other hand (with linear d-VAE + ANN), as explained in comment 3.

4.3) From S Fig 8, where the authors compare cumulative variance of PCs for raw and inferred behaviorally relevant signals, the authors conclude that (line 554): "behaviorally-irrelevant signals can cause an overestimation of the neural dimensionality of behaviorally-relevant responses (Supplementary Fig. S8)." However, this analysis does not really say anything about overestimation of "behaviorally relevant" neural dimensionality since the comparison is done with the dimensionality of "raw" signals. The next sentence is ok though: "These findings highlight the need to filter out relevant signals when estimating the neural dimensionality.", because they use the phrase "neural dimensionality" not "neural dimensionality of behaviorally-relevant responses".”

Questions 4.1 and 4.2 are a combination of Q2 and Q3. Please refer to our responses to Q2 and Q3.

Regarding question 4.3 about “behaviorally-irrelevant signals can cause an overestimation of the neural dimensionality of behaviorally-relevant responses”: Previous studies usually used raw signals to estimate the neural dimensionality of specific behaviors. We mean that using raw signals, which include many irrelevant signals, will cause an overestimation of the neural dimensionality. We have modified this sentence in the revised manuscripts.

Thank you for your valuable feedback.

Q5: “Imprecise use of language in many places leads to inaccurate statements. I will list some of these statements”

5.1) In the abstract: "One solution is to accurately separate behaviorally-relevant and irrelevant signals, but this approach remains elusive due to the unknown ground truth of behaviorally-relevant signals". This statement is not accurate because it implies no prior work does this. The authors should make their statement more specific and also refer to some goal that existing linear (e.g., PSID) and nonlinear (e.g., TNDM) methods for extracting behaviorally relevant signals fail to achieve.

5.2) In the abstract: "we found neural responses previously considered useless encode rich behavioral information" => what does "useless" mean operationally? Low behavior tuning? More precise use of language would be better.

5.3) "... recent studies (Glaser 58 et al., 2020; Willsey et al., 2022) demonstrate nonlinear readout outperforms linear readout." => do these studies show that nonlinear "readout" outperforms linear "readout", or just that nonlinear models outperform linear models?

5.4) Line 144: "The first criterion is that the decoding performance of the behaviorally-relevant signals (red bar, Fig.1) should surpass that of raw signals (the red dotted line, Fig.1).". Do the authors mean linear decoding here or decoding in general? If the latter, how can something extracted from neural surpass decoding of neural data, when the extraction itself can be thought of as part of decoding? The operational definition for this "decoding performance" should be clarified.

5.5) Line 311: "we found that the dimensionality of primary subspace of raw signals (26, 64, and 45 for datasets A, B, and C) is significantly higher than that of behaviorally-relevant signals (7, 13, and 9), indicating that behaviorally-irrelevant signals lead to an overestimation of the neural dimensionality of behaviorally-relevant signals." => here the dimensionality of the total PC space (i.e., primary subspace of raw signals) is being compared with that of inferred behaviorally-relevant signals, so the former being higher does not indicate that neural dimensionality of behaviorally-relevant signals was overestimated. The former is simply not behavioral so this conclusion is not accurate.

5.6) Section "Distilled behaviorally-relevant signals uncover that smaller R2 neurons encode rich behavioral information in complex nonlinear ways". Based on what kind of R2 are the neurons grouped? Behavior decoding R2 from raw signals? Using what mapping? Using KF? If KF is used, the result that small R2 neurons benefit a lot from d-VAE could be somewhat expected, given the nonlinearity of d-VAE: because only ANN would have the capacity to unwrap the nonlinear encoding of d-VAE as needed. If decoding performance that is used to group neurons is based on data, regression to the mean could also partially explain the result: the neurons with worst raw decoding are most likely to benefit from a change in decoder, than neurons that already had good decoding. In any case, the R2 used to partition and sort neurons should be more clearly stated and reminded throughout the text and I Fig 3.

5.7) Line 346 "...it is impossible for our model to add the activity of larger R2 neurons to that of smaller R2 neurons" => Is it really impossible? The optimization can definitely add small-scale copies of behaviorally relevant information to all neurons with minimal increase in the overall optimization loss, so this statement seems inaccurate.

5.8) Line 490: "we found that linear decoders can achieve comparable performance to that of nonlinear decoders, providing compelling evidence for the presence of linear readout in the motor cortex." => inaccurate because no d-VAE decoding is really linear, as explained in comment 3 above.

5.9) Line 578: ". However, our results challenge this idea by showing that signals composed of smaller variance PCs nonlinearly encode a significant amount of behavioral information." => inaccurate as results are confounded by nonlinearity of d-VAE as explained in comment 3 above.

5.10) Line 592: "By filtering out behaviorally-irrelevant signals, our study found that accurate decoding performance can be achieved through linear readout, suggesting that the motor cortex may perform linear readout to generate movement behaviors." => inaccurate because it us confounded by the nonlinearity of d-VAE as explained in comment 3 above.”

Regarding “5.1) In the abstract: "One solution is to accurately separate behaviorally-relevant and irrelevant signals, but this approach remains elusive due to the unknown ground truth of behaviorally-relevant signals". This statement is not accurate because it implies no prior work does this. The authors should make their statement more specific and also refer to some goal that existing linear (e.g., PSID) and nonlinear (e.g., TNDM) methods for extracting behaviorally relevant signals fail to achieve”:

We believe our statement is accurate. Our primary objective is to extract accurate behaviorally-relevant signals that closely approximate the ground truth relevant signals. To achieve this, we strike a balance between the reconstruction and decoding performance of the generated signals, aiming to effectively capture the relevant signals. This crucial aspect of our approach sets it apart from other methods. In contrast, other methods tend to emphasize the extraction of valuable latent neural dynamics. We have provided elaboration on the distinctions between d-VAE and other approaches in the Introduction and Discussion sections.

Thank you for your valuable feedback.

Regarding “5.2) In the abstract: "we found neural responses previously considered useless encode rich behavioral information" => what does "useless" mean operationally? Low behavior tuning? More precise use of language would be better.”:

In the analysis of neural signals, smaller variance PC signals are typically seen as noise and are often discarded. Similarly, smaller R2 neurons are commonly thought to be dominated by noise and are not further analyzed. Given these considerations, we believe that the term "considered useless" is appropriate in this context. Thank you for your valuable feedback.

Regarding “5.3) "... recent studies (Glaser 58 et al., 2020; Willsey et al., 2022) demonstrate nonlinear readout outperforms linear readout." => do these studies show that nonlinear "readout" outperforms linear "readout", or just that nonlinear models outperform linear models?”:

In this paper, we consider the two statements to be equivalent. Thank you for your valuable feedback.

Regarding “5.4) Line 144: "The first criterion is that the decoding performance of the behaviorally-relevant signals (red bar, Fig.1) should surpass that of raw signals (the red dotted line, Fig.1).". Do the authors mean linear decoding here or decoding in general? If the latter, how can something extracted from neural surpass decoding of neural data, when the extraction itself can be thought of as part of decoding? The operational definition for this "decoding performance" should be clarified.”:

We mean the latter, as we said in the section “Framework for defining, extracting, and separating behaviorally-relevant signals”, since raw signals contain too many behaviorally-irrelevant signals, deep neural networks are more prone to overfit raw signals than relevant signals. Therefore the decoding performance of relevant signals should surpass that of raw signals. Thank you for your valuable feedback.

Regarding “5.5) Line 311: "we found that the dimensionality of primary subspace of raw signals (26, 64, and 45 for datasets A, B, and C) is significantly higher than that of behaviorally-relevant signals (7, 13, and 9), indicating that behaviorally-irrelevant signals lead to an overestimation of the neural dimensionality of behaviorally-relevant signals." => here the dimensionality of the total PC space (i.e., primary subspace of raw signals) is being compared with that of inferred behaviorally-relevant signals, so the former being higher does not indicate that neural dimensionality of behaviorally-relevant signals was overestimated. The former is simply not behavioral so this conclusion is not accurate.”: In practice, researchers usually used raw signals to estimate the neural dimensionality. We mean that using raw signals to do this would overestimate the neural dimensionality. Thank you for your valuable feedback.

Regarding “5.6) Section "Distilled behaviorally-relevant signals uncover that smaller R2 neurons encode rich behavioral information in complex nonlinear ways". Based on what kind of R2 are the neurons grouped? Behavior decoding R2 from raw signals? Using what mapping? Using KF? If KF is used, the result that small R2 neurons benefit a lot from d-VAE could be somewhat expected, given the nonlinearity of d-VAE: because only ANN would have the capacity to unwrap the nonlinear encoding of d-VAE as needed. If decoding performance that is used to group neurons is based on data, regression to the mean could also partially explain the result: the neurons with worst raw decoding are most likely to benefit from a change in decoder, than neurons that already had good decoding. In any case, the R2 used to partition and sort neurons should be more clearly stated and reminded throughout the text and I Fig 3.”:

When employing R2 to characterize neurons, it indicates the extent to which neuronal activity is explained by the linear encoding model [1-3]. Smaller R2 neurons have a lower capacity for linearly tuning (encoding) behaviors, while larger R2 neurons have a higher capacity for linearly tuning (encoding) behaviors. Specifically, the approach involves first establishing an encoding relationship from velocity to neural signal using a linear model, i.e., y=f(x), where f represents a linear regression model, x denotes velocity, and y denotes the neural signal. Subsequently, R2 is utilized to quantify the effectiveness of the linear encoding model in explaining neural activity. We have provided a comprehensive explanation in the revised manuscript. Thank you for your valuable feedback.

[1] Collinger, J.L., Wodlinger, B., Downey, J.E., Wang, W., Tyler-Kabara, E.C., Weber, D.J., McMorland, A.J., Velliste, M., Boninger, M.L. and Schwartz, A.B., 2013. High-performance neuroprosthetic control by an individual with tetraplegia. The Lancet, 381(9866), pp.557-564.

[2] Wodlinger, B., et al. "Ten-dimensional anthropomorphic arm control in a human brain− machine interface: difficulties, solutions, and limitations." Journal of neural engineering 12.1 (2014): 016011.

[3] Inoue, Y., Mao, H., Suway, S.B., Orellana, J. and Schwartz, A.B., 2018. Decoding arm speed during reaching. Nature communications, 9(1), p.5243.

Regarding Questions 5.7, 5.8, 5.9, and 5.10:

We believe our conclusions are solid. The reasons can be found in our replies in Q2 and Q3. Thank you for your valuable feedback.

Q6: “Imprecise use of language also sometimes is not inaccurate but just makes the text hard to follow.

6.1) Line 41: "about neural encoding and decoding mechanisms" => what is the definition of encoding/decoding and how do these differ? The definitions given much later in line 77-79 is also not clear.

6.2) Line 323: remind the reader about what R2 is being discussed, e.g., R2 of decoding behavior using KF. It is critical to know if linear or nonlinear decoding is being discussed.

6.3) Line 488: "we found that neural responses previously considered trivial encode rich behavioral information in complex nonlinear ways" => "trivial" in what sense? These phrases would benefit from more precision, for example: "neurons that may seem to have little or no behavior information encoded". The same imprecise word ("trivial") is also used in many other places, for example in the caption of Fig S9.

6.4) Line 611: "The same should be true for the brain." => Too strong of a statement for an unsupported claim suggesting the brain does something along the lines of nonlin VAE + linear readout.

6.5) In Fig 1, legend: what is the operational definition of "generating performance"? Generating what? Neural reconstruction?”

Regarding “6.1) Line 41: "about neural encoding and decoding mechanisms" => what is the definition of encoding/decoding and how do these differ? The definitions given much later in line 77-79 is also not clear.”:

We would like to provide a detailed explanation of neural encoding and decoding. Neural encoding means how neuronal activity encodes the behaviors, that is, y=f(x), where y denotes neural activity and, x denotes behaviors, f is the encoding model. Neural decoding means how the brain decodes behaviors from neural activity, that is, x=g(y), where g is the decoding model. For further elaboration, please refer to [1]. We have included references that discuss the concepts of encoding and decoding in the revised manuscript. Thank you for your valuable feedback.

[1] Kriegeskorte, Nikolaus, and Pamela K. Douglas. "Interpreting encoding and decoding models." Current opinion in neurobiology 55 (2019): 167-179.

Regarding “6.2) Line 323: remind the reader about what R2 is being discussed, e.g., R2 of decoding behavior using KF. It is critical to know if linear or nonlinear decoding is being discussed.”:

This question is the same as Q5.6. Please refer to the response to Q5.6. Thank you for your valuable feedback.

Regarding “6.3) Line 488: "we found that neural responses previously considered trivial encode rich behavioral information in complex nonlinear ways" => "trivial" in what sense? These phrases would benefit from more precision, for example: "neurons that may seem to have little or no behavior information encoded". The same imprecise word ("trivial") is also used in many other places, for example in the caption of Fig S9.”:

We have revised this statement in the revised manuscript. Thanks for your recommendation.

Regarding “6.4) Line 611: "The same should be true for the brain." => Too strong of a statement for an unsupported claim suggesting the brain does something along the lines of nonlin VAE + linear readout.”

We mean that removing the interference of irrelevant signals and decoding the relevant signals should logically be two stages. We have revised this statement in the revised manuscript. Thank you for your valuable feedback.

Regarding “6.5) In Fig 1, legend: what is the operational definition of "generating performance"? Generating what? Neural reconstruction?””:

We have replaced “generating performance” with “reconstruction performance” in the revised manuscript. Thanks for your recommendation.

Q7: “In the analysis presented starting in line 449, the authors compare improvement gained for decoding various speed ranges by adding secondary (small PC) neurons to the KF decoder (Fig S11). Why is this done using the KF decoder, when earlier results suggest an ANN decoder is needed for accurate decoding from these small PC neurons? It makes sense to use the more accurate nonlinear ANN decoder to support the fundamental claim made here, that smaller variance PCs are involved in regulating precise control”

Because when the secondary signal is superimposed on the primary signal, the enhancement in KF performance is substantial. We wanted to explore in which aspect of the behavior the KF performance improvement is mainly reflected. In comparison, the improvement of ANN by the secondary signal is very small, rendering the exploration of the aforementioned questions inconsequential. Thank you for your valuable feedback.

Q8: “A key limitation of the VAE architecture is that it doesn't aggregate information over multiple time samples. This may be why the authors decided to use a very large bin size of 100ms and beyond that smooth the data with a moving average. This limitation should be clearly stated somewhere in contrast with methods that can aggregate information over time (e.g., TNDM, LFADS, PSID) ”

We have added this limitation in the Discussion in the revised manuscript. Thanks for your recommendation.

Q9: “Fig 5c and parts of the text explore the decoding when some neurons are dropped. These results should come with a reminder that dropping neurons from behaviorally relevant signals is not technically possible since the extraction of behaviorally relevant signals with d-VAE is a population level aggregation that requires the raw signal from all neurons as an input. This is also important to remind in some places in the text for example:

• Line 498: "...when one of the neurons is destroyed."

• Line 572: "In contrast, our results show that decoders maintain high performance on distilled signals even when many neurons drop out."”

We want to explore the robustness of real relevant signals in the face of neuron drop-out. The signals our model extracted are an approximation of the ground truth relevant signals and thus serve as a substitute for ground truth to study this problem. Thank you for your valuable feedback.

Q10: “Besides the confounded conclusions regarding the readout being linear (see comment 3 and items related to it in comment 5), the authors also don't adequately discuss prior works that suggest nonlinearity helps decoding of behavior from the motor cortex. Around line 594, a few works are discussed as support for the idea of a linear readout. This should be accompanied by a discussion of works that support a nonlinear encoding of behavior in the motor cortex, for example (Naufel et al. 2019; Glaser et al. 2020), some of which the authors cite elsewhere but don't discuss here.”

We have added this discussion in the revised manuscript. Thanks for your recommendation.

Q11: “Selection of hyperparameters is not clearly explained. Starting line 791, the authors give some explanation for one hyperparameter, but not others. How are the other hyperparameters determined? What is the search space for the grid search of each hyperparameter? Importantly, if hyperparameters are determined only based on the training data of each fold, why is only one value given for the hyperparameter selected in each dataset (line 814)? Did all 5 folds for each dataset happen to select exactly the same hyperparameter based on their 5 different training/validation data splits? That seems unlikely.”

We perform a grid search in {0.001, 0.01,0.1,1} for hyperparameter beta. And we found that 0.001 is the best for all datasets. As for the model parameters, such as hidden neuron numbers, this model capacity has reached saturation decoding performance and does not influence the results.

Regarding “Importantly, if hyperparameters are determined only based on the training data of each fold, why is only one value given for the hyperparameter selected in each dataset (line 814)? Did all 5 folds for each dataset happen to select exactly the same hyperparameter based on their 5 different training/validation data splits”: We selected the hyperparameter based on the average performance of 5 folds data on validation sets. The selected value denotes the one that yields the highest average performance across the 5 folds data.

Thank you for your valuable feedback.

Q12: “d-VAE itself should also be explained more clearly in the main text. Currently, only the high-level idea of the objective is explained. The explanation should be more precise and include the idea of encoding to latent state, explain the relation to pip-VAE, explain inputs and outputs, linearity/nonlinearity of various mappings, etc. Also see comment 1 above, where I suggest adding more details about other methods in the main text.”

Our primary objective is to delve into the encoding and decoding mechanisms using the separated relevant signals. Therefore, providing an excessive amount of model details could potentially distract from the main focus of the paper. In response to your suggestion, we have included a visual representation of d-VAE's structure, input, and output (see Fig. S1) in the revised manuscript, which offers a comprehensive and intuitive overview. Additionally, we have expanded on the details of d-VAE and other methods in the Methods section.

Thank you for your valuable feedback.

Q13: “In Fig 1f and g, shouldn't the performance plots be swapped? The current plots seem counterintuitive. If there is bias toward decoding (panel g), why is the irrelevant residual so good at decoding?”

The placement of the performance plots in Fig. 1f and 1g is accurate. When the model exhibits a bias toward decoding, it prioritizes extracting the most relevant features (latent variables) for decoding purposes. As a consequence, the model predominantly generates signals that are closely associated with these extracted features. This selective signal extraction and generation process may result in the exclusion of other potentially useful information, which will be left in the residuals. To illustrate this concept, consider the example of face recognition: if a model can accurately identify an individual using only the person's eyes (assuming these are the most useful features), other valuable information, such as details of the nose or mouth, will be left in the residuals, which could also be used to identify the individual.

Thank you for your valuable feedback.

Author response:

The following is the authors’ response to the previous reviews.

eLife Assessment

This neuroimaging and electrophysiology study in a small cohort of congenital cataract patients with sight recovery aims to characterize the effects of early visual deprivation on excitatory and inhibitory balance in visual cortex. While contrasting sight-recovery with visually intact controls suggested the existence of persistent alterations in Glx/GABA ratio and aperiodic EEG signals, it provided only incomplete evidence supporting claims about the effects of early deprivation itself. The reported data were considered valuable, given the rare study population. However, the small sample sizes, lack of a specific control cohort and multiple methodological limitations will likely restrict usefulness to scientists working in this particular subfield.

We thank the reviewing editors for their consideration and updated assessment of our manuscript after its first revision.

In order to assess the effects of early deprivation, we included an age-matched, normally sighted control group recruited from the same community, measured in the same scanner and laboratory. This study design is analogous to numerous studies in permanently congenitally blind humans, which typically recruited sighted controls, but hardly ever individuals with a different, e.g. late blindness history. In order to improve the specificity of our conclusions, we used a frontal cortex voxel in addition to a visual cortex voxel (MRS). Analogously, we separately analyzed occipital and frontal electrodes (EEG).

Moreover, we relate our findings in congenital cataract reversal individuals to findings in the literature on permanent congenital blindness. Note, there are, to the best of our knowledge, neither MRS nor resting-state EEG studies in individuals with permanent late blindness.

Our participants necessarily have nystagmus and low visual acuity due to their congenital deprivation phase, and the existence of nystagmus is a recruitment criterion to diagnose congenital cataracts.

It might be interesting for future studies to investigate individuals with transient late blindness. However, such a study would be ill-motivated had we not found differences between the most “extreme” of congenital visual deprivation conditions and normally sighted individuals (analogous to why earlier research on permanent blindness investigated permanent congenitally blind humans first, rather than permanently late blind humans, or both in the same study). Any result of these future work would need the reference to our study, and neither results in these additional groups would invalidate our findings.

Since all our congenital cataract reversal individuals by definition had visual impairments, we included an eyes closed condition, both in the MRS and EEG assessment. Any group effect during the eyes closed condition cannot be due to visual acuity deficits changing the bottom-up driven visual activation.

As we detail in response to review 3, our EEG analyses followed the standards in the field.

Public Reviews:

Reviewer #1 (Public review):

Summary

In this human neuroimaging and electrophysiology study, the authors aimed to characterise effects of a period of visual deprivation in the sensitive period on excitatory and inhibitory balance in the visual cortex. They attempted to do so by comparing neurochemistry conditions ('eyes open', 'eyes closed') and resting state, and visually evoked EEG activity between ten congenital cataract patients with recovered sight (CC), and ten age-matched control participants (SC) with normal sight.

First, they used magnetic resonance spectroscopy to measure in vivo neurochemistry from two locations, the primary location of interest in the visual cortex, and a control location in the frontal cortex. Such voxels are used to provide a control for the spatial specificity of any effects, because the single-voxel MRS method provides a single sampling location. Using MR-visible proxies of excitatory and inhibitory neurotransmission, Glx and GABA+ respectively, the authors report no group effects in GABA+ or Glx, no difference in the functional conditions 'eyes closed' and 'eyes open'. They found an effect of group in the ratio of Glx/GABA+ and no similar effect in the control voxel location. They then perform multiple exploratory correlations between MRS measures and visual acuity, and report a weak positive correlation between the 'eyes open' condition and visual acuity in CC participants.

The same participants then took part in an EEG experiment. The authors selected two electrodes placed in the visual cortex for analysis and report a group difference in an EEG index of neural activity, the aperiodic intercept, as well as the aperiodic slope, considered a proxy for cortical inhibition. Control electrodes in the frontal region did not present with the same pattern. They report an exploratory correlation between the aperiodic intercept and Glx in one out of three EEG conditions.

The authors report the difference in E/I ratio, and interpret the lower E/I ratio as representing an adaptation to visual deprivation, which would have initially caused a higher E/I ratio. Although intriguing, the strength of evidence in support of this view is not strong. Amongst the limitations are the low sample size, a critical control cohort that could provide evidence for higher E/I ratio in CC patients without recovered sight for example, and lower data quality in the control voxel. Nevertheless, the study provides a rare and valuable insight into experience-dependent plasticity in the human brain.

Strengths of study

How sensitive period experience shapes the developing brain is an enduring and important question in neuroscience. This question has been particularly difficult to investigate in humans. The authors recruited a small number of sight-recovered participants with bilateral congenital cataracts to investigate the effect of sensitive period deprivation on the balance of excitation and inhibition in the visual brain using measures of brain chemistry and brain electrophysiology. The research is novel, and the paper was interesting and well written.

Limitations

Low sample size. Ten for CC and ten for SC, and further two SC participants were rejected due to lack of frontal control voxel data. The sample size limits the statistical power of the dataset and increases the likelihood of effect inflation.

In the updated manuscript, the authors have provided justification for their sample size by pointing to prior studies and the inherent difficulties in recruiting individuals with bilateral congenital cataracts. Importantly, this highlights the value the study brings to the field while also acknowledging the need to replicate the effects in a larger cohort.

Lack of specific control cohort. The control cohort has normal vision. The control cohort is not specific enough to distinguish between people with sight loss due to different causes and patients with congenital cataracts with co-morbidities. Further data from a more specific populations, such as patients whose cataracts have not been removed, with developmental cataracts, or congenitally blind participants, would greatly improve the interpretability of the main finding. The lack of a more specific control cohort is a major caveat that limits a conclusive interpretation of the results.

In the updated version, the authors have indicated that future studies can pursue comparisons between congenital cataract participants and cohorts with later sight loss.

MRS data quality differences. Data quality in the control voxel appears worse than in the visual cortex voxel. The frontal cortex MRS spectrum shows far broader linewidth than the visual cortex (Supplementary Figures). Compared to the visual voxel, the frontal cortex voxel has less defined Glx and GABA+ peaks; lower GABA+ and Glx concentrations, lower NAA SNR values; lower NAA concentrations. If the data quality is a lot worse in the FC, then small effects may not be detectable.

In the updated version, the authors have added more information that informs the reader of the MRS quality differences between voxel locations. This increases the transparency of their reporting and enhances the assessment of the results.

Because of the direction of the difference in E/I, the authors interpret their findings as representing signatures of sight improvement after surgery without further evidence, either within the study or from the literature. However, the literature suggests that plasticity and visual deprivation drives the E/I index up rather than down. Decreasing GABA+ is thought to facilitate experience dependent remodelling. What evidence is there that cortical inhibition increases in response to a visual cortex that is over-sensitised to due congenital cataracts? Without further experimental or literature support this interpretation remains very speculative.

The updated manuscript contains key reference from non-human work to justify their interpretation.

Heterogeneity in patient group. Congenital cataract (CC) patients experienced a variety of duration of visual impairment and were of different ages. They presented with co-morbidities (absorbed lens, strabismus, nystagmus). Strabismus has been associated with abnormalities in GABAergic inhibition in the visual cortex. The possible interactions with residual vision and confounds of co-morbidities are not experimentally controlled for in the correlations, and not discussed.

The updated document has addressed this caveat.

Multiple exploratory correlations were performed to relate MRS measures to visual acuity (shown in Supplementary Materials), and only specific ones shown in the main document. The authors describe the analysis as exploratory in the 'Methods' section. Furthermore, the correlation between visual acuity and E/I metric is weak, not corrected for multiple comparisons. The results should be presented as preliminary, as no strong conclusions can be made from them. They can provide a hypothesis to test in a future study.

This has now been done throughout the document and increases the transparency of the reporting.

P.16 Given the correlation of the aperiodic intercept with age ("Age negatively correlated with the aperiodic intercept across CC and SC individuals, that is, a flattening of the intercept was observed with age"), age needs to be controlled for in the correlation between neurochemistry and the aperiodic intercept. Glx has also been shown to negatively correlates with age.

This caveat has been addressed in the revised manuscript.

Multiple exploratory correlations were performed to relate MRS to EEG measures (shown in Supplementary Materials), and only specific ones shown in the main document. Given the multiple measures from the MRS, the correlations with the EEG measures were exploratory, as stated in the text, p.16, and in Fig.4. yet the introduction said that there was a prior hypothesis "We further hypothesized that neurotransmitter changes would relate to changes in the slope and intercept of the EEG aperiodic activity in the same subjects." It would be great if the text could be revised for consistency and the analysis described as exploratory.

This has been done throughout the document and increases the transparency of the reporting.

The analysis for the EEG needs to take more advantage of the available data. As far as I understand, only two electrodes were used, yet far more were available as seen in their previous study (Ossandon et al., 2023). The spatial specificity is not established. The authors could use the frontal cortex electrode (FP1, FP2) signals as a control for spatial specificity in the group effects, or even better, all available electrodes and correct for multiple comparisons. Furthermore, they could use the aperiodic intercept vs Glx in SC to evaluate the specificity of the correlation to CC.

This caveat has been addressed. The authors have added frontal electrodes to their analysis, providing an essential regional control for the visual cortex location.

Comments on the latest version:

The authors have made reasonable adjustments to their manuscript that addressed most of my comments by adding further justification for their methodology, essential literature support, pointing out exploratory analyses, limitations and adding key control analyses. Their revised manuscript has overall improved, providing valuable information, though the evidence that supports their claims is still incomplete.

We thank the reviewer for suggesting ways to improve our manuscript and carefully reassessing our revised manuscript.

Reviewer #2 (Public review):

Summary:

The study examined 10 congenitally blind patients who recovered vision through the surgical removal of bilateral dense cataracts, measuring neural activity and neuro chemical profiles from the visual cortex. The declared aim is to test whether restoring visual function after years of complete blindness impacts excitation/inhibition balance in the visual cortex.

Strengths:

The findings are undoubtedly useful for the community, as they contribute towards characterising the many ways in which this special population differs from normally sighted individuals. The combination of MRS and EEG measures is a promising strategy to estimate a fundamental physiological parameter - the balance between excitation and inhibition in the visual cortex, which animal studies show to be heavily dependent upon early visual experience. Thus, the reported results pave the way for further studies, which may use a similar approach to evaluate more patients and control groups.

Weaknesses:

The main methodological limitation is the lack of an appropriate comparison group or condition to delineate the effect of sight recovery (as opposed to the effect of congenital blindness). Few previous studies suggested that Excitation/Inhibition ratio in the visual cortex is increased in congenitally blind patients; the present study reports that E/I ratio decreases instead. The authors claim that this implies a change of E/I ratio following sight recovery. However, supporting this claim would require showing a shift of E/I after vs. before the sight-recovery surgery, or at least it would require comparing patients who did and did not undergo the sight-recovery surgery (as common in the field).

We thank the reviewer for suggesting ways to improve our manuscript and carefully reassessing our revised manuscript.

Since we have not been able to acquire longitudinal data with the experimental design of the present study in congenital cataract reversal individuals, we compared the MRS and EEG results of congenital cataract reversal individuals  to published work in congenitally permanent blind individuals. We consider this as a resource saving approach. We think that the results of our cross-sectional study now justify the costs and enormous efforts (and time for the patients who often have to travel long distances) associated with longitudinal studies in this rare population.

There are also more technical limitations related to the correlation analyses, which are partly acknowledged in the manuscript. A bland correlation between GLX/GABA and the visual impairment is reported, but this is specific to the patients group (N=10) and would not hold across groups (the correlation is positive, predicting the lowest GLX/GABA ratio values for the sighted controls - opposite of what is found). There is also a strong correlation between GLX concentrations and the EEG power at the lowest temporal frequencies. Although this relation is intriguing, it only holds for a very specific combination of parameters (of the many tested): only with eyes open, only in the patients group.

Given the exploratory nature of the correlations, we do not base the majority of our conclusions on this analysis. There are no doubts that the reported correlations need replication; however, replication is only possible after a first report. Thus, we hope to motivate corresponding analyses in further studies.

It has to be noted that in the present study significance testing for correlations were corrected for multiple comparisons, and that some findings replicate earlier reports (e.g. effects on EEG aperiodic slope, alpha power, and correlations with chronological age).

Conclusions:

The main claim of the study is that sight recovery impacts the excitation/inhibition balance in the visual cortex, estimated with MRS or through indirect EEG indices. However, due to the weaknesses outlined above, the study cannot distinguish the effects of sight recovery from those of visual deprivation. Moreover, many aspects of the results are interesting but their validation and interpretation require additional experimental work.

We interpret the group differences between individuals tested years after congenital visual deprivation and normally sighted individuals as supportive of the E/I ratio being impacted by congenital visual deprivation. In the absence of a sensitive period for the development of an E/I ratio, individuals with a transient phase of congenital blindness might have developed a visual system indistinguishable  from normally sighted individuals. As we demonstrate, this is not so. Comparing the results of congenitally blind humans with those of congenitally permanently blind humans (from previous studies) allowed us to identify changes of E/I ratio, which add to those found for congenital blindness.  

We thank the reviewer for the helpful comments and suggestions related to the first submission and first revision of our manuscript. We are keen to translate some of them into future studies.

Reviewer #3 (Public review):

This manuscript examines the impact of congenital visual deprivation on the excitatory/inhibitory (E/I) ratio in the visual cortex using Magnetic Resonance Spectroscopy (MRS) and electroencephalography (EEG) in individuals whose sight was restored. Ten individuals with reversed congenital cataracts were compared to age-matched, normally sighted controls, assessing the cortical E/I balance and its interrelationship and to visual acuity. The study reveals that the Glx/GABA ratio in the visual cortex and the intercept and aperiodic signal are significantly altered in those with a history of early visual deprivation, suggesting persistent neurophysiological changes despite visual restoration.

First of all, I would like to disclose that I am not an expert in congenital visual deprivation, nor in MRS. My expertise is in EEG (particularly in the decomposition of periodic and aperiodic activity) and statistical methods.

Although the authors addressed some of the concerns of the previous version, major concerns and flaws remain in terms of methodological and statistical approaches along with the (over)interpretation of the results. Specific concerns include:

(1 3.1) Response to Variability in Visual Deprivation<br /> Rather than listing the advantages and disadvantages of visual deprivation, I recommend providing at least a descriptive analysis of how the duration of visual deprivation influenced the measures of interest. This would enhance the depth and relevance of the discussion.

Although Review 2 and Review 3 (see below) pointed out problems in interpreting multiple correlational analyses in small samples, we addressed this request by reporting such correlations between visual deprivation history and measured EEG/MRS outcomes.

Calculating the correlation between duration of visual deprivation and behavioral or brain measures is, in fact, a common suggestion. The existence of sensitive periods, which are typically assumed to not follow a linear gradual decline of neuroplasticity, does not necessary allow predicting a correlation with duration of blindness. Daphne Maurer has additionally worked on the concept of “sleeper effects” (Maurer et al., 2007), that is, effects on the brain and behavior by early deprivation which are observed only later in life when the function/neural circuits matures.

In accordance with this reasoning, we did not observe a significant correlation between duration of visual deprivation and any of our dependent variables.

(2 3.2) Small Sample Size<br /> The issue of small sample size remains problematic. The justification that previous studies employed similar sample sizes does not adequately address the limitation in the current study. I strongly suggest that the correlation analyses should not feature prominently in the main manuscript or the abstract, especially if the discussion does not substantially rely on these correlations. Please also revisit the recommendations made in the section on statistical concerns.

In the revised manuscript, we explicitly mention that our sample size is not atypical for the special group investigated, but that a replication of our results in larger samples would foster their impact. We only explicitly mention correlations that survived stringent testing for multiple comparisons in the main manuscript.

Given the exploratory nature of the correlations, we have not based the majority of our claims on this analysis.

(3 3.3) Statistical Concerns<br /> While I appreciate the effort of conducting an independent statistical check, it merely validates whether the reported statistical parameters, degrees of freedom (df), and p-values are consistent. However, this does not address the appropriateness of the chosen statistical methods.

We did not intend for the statcheck report to justify the methods used for statistics, which we have done in a separate section with normality and homogeneity testing (Supplementary Material S9), and references to it in the descriptions of the statistical analyses (Methods, Page 13, Lines 326-329 and Page 15, Lines 400-402).

Several points require clarification or improvement:<br /> (4) Correlation Methods: The manuscript does not specify whether the reported correlation analyses are based on Pearson or Spearman correlation.

The depicted correlations are Pearson correlations. We will add this information to the Methods.

(5) Confidence Intervals: Include confidence intervals for correlations to represent the uncertainty associated with these estimates.

We have added the confidence intervals for all measured correlations to the second revision of our manuscript.

(6) Permutation Statistics: Given the small sample size, I recommend using permutation statistics, as these are exact tests and more appropriate for small datasets.

Our study focuses on a rare population, with a sample size limited by the availability of participants. Our findings provide exploratory insights rather than make strong inferential claims. To this end, we have ensured that our analysis adheres to key statistical assumptions (Shapiro-Wilk as well as Levene’s tests, Supplementary Material S9), and reported our findings with effect sizes, appropriate caution and context.

(7) Adjusted P-Values: Ensure that reported Bonferroni corrected p-values (e.g., p > 0.999) are clearly labeled as adjusted p-values where applicable.

In the revised manuscript, we have changed Figure 4 to say ‘adjusted p,’  which we indeed reported.

(8) Figure 2C

Figure 2C still lacks crucial information that the correlation between Glx/GABA ratio and visual acuity was computed solely in the control group (as described in the rebuttal letter). Why was this analysis restricted to the control group? Please provide a rationale.

Figure 2C depicts the correlation between Glx/GABA+ ratio and visual acuity in the congenital cataract reversal group, not the control group. This is mentioned in the Figure 2 legend, as well as in the main text where the figure is referred to (Page 18, Line 475).

The correlation analyses between visual acuity and MRS/EEG measures were only performed in the congenital cataract reversal group since the sighed control group comprised of individuals with vision in the normal range; thus this analyses would not make sense. Table 1 with the individual visual acuities for all participants, including the normally sighted controls, shows the low variance in the latter group.  

For variables in which no apiori group differences in variance were predicted, we performed the correlation analyses across groups (see Supplementary Material S12, S15).

We have now highlighted these motivations more clearly in the Methods of the revised manuscript (Page 16, Lines 405-410).

(9 3.4) Interpretation of Aperiodic Signal

Relying on previous studies to interpret the aperiodic slope as a proxy for excitation/inhibition (E/I) does not make the interpretation more robust.

How to interpret aperiodic EEG activity has been subject of extensive investigation. We cite studies which provide evidence from multiple species (monkeys, humans) and measurements (EEG, MEG, ECoG), including studies which pharmacologically manipulated E/I balance.

Whether our findings are robust, in fact, requires a replication study. Importantly, we analyzed the intercept of the aperiodic activity fit as well, and discuss results related to the intercept.

Quote:

“(3.4) Interpretation of aperiodic signal:

- Several recent papers demonstrated that the aperiodic signal measured in EEG or ECoG is related to various important aspects such as age, skull thickness, electrode impedance, as well as cognition. Thus, currently, very little is known about the underlying effects which influence the aperiodic intercept and slope. The entire interpretation of the aperiodic slope as a proxy for E/I is based on a computational model and simulation (as described in the Gao et al. paper).

Apart from the modeling work from Gao et al., multiple papers which have also been cited which used ECoG, EEG and MEG and showed concomitant changes in aperiodic activity with pharmacological manipulation of the E/I ratio (Colombo et al., 2019; Molina et al., 2020; Muthukumaraswamy & Liley, 2018). Further, several prior studies have interpreted changes in the aperiodic slope as reflective of changes in the E/I ratio, including studies of developmental groups (Favaro et al., 2023; Hill et al., 2022; McSweeney et al., 2023; Schaworonkow & Voytek, 2021) as well as patient groups (Molina et al., 2020; Ostlund et al., 2021).

- The authors further wrote: We used the slope of the aperiodic (1/f) component of the EEG spectrum as an estimate of E/I ratio (Gao et al., 2017; Medel et al., 2020; Muthukumaraswamy & Liley, 2018). This is a highly speculative interpretation with very little empirical evidence. These papers were conducted with ECoG data (mostly in animals) and mostly under anesthesia. Thus, these studies only allow an indirect interpretation by what the 1/f slope in EEG measurements is actually influenced.

Note that Muthukumaraswamy et al. (2018) used different types of pharmacological manipulations and analyzed periodic and aperiodic MEG activity in humans, in addition to monkey ECoG (Muthukumaraswamy & Liley, 2018). Further, Medel et al. (now published as Medel et al., 2023) compared EEG activity in addition to ECoG data after propofol administration. The interpretation of our results are in line with a number of recent studies in developing (Hill et al., 2022; Schaworonkow & Voytek, 2021) and special populations using EEG. As mentioned above, several prior studies have used the slope of the 1/f component/aperiodic activity as an indirect measure of the E/I ratio (Favaro et al., 2023; Hill et al., 2022; McSweeney et al., 2023; Molina et al., 2020; Ostlund et al., 2021; Schaworonkow & Voytek, 2021), including studies using scalp-recorded EEG from humans.

In the introduction of the revised manuscript, we have made more explicit that this metric is indirect (Page 3, Line 91), (additionally see Discussion, Page 24, Lines 644-645, Page 25, Lines 650-657).

While a full understanding of aperiodic activity needs to be provided, some convergent ideas have emerged. We think that our results contribute to this enterprise, since our study is, to the best of our knowledge, the first which assessed MRS measured neurotransmitter levels and EEG aperiodic activity. “

(10) Additionally, the authors state:

"We cannot think of how any of the exploratory correlations between neurophysiological measures and MRS measures could be accounted for by a difference e.g. in skull thickness."

(11) This could be addressed directly by including skull thickness as a covariate or visualizing it in scatterplots, for instance, by representing skull thickness as the size of the dots.

We are not aware of any study that would justify such an analysis.

Our analyses were based on previous findings in the literature.

Since to the best of our knowledge, no evidence exists that congenital cataracts go together with changes in skull thickness, and that skull thickness might selectively modulate visual cortex Glx/GABA+ but not NAA measures, we decided against following this suggestion.

Notably, the neurotransmitter concentration reported here is after tissue segmentation of the voxel region. The tissue fraction was shown to not differ between groups in the MRS voxels (Supplementary Material S4). The EEG electrode impedance was lowered to <10 kOhm in every participant (Methods, Page 13, Line 344), and preparation was identical across groups.

(12 3.5) Problems with EEG Preprocessing and Analysis

Downsampling: The decision to downsample the data to 60 Hz "to match the stimulation rate" is problematic. This choice conflates subsequent spectral analyses due to aliasing issues, as explained by the Nyquist theorem. While the authors cite prior studies (Schwenk et al., 2020; VanRullen & MacDonald, 2012) to justify this decision, these studies focused on alpha (8-12 Hz), where aliasing is less of a concern compared of analyzing aperiodic signal. Furthermore, in contrast, the current study analyzes the frequency range from 1-20 Hz, which is too narrow for interpreting the aperiodic signal as E/I. Typically, this analysis should include higher frequencies, spanning at least 1-30 Hz or even 1-45 Hz (not 20-40 Hz).

As previously mentied in the Methods (Page 15 Line 376) and the previous response, the pop_resample function used by EEGLAB applies an anti-aliasing filter, at half the resampling frequency (as per the Nyquist theorem

https://eeglab.org/tutorials/05_Preprocess/resampling.html). The upper cut off of the low pass filter set by EEGlab prior to down sampling (30 Hz) is still far above the frequency of interest in the current study  (1-20 Hz), thus allowing us to derive valid results.

Quote:

“- The authors downsampled the data to 60Hz to "to match the stimulation rate". What is the intention of this? Because the subsequent spectral analyses are conflated by this choice (see Nyquist theorem).

This data were collected as part of a study designed to evoke alpha activity with visual white-noise, which ranged in luminance with equal power at all frequencies from 1-60 Hz, restricted by the refresh rate of the monitor on which stimuli were presented (Pant et al., 2023). This paradigm and method was developed by VanRullen and colleagues (Schwenk et al., 2020; Vanrullen & MacDonald, 2012), wherein the analysis requires the same sampling rate between the presented frequencies and the EEG data. The downsampling function used here automatically applies an anti-aliasing filter (EEGLAB 2019) .”

Moreover, the resting-state data were not resampled to 60 Hz. We have made this clearer in the Methods of the second revision (Page 15, Line 367).

Our consistent results of group differences across all three EEG conditions, thus, exclude any possibility that they were driven by aliasing artifacts.

The expected effects of this anti-aliasing filter can be seen in the attached Author response image 1, showing an example participant’s spectrum in the 1-30 Hz range (as opposed to the 1-20 Hz plotted in the manuscript), clearly showing a 30-40 dB drop at 30 Hz. Any aliasing due to, for example, remaining line noise, would additionally be visible in this figure (as well as Figure 3) as a peak.

Author response image 1.

Power spectral density of one congenital cataract-reversal (CC) participant in the visual stimulation condition across all channels. The reduced power at 30 Hz shows the effects of the anti-aliasing filter applied by EEGLAB’s pop_resample function.

As we stated in the manuscript, and in previous reviews, so far there has been no consensus on the exact range of measuring aperiodic activity. We made a principled decision based on the literature (showing a knee in aperiodic fits of this dataset at 20 Hz) (Medel et al., 2023; Ossandón et al., 2023), data quality (possible contamination by line noise at higher frequencies) and the purpose of the visual stimulation experiment (to look at the lower frequency range by stimulating up to 60 Hz, thereby limiting us to quantifying below 30 Hz), that 1-20 Hz would be the fit range in this dataset.

Quote:

“(3) What's the underlying idea of analyzing two separate aperiodic slopes (20-40Hz and 1-19Hz). This is very unusual to compute the slope between 20-40 Hz, where the SNR is rather low.

"Ossandón et al. (2023), however, observed that in addition to the flatter slope of the aperiodic power spectrum in the high frequency range (20-40 Hz), the slope of the low frequency range (1-19 Hz) was steeper in both, congenital cataract-reversal individuals, as well as in permanently congenitally blind humans."

The present manuscript computed the slope between 1-20 Hz. Ossandón et al. as well as Medel et al. (2023) found a “knee” of the 1/f distribution at 20 Hz and describe further the motivations for computing both slope ranges. For example, Ossandón et al. used a data driven approach and compared single vs. dual fits and found that the latter fitted the data better. Additionally, they found the best fit if a knee at 20 Hz was used. We would like to point out that no standard range exists for the fitting of the 1/f component across the literature and, in fact, very different ranges have been used (Gao et al., 2017; Medel et al., 2023; Muthukumaraswamy & Liley, 2018). “

(13) Baseline Removal: Subtracting the mean activity across an epoch as a baseline removal step is inappropriate for resting-state EEG data. This preprocessing step undermines the validity of the analysis. The EEG dataset has fundamental flaws, many of which were pointed out in the previous review round but remain unaddressed. In its current form, the manuscript falls short of standards for robust EEG analysis. If I were reviewing for another journal, I would recommend rejection based on these flaws.

The baseline removal step from each epoch serves to remove the DC component of the recording and detrend the data. This is a standard preprocessing step (included as an option in preprocessing pipelines recommended by the EEGLAB toolbox, FieldTrip toolbox and MNE toolbox), additionally necessary to improve the efficacy of ICA decomposition (Groppe et al., 2009).

In the previous review round, a clarification of the baseline timing was requested, which we added. Beyond this request, there was no mention of the appropriateness of the baseline removal and/or a request to provide reasons for why it might not undermine the validity of the analysis.

Quote:

“- "Subsequently, baseline removal was conducted by subtracting the mean activity across the length of an epoch from every data point." The actual baseline time segment should be specified.

The time segment was the length of the epoch, that is, 1 second for the resting state conditions and 6.25 seconds for the visual stimulation conditions. This has been explicitly stated in the revised manuscript (Page 13, Line 354).”

Prior work in the time (not frequency) domain on event-related potential (ERP) analysis has suggested that the baselining step might cause spurious effects (Delorme, 2023) (although see (Tanner et al., 2016)). We did not perform ERP analysis at any stage. One recent study suggests spurious group differences in the 1/f signal might be driven by an inappropriate dB division baselining method (Gyurkovics et al., 2021), which we did not perform.

Any effect of our baselining procedure on the FFT spectrum would be below the 1 Hz range, which we did not analyze.  

Each of the preprocessing steps in the manuscript match pipelines described and published in extensive prior work. We document how multiple aspects of our EEG results replicate prior findings (Supplementary Material S15, S18, S19), reports of other experimenters, groups and locations, validating that our results are robust.

We therefore reject the claim of methodological flaws in our EEG analyses in the strongest possible terms.

Quote:

“(3.5) Problems with EEG preprocessing and analysis:

- It seems that the authors did not identify bad channels nor address the line noise issue (even a problem if a low pass filter of below-the-line noise was applied).

As pointed out in the methods and Figure 1, we only analyzed data from two occipital channels, O1 and O2 neither of which were rejected for any participant. Channel rejection was performed for the larger dataset, published elsewhere (Ossandón et al., 2023; Pant et al., 2023). As control sites we added the frontal channels FP1 and Fp2 (see Supplementary Material S14)

Neither Ossandón et al. (2023) nor Pant et al. (2023) considered frequency ranges above 40 Hz to avoid any possible contamination with line noise. Here, we focused on activity between 0 and 20 Hz, definitely excluding line noise contaminations (Methods, Page 14, Lines 365-367). The low pass filter (FIR, 1-45 Hz) guaranteed that any spill-over effects of line noise would be restricted to frequencies just below the upper cutoff frequency.

Additionally, a prior version of the analysis used spectrum interpolation to remove line noise; the group differences remained stable (Ossandón et al., 2023). We have reported this analysis in the revised manuscript (Page 14, Lines 364-357).

Further, both groups were measured in the same lab, making line noise (~ 50 Hz) as an account for the observed group effects in the 1-20 Hz frequency range highly unlikely. Finally, any of the exploratory MRS-EEG correlations would be hard to explain if the EEG parameters would be contaminated with line noise.

- What was the percentage of segments that needed to be rejected due to the 120μV criteria? This should be reported specifically for EO & EC and controls and patients.

The mean percentage of 1 second segments rejected for each resting state condition and the percentage of 6.25 long segments rejected in each group for the visual stimulation condition have been added to the revised manuscript (Supplementary Material S10), and referred to in the Methods on Page 14, Lines 372-373).

- The authors downsampled the data to 60Hz to "to match the stimulation rate". What is the intention of this? Because the subsequent spectral analyses are conflated by this choice (see Nyquist theorem).

This data were collected as part of a study designed to evoke alpha activity with visual white-noise, which changed in luminance with equal power at all frequencies from 1-60 Hz, restricted by the refresh rate of the monitor on which stimuli were presented (Pant et al., 2023). This paradigm and method was developed by VanRullen and colleagues (Schwenk et al., 2020; VanRullen & MacDonald, 2012), wherein the analysis requires the same sampling rate between the presented frequencies and the EEG data. The downsampling function used here automatically applies an anti-aliasing filter (EEGLAB 2019) .

- "Subsequently, baseline removal was conducted by subtracting the mean activity across the length of an epoch from every data point." The actual baseline time segment should be specified.

The time segment was the length of the epoch, that is, 1 second for the resting state conditions and 6.25 seconds for the visual stimulation conditions. This has now been explicitly stated in the revised manuscript (Page 14, Lines 379-380).

- "We excluded the alpha range (8-14 Hz) for this fit to avoid biasing the results due to documented differences in alpha activity between CC and SC individuals (Bottari et al., 2016; Ossandón et al., 2023; Pant et al., 2023)." This does not really make sense, as the FOOOF algorithm first fits the 1/f slope, for which the alpha activity is not relevant.

We did not use the FOOOF algorithm/toolbox in this manuscript. As stated in the Methods, we used a 1/f fit to the 1-20 Hz spectrum in the log-log space, and subtracted this fit from the original spectrum to obtain the corrected spectrum. Given the pronounced difference in alpha power between groups (Bottari et al., 2016; Ossandón et al., 2023; Pant et al., 2023), we were concerned it might drive differences in the exponent values. Our analysis pipeline had been adapted from previous publications of our group and other labs (Ossandón et al., 2023; Voytek et al., 2015; Waschke et al., 2017).

We have conducted the analysis with and without the exclusion of the alpha range, as well as using the FOOOF toolbox both in the 1-20 Hz and 20-40 Hz ranges (Ossandón et al., 2023). The findings of a steeper slope in the 1-20 Hz range as well as lower alpha power in CC vs SC individuals remained stable. In Ossandón et al., the comparison between the piecewise fits and FOOOF fits led the authors to use the former, as it outperformed the FOOOF algorithm for their data.

- The model fits of the 1/f fitting for EO, EC, and both participant groups should be reported.

In Figure 3 of the manuscript, we depicted the mean spectra and 1/f fits for each group.

In the revised manuscript, we added the fit quality metrics (average R² values > 0.91 for each group and condition) (Methods Page 15, Lines 395-396; Supplementary Material S11) and additionally show individual subjects’ fits (Supplementary Material S11). “

(14) The authors mention:

"The EEG data sets reported here were part of data published earlier (Ossandón et al., 2023; Pant et al., 2023)." Thus, the statement "The group differences for the EEG assessments corresponded to those of a larger sample of CC individuals (n=38) " is a circular argument and should be avoided."

The authors addressed this comment and adjusted the statement. However, I do not understand, why not the full sample published earlier (Ossandón et al., 2023) was used in the current study?

The recording of EEG resting state data stated in 2013, while MRS testing could only be set up by the second half of 2019. Moreover, not all subjects who qualify for EEG recording qualify for being scanned (e.g. due to MRI safety, claustrophobia)

References

Bottari, D., Troje, N. F., Ley, P., Hense, M., Kekunnaya, R., & Röder, B. (2016). Sight restoration after congenital blindness does not reinstate alpha oscillatory activity in humans. Scientific Reports. https://doi.org/10.1038/srep24683

Colombo, M. A., Napolitani, M., Boly, M., Gosseries, O., Casarotto, S., Rosanova, M., Brichant, J. F., Boveroux, P., Rex, S., Laureys, S., Massimini, M., Chieregato, A., & Sarasso, S. (2019). The spectral exponent of the resting EEG indexes the presence of consciousness during unresponsiveness induced by propofol, xenon, and ketamine. NeuroImage, 189(September 2018), 631–644. https://doi.org/10.1016/j.neuroimage.2019.01.024

Delorme, A. (2023). EEG is better left alone. Scientific Reports, 13(1), 2372. https://doi.org/10.1038/s41598-023-27528-0

Favaro, J., Colombo, M. A., Mikulan, E., Sartori, S., Nosadini, M., Pelizza, M. F., Rosanova, M., Sarasso, S., Massimini, M., & Toldo, I. (2023). The maturation of aperiodic EEG activity across development reveals a progressive differentiation of wakefulness from sleep. NeuroImage, 277. https://doi.org/10.1016/J.NEUROIMAGE.2023.120264

Gao, R., Peterson, E. J., & Voytek, B. (2017). Inferring synaptic excitation/inhibition balance from field potentials. NeuroImage, 158(March), 70–78. https://doi.org/10.1016/j.neuroimage.2017.06.078

Groppe, D. M., Makeig, S., & Kutas, M. (2009). Identifying reliable independent components via split-half comparisons. NeuroImage, 45(4), 1199–1211. https://doi.org/10.1016/j.neuroimage.2008.12.038

Gyurkovics, M., Clements, G. M., Low, K. A., Fabiani, M., & Gratton, G. (2021). The impact of 1/f activity and baseline correction on the results and interpretation of time-frequency analyses of EEG/MEG data: A cautionary tale. NeuroImage, 237. https://doi.org/10.1016/j.neuroimage.2021.118192

Hill, A. T., Clark, G. M., Bigelow, F. J., Lum, J. A. G., & Enticott, P. G. (2022). Periodic and aperiodic neural activity displays age-dependent changes across early-to-middle childhood. Developmental Cognitive Neuroscience, 54, 101076. https://doi.org/10.1016/J.DCN.2022.101076

Maurer, D., Mondloch, C. J., & Lewis, T. L. (2007). Sleeper effects. In Developmental Science. https://doi.org/10.1111/j.1467-7687.2007.00562.x

McSweeney, M., Morales, S., Valadez, E. A., Buzzell, G. A., Yoder, L., Fifer, W. P., Pini, N., Shuffrey, L. C., Elliott, A. J., Isler, J. R., & Fox, N. A. (2023). Age-related trends in aperiodic EEG activity and alpha oscillations during early- to middle-childhood. NeuroImage, 269, 119925. https://doi.org/10.1016/j.neuroimage.2023.119925

Medel, V., Irani, M., Crossley, N., Ossandón, T., & Boncompte, G. (2023). Complexity and 1/f slope jointly reflect brain states. Scientific Reports, 13(1), 21700. https://doi.org/10.1038/s41598-023-47316-0

Molina, J. L., Voytek, B., Thomas, M. L., Joshi, Y. B., Bhakta, S. G., Talledo, J. A., Swerdlow, N. R., & Light, G. A. (2020). Memantine Effects on Electroencephalographic Measures of Putative Excitatory/Inhibitory Balance in Schizophrenia. Biological Psychiatry: Cognitive Neuroscience and Neuroimaging, 5(6), 562–568. https://doi.org/10.1016/j.bpsc.2020.02.004

Muthukumaraswamy, S. D., & Liley, D. T. (2018). 1/F electrophysiological spectra in resting and drug-induced states can be explained by the dynamics of multiple oscillatory relaxation processes. NeuroImage, 179(November 2017), 582–595. https://doi.org/10.1016/j.neuroimage.2018.06.068

Ossandón, J. P., Stange, L., Gudi-Mindermann, H., Rimmele, J. M., Sourav, S., Bottari, D., Kekunnaya, R., & Röder, B. (2023). The development of oscillatory and aperiodic resting state activity is linked to a sensitive period in humans. NeuroImage, 275, 120171. https://doi.org/10.1016/J.NEUROIMAGE.2023.120171

Ostlund, B. D., Alperin, B. R., Drew, T., & Karalunas, S. L. (2021). Behavioral and cognitive correlates of the aperiodic (1/f-like) exponent of the EEG power spectrum in adolescents with and without ADHD. Developmental Cognitive Neuroscience, 48, 100931. https://doi.org/10.1016/j.dcn.2021.100931

Pant, R., Ossandón, J., Stange, L., Shareef, I., Kekunnaya, R., & Röder, B. (2023). Stimulus-evoked and resting-state alpha oscillations show a linked dependence on patterned visual experience for development. NeuroImage: Clinical, 103375. https://doi.org/10.1016/J.NICL.2023.103375

Schaworonkow, N., & Voytek, B. (2021). Longitudinal changes in aperiodic and periodic activity in electrophysiological recordings in the first seven months of life. Developmental Cognitive Neuroscience, 47. https://doi.org/10.1016/j.dcn.2020.100895

Schwenk, J. C. B., VanRullen, R., & Bremmer, F. (2020). Dynamics of Visual Perceptual Echoes Following Short-Term Visual Deprivation. Cerebral Cortex Communications, 1(1). https://doi.org/10.1093/TEXCOM/TGAA012

Tanner, D., Norton, J. J. S., Morgan-Short, K., & Luck, S. J. (2016). On high-pass filter artifacts (they’re real) and baseline correction (it’s a good idea) in ERP/ERMF analysis. Journal of Neuroscience Methods, 266, 166–170. https://doi.org/10.1016/j.jneumeth.2016.01.002

Vanrullen, R., & MacDonald, J. S. P. (2012). Perceptual echoes at 10 Hz in the human brain. Current Biology. https://doi.org/10.1016/j.cub.2012.03.050

Voytek, B., Kramer, M. A., Case, J., Lepage, K. Q., Tempesta, Z. R., Knight, R. T., & Gazzaley, A. (2015). Age-related changes in 1/f neural electrophysiological noise. Journal of Neuroscience, 35(38). https://doi.org/10.1523/JNEUROSCI.2332-14.2015

Waschke, L., Wöstmann, M., & Obleser, J. (2017). States and traits of neural irregularity in the age-varying human brain. Scientific Reports 2017 7:1, 7(1), 1–12. https://doi.org/10.1038/s41598-017-17766-4

Author response:

The following is the authors’ response to the previous reviews

Public Reviews:

Reviewer #1 (Public review):

(1) Authors' experimental designs have some caveats to definitely support their claims. Authors claimed that aged LT-HSCs have no myeloid-biased clone expansion using transplantation assays. In these experiments, authors used 10 HSCs and young mice as recipients. Given the huge expansion of old HSC by number and known heterogeneity in immunophenotypically defined HSC populations, it is questionable how 10 out of so many old HSCs (an average of 300,000 up to 500,000 cells per mouse; Mitchell et al., Nature Cell Biology, 2023) can faithfully represent old HSC population. The Hoxb5+ old HSC primary and secondary recipient mice data (Fig. 2C and D) support this concern. In addition, they only used young recipients. Considering the importance of inflammatory aged niche in the myeloid-biased lineage output, transplanting young vs old LT-HSCs into aged mice will complete the whole picture. 

We sincerely appreciate your insightful comment regarding the existence of approximately 500,000 HSCs per mouse in older mice. To address this, we have conducted a statistical analysis to determine the appropriate sample size needed to estimate the characteristics of a population of 500,000 cells with a 95% confidence level and a ±5% margin of error. This calculation was performed using the finite population correction applied to Cochran’s formula.

For our calculations, we used a proportion of 50% (p = 0.5), as it has been reported that approximately 50% of HSCs are myeloid-biased1,2. The formula used is as follows:

N \= 500,000 (total population size)

Z = 1.96 (Z-score for a 95% confidence level)

p = 0.5 (expected proportion)

e \= 0.05 (margin of error)

Applying this formula, we determined that the required sample size is approximately 384 cells. This sample size ensures that the observed proportion in the sample will reflect the characteristics of the entire population. In our study, we have conducted functional experiments across Figures 2, 3, 5, 6, S3, and S6, with a total sample size of n = 126, which corresponds to over 1260 cells. While it would be ideal to analyze all 500,000 cells, this would necessitate the use of 50,000 recipient mice, which is not feasible. We believe that the number of cells analyzed is reasonable from a statistical standpoint. 

References

(1) Dykstra, Brad et al. “Clonal analysis reveals multiple functional defects of aged murine hematopoietic stem cells.” The Journal of experimental medicine vol. 208,13 (2011): 2691-703. doi:10.1084/jem.20111490

(2) Beerman, Isabel et al. “Functionally distinct hematopoietic stem cells modulate hematopoietic lineage potential during aging by a mechanism of clonal expansion.” Proceedings of the National Academy of Sciences of the United States of America vol. 107,12 (2010): 5465-70. doi:10.1073/pnas.1000834107

(2) Authors' molecular data analyses need more rigor with unbiased approaches. They claimed that neither aged LT-HSCs nor aged ST-HSCs exhibited myeloid or lymphoid gene set enrichment but aged bulk HSCs, which are just a sum of LTHSCs and ST-HSCs by their gating scheme (Fig. 4A), showed the "tendency" of enrichment of myeloid-related genes based on the selected gene set (Fig. 4D). Although the proportion of ST-HSCs is reduced in bulk HSCs upon aging, since STHSCs do not exhibit lymphoid gene set enrichment based on their data, it is hard to understand how aged bulk HSCs have more myeloid gene set enrichment compared to young bulk HSCs. This bulk HSC data rather suggest that there could be a trend toward certain lineage bias (although not significant) in aged LT-HSCs or ST-HSCs. Authors need to verify the molecular lineage priming of LT-HSCs and ST-HSCs using another comprehensive dataset. 

Thank you for your thoughtful feedback regarding the lack of myeloid or lymphoid gene set enrichment in aged LT-HSCs and aged ST-HSCs, despite the observed tendency for myeloid-related gene enrichment in aged bulk HSCs.

First, we acknowledge that the GSEA results vary among the different myeloid gene sets analyzed (Fig. 4, D–F; Fig. S4, C–D). Additionally, a comprehensive analysis of mouse HSC aging using multiple RNA-seq datasets reported that nearly 80% of differentially expressed genes show poor reproducibility across datasets[1]. These factors highlight the challenges of interpreting lineage bias in HSCs based solely on previously published transcriptomic data.

Given these points, we believe that emphasizing functional experimental results is more critical than incorporating an additional dataset to support our claim. In this regard, we have confirmed that young and aged LT-HSCs have similar differentiation capacity (Figure 3), while myeloid-biased hematopoiesis is observed in aged bulk HSCs (Figure S3). These findings are further corroborated by independent functional experiments. We sincerely appreciate your insightful comments.

Reference

(1) Flohr Svendsen, Arthur et al. “A comprehensive transcriptome signature of murine hematopoietic stem cell aging.” Blood vol. 138,6 (2021): 439-451. doi:10.1182/blood.2020009729

(3) Although authors could not find any molecular evidence for myeloid-biased hematopoiesis from old HSCs (either LT or ST), they argued that the ratio between LT-HSC and ST-HSC causes myeloid-biased hematopoiesis upon aging based on young HSC experiments (Fig. 6). However, old ST-HSC functional data showed that they barely contribute to blood production unlike young Hoxb5- HSCs (ST-HSC) in the transplantation setting (Fig. 2). Is there any evidence that in unperturbed native old hematopoiesis, old Hoxb5- HSCs (ST-HSC) still contribute to blood production?

If so, what are their lineage potential/output? Without this information, it is hard to argue that the different ratio causes myeloid-biased hematopoiesis in aging context. 

Thank you for the insightful and important question. The post-transplant chimerism of ST-HSCs was low in Fig. 2, indicating that transplantation induced a short-term loss of hematopoietic potential due to hematopoietic stress per cell. 

To reduce this stress, we increased the number of HSCs in transplantation setting. In Fig. S6, old LT-HSCs and old ST-HSCs were transplanted in a 50:50 or 20:80 ratio, respectively. As shown in Fig. S6.D, the 20:80 group, which had a higher proportion of old ST-HSCs, exhibited a statistically significant increase in the lymphoid percentage in the peripheral blood post-transplantation. 

These findings suggest that old ST-HSCs contribute to blood production following transplantation. 

Reviewer #2 (Public review):

While aspects of their work are fascinating and might have merit, several issues weaken the overall strength of the arguments and interpretation. Multiple experiments were done with a very low number of recipient mice, showed very large standard deviations, and had no statistically detectable difference between experimental groups. While the authors conclude that these experimental groups are not different, the displayed results seem too variable to conclude anything with certainty. The sensitivity of the performed experiments (e.g. Fig 3; Fig 6C, D) is too low to detect even reasonably strong differences between experimental groups and is thus inadequate to support the author's claims. This weakness of the study is not acknowledged in the text and is also not discussed. To support their conclusions the authors need to provide higher n-numbers and provide a detailed power analysis of the transplants in the methods section. 

Response #2-1:

Thank you for your important remarks. The power analysis for this experiment shows that power = 0.319, suggesting that more number may be needed. On the other hand, our method for determining the sample size in Figure 3 is as follows:

(1) First, we checked whether myeloid biased change is detected in the bulk-HSC fraction (Figure S3). The results showed that the difference in myeloid output at 16 weeks after transplantation was statistically significant (young vs. aged = 7.2 ± 8.9 vs. 42.1 ± 35.5%, p = 0.01), even though n = 10.

(2) Next, myeloid biased HSCs have been reported to be a fraction with high selfrenewal ability (2004, Blood). If myeloid biased HSCs increase with aging, the increase in myeloid biased HSCs in LT-HSC fraction would be detected with higher sensitivity than in the bulk-HSC fraction used in Figure S3.

(3) However, there was no difference not only in p-values but also in the mean itself, young vs aged = 51.4±31.5% vs 47.4±39.0%, p = 0.82, even though n = 8 in Figure 3. Since there was no difference in the mean itself, it is highly likely that no difference will be detected even if n is further increased.

Regarding Figure 6, we obtained a statistically significant difference and consider the sample size to be sufficient. In addition, we have performed various functional experiments (Figures 2, 5, 6 and S6), and have obtained consistent results that expansion of myeloid biased HSCs does not occur with aging in Hoxb5+HSCs fraction. Based on the above, we conclude that the LT-HSC fraction does not differ in myeloid differentiation potential with aging.

As the authors attempt to challenge the current model of the age-associated expansion of myeloid-biased HSCs (which has been observed and reproduced by many different groups), ideally additional strong evidence in the form of single-cell transplants is provided. 

Response #2-2:

Thank you for the comments. As the reviewer pointed out, we hope we could reconfirm our results using single-cell level technology in the future.

On the other hand, we have reported that the ratio of myeloid to lymphoid cells in the peripheral blood changes when the number of HSCs transplanted, or the number of supporting cells transplanted with HSCs, is varied[1-2]. Therefore, single-cell transplant data need to be interpreted very carefully to determine differentiation potential.

From this viewpoint, future experiments will combine the Hoxb5 reporter system with a lineage tracing system that can track HSCs at the single-cell level over time. This approach will investigate changes in the self-renewal capacity of individual HSCs and their subsequent differentiation into progenitor cells and peripheral blood cells. We have reflected this comment by adding the following sentences in the manuscript.

[P19, L451] “In contrast, our findings should be considered in light of some limitations. In this report, we primarily performed ten to twenty cell transplantation assays. Therefore, the current theory should be revalidated using single-cell technology with lineage tracing system[3-4]. This approach will investigate changes in the self-renewal capacity of individual HSCs and their subsequent differentiation into progenitor cells and peripheral blood cells.” 

It is also unclear why the authors believe that the observed reduction of ST-HSCs relative to LT-HSCs explains the myeloid-biased phenotype observed in the peripheral blood. This point seems counterintuitive and requires further explanation. 

Response #2-3:

Thank you for your comment. We apologize for the insufficient explanation. Our data, as shown in Figures 3 and 4, demonstrate that the differentiation potential of LT-HSCs remains unchanged with age. Therefore, rather than suggesting that an increase in LT-HSCs with a consistent differentiation capacity leads to myeloidbiased hematopoiesis, it seems more accurate to highlight that the relative decrease in the proportion of ST-HSCs, which remain in peripheral blood as lymphocytes, leads to a relative increase in myeloid cells in peripheral blood and thus causes myeloid-biased hematopoiesis.

However, if we focus on the increase in the ratio of LT-HSCs, it is also plausible to explain that “with aging, the proportion of LT-HSCs capable of long-term myeloid hematopoiesis increases. As a result, from 16 weeks after transplantation, the influence of LT-HSCs maintaining the long-term ability to produce myeloid cells becomes relatively more significant, leading to an increase in the ratio of myeloid cells in the peripheral blood and causing myeloid-biased hematopoiesis.”

Based on my understanding of the presented data, the authors argue that myeloidbiased HSCs do not exist, as 

a) they detect no difference between young/aged HSCs after transplant (mind low nnumbers and large std!!!); b) myeloid progenitors downstream of HSCs only show minor or no changes in frequency and c) aged LT-HSCs do not outperform young LT-HSC in myeloid output LT-HSCs in competitive transplants (mind low n-numbers and large std!!!). 

However, given the low n-numbers and high variance of the results, the argument seems weak and the presented data does not support the claims sufficiently. That the number of downstream progenitors does not change could be explained by other mechanisms, for instance, the frequently reported differentiation short-cuts of HSCs and/or changes in the microenvironment. 

Response #2-4:

We appreciate the comments. As mentioned above, we will correct the manuscript regarding the sample size. Regarding the interpreting of the lack of increase in the percentage of myeloid progenitor cells in the bone marrow with age, it is instead possible that various confounding factors, such as differentiation shortcuts or changes in the microenvironment, are involved.

However, even when aged LT-HSCs and young LT-HSCs are transplanted into the same recipient mice, the timing of the appearance of different cell fractions in peripheral blood is similar (Figure 3 of this paper). Therefore, we have not obtained data suggesting that clear shortcuts exist in the differentiation process of aged HSCs into neutrophils or monocytes. Additionally, it is currently consensually accepted that myeloid cells, including neutrophils and monocytes, differentiate from GMPs[1]. Since there is no changes in the proportion of GMPs in the bone marrow with age, we concluded that the differentiation potential into myeloid cells remains consistent with aging.

"Then, we found that the myeloid lineage proportions from young and aged LT-HSCs were nearly comparable during the observation period after transplantation (Fig. 3, B and C)." 

[Comment to the authors]: Given the large standard deviation and low n-numbers, the power of the analysis to detect differences between experimental groups is very low. Experimental groups with too large standard deviations (as displayed here) are difficult to interpret and might be inconclusive. The absence of clearly detectable differences between young and aged transplanted HSCs could thus simply be a false-negative result. The shown experimental results hence do not provide strong evidence for the author's interpretation of the data. The authors should add additional transplants and include a detailed power analysis to be able to detect differences between experimental groups with reasonable sensitivity. 

Response #2-5:

Thank you for providing these insights. Regarding the sample size, we have addressed this in Response #2-1.

Line 293: "Based on these findings, we concluded that myeloid-biased hematopoiesis observed following transplantation of aged HSCs was caused by a relative decrease in ST-HSC in the bulk-HSC compartment in aged mice rather than the selective expansion of myeloid-biased HSC clones." 

Couldn't that also be explained by an increase in myeloid-biased HSCs, as repeatedly reported and seen in the expansion of CD150+ HSCs? It is not intuitively clear why a reduction of ST-HSCs clones would lead to a myeloid bias. The author should try to explain more clearly where they believe the increased number of myeloid cells comes from. What is the source of myeloid cells if the authors believe they are not derived from the expanded population of myeloid-biased HSCs? t 

Response #2-6:

Thank you for pointing this out. We apologize for the insufficient explanation. We will explain using Figure 8 from the paper.

First, our data show that LT-HSCs maintain their differentiation capacity with age, while ST-HSCs lose their self-renewal capacity earlier, so that only long-lived memory lymphocytes remain in the peripheral blood after the loss of selfrenewal capacity in ST-HSCs (Figure 8, upper panel). In mouse bone marrow, the proportion of LT-HSCs increases with age, while the proportion of ST-HSCs relatively decreases (Figure 8, lower panel and Figure S5). 

Our data show that merely reproducing the ratio of LT-HSCs to ST-HSCs observed in aged mice using young LT-HSCs and ST-HSCs can replicate myeloidbiased hematopoiesis. This suggests that the increase in LT-HSC and the relative decrease in ST-HSC within the HSC compartment with aging are likely to contribute to myeloid-biased hematopoiesis.

As mentioned earlier, since the differentiation capacity of LT-HSCs remain unchaged with age, it seems more accurate to describe that the relative decrease in the proportion of ST-HSCs, which retain long-lived memory lymphocytes in peripheral blood, leads to a relative increase in myeloid cells in peripheral blood and thus causes myeloid-biased hematopoiesis.

However, focusing on the increase in the proportion of LT-HSCs, it is also possible to explain that “with aging, the proportion of LT-HSCs capable of long-term myeloid hematopoiesis increases. As a result, from 16 weeks after transplantation, the influence of LT-HSCs maintaining the long-term ability to produce myeloid cells becomes relatively more significant, leading to an increase in the ratio of myeloid cells in the peripheral blood and causing myeloid-biased hematopoiesis.”

Recommendations for the authors: 

Reviewer #2 (Recommendations for the authors):

Summary: 

Comment #2-1: While aspects of their work are fascinating and might have merit, several issues weaken the overall strength of the arguments and interpretation. Multiple experiments were done with a very low number of recipient mice, showed very large standard deviations, and had no statistically detectable difference between experimental groups. While the authors conclude that these experimental groups are not different, the displayed results seem too variable to conclude anything with certainty. The sensitivity of the performed experiments (e.g. Figure 3; Figure 6C, D) is too low to detect even reasonably strong differences between experimental groups and is thus inadequate to support the author's claims. This weakness of the study is not acknowledged in the text and is also not discussed. To support their conclusions the authors, need to provide higher n-numbers and provide a detailed power analysis of the transplants in the methods section. 

Response #2-1

Thank you for your important remarks. The power analysis for this experiment shows that power = 0.319, suggesting that more number may be needed. On the other hand, our method for determining the sample size in Figure 3 is as follows: 

(1) First, we checked whether myeloid biased change is detected in the bulk-HSC fraction (Figure S3). The results showed that the difference in myeloid output at 16 weeks after transplantation was statistically significant (young vs. aged = 7.2 {plus minus} 8.9 vs. 42.1 {plus minus} 35.5%, p = 0.01), even though n = 10. 

(2) Next, myeloid biased HSCs have been reported to be a fraction with high selfrenewal ability (2004, Blood). If myeloid biased HSCs increase with aging, the increase in myeloid biased HSCs in LT-HSC fraction would be detected with higher sensitivity than in the bulk-HSC fraction used in Figure S3. 

(3) However, there was no difference not only in p-values but also in the mean itself, young vs aged = 51.4{plus minus}31.5% vs 47.4{plus minus}39.0%, p = 0.82, even though n = 8 in Figure 3. Since there was no difference in the mean itself, it is highly likely that no difference will be detected even if n is further increased. 

Regarding Figure 6, we obtained a statistically significant difference and consider the sample size to be sufficient. In addition, we have performed various functional experiments (Figures 2, 5, 6 and S6), and have obtained consistent results that expansion of myeloid-biased HSCs does not occur with aging in Hoxb5+HSCs fraction. Based on the above, we conclude that the LT-HSC fraction does not differ in myeloid differentiation potential with aging. 

[Comment for authors]  

Paradigm-shifting extraordinary claims require extraordinary data. Unfortunately, the authors do not provide additional data to further support their claims. Instead, the authors argue the following: Because they were able to find significant differences between experimental groups in some experiments, the absence of significant differences in the results of other experiments must be correct, too. 

This logic is in my view flawed. Any assay/experiment with highly variable data has a very low sensitivity to detect significant differences between groups. If, as in this case, the variance is as large as the entire dynamic range of the readout, it becomes impossible to be able to detect any difference. In these cases, it is not surprising and actually expected that the mean of the group is located close to the center of the dynamic range as is the case here (center of dynamic range: 50%). In other words, this means that the experiments are simply not reproducible. It is absolutely critical to remember that any experiment and its associated statistical analysis has 3 (!!!) instead of 2 possible outcomes: 

(1) There is a statistically significant difference 

(2) There is no statistically significant difference 

(3) The results of the experiment are inconclusive because the replicates are too variable and the results are not reproducible.  

While most of us are inclined to think about outcomes (1) or (2), outcome (3) cannot be neglected. While it might be painful to accept, the only way to address concerns about data reproducibility is to provide additional data, improve reproducibility, and lower the power of the analysis to an acceptable level (e.g. able to detect difference of 5-10% between groups). 

Without going into the technical details, the example graph from the link below illustrates that with a power 0.319 as stated by the authors, approx. 25 transplants, instead of 8, would be required. 

Typically, however, a power of 0.8 is a reasonable value for any power analysis (although it's not a very strong power either). Even if we are optimistic and assume that there might be a reasonably large difference between experimental groups (in the example above P2 = 0.6, which is actually not that large) we can estimate that we would need over 10 transplants per group to say with confidence that two experimental groups likely do not differ. With smaller differences, these numbers increase quickly to 20+ transplants per group as can be seen in the example graph using an Alpha of 0.1 above. 

Further reading can be found here and in many textbooks or other online resources: https://power-analysis.com/effect_size.htm  https://tss.awf.poznan.pl/pdf-188978-110207? filename=Using%20power%20analysis%20to.pdf 

Response:

Thank you for your feedback. We fully agree with the reviewer that paradigmshifting claims must be supported by equally robust data. It has been welldocumented that the frequency of myeloid-biased HSCs increases with age, with reports indicating that over 50% of the HSC compartment in aged mice consists of myeloid-biased HSCs[1,2]. Based on this, we believe that if aged LT-HSCs were substantially myeloid-biased, the difference should be readily detectable.

To further validate our findings, we showed the similar preliminary experiment. The resulting data are shown below (n = 8). 

Author response image 1.

(A) Experimental design for competitive co-transplantation assay. Ten CD45.2⁺ young LT-HSCs and ten CD45.2⁺ aged LT-HSCs were transplanted with 2 × 10⁵ CD45.1⁺/CD45.2⁺ supporting cells into lethally irradiated CD45.1⁺ recipient mice (n \= 8). (B) Lineage output of young or aged LT-HSCs at 4, 8, 12, 16 weeks after transplantation. Each bar represents an individual mouse. *P < 0.05. **P < 0.01.

While a slight increase in myeloid-biased hematopoiesis was observed in the aged LT-HSC fraction, the difference was not statistically significant. These new results are presented alongside the original Figure 3, which was generated using a larger sample size (n = 16).

Author response image 2.

(A) Experimental design for competitive co-transplantation assay. Ten CD45.2⁺ young LT-HSCs and ten CD45.2⁺ aged LT-HSCs were transplanted with 2 × 10⁵ CD45.1⁺/CD45.2⁺ supporting cells into lethally irradiated CD45.1⁺ recipient mice (n \= 16). (B) Lineage output of young or aged LT-HSCs at 4, 8, 12, 16 weeks after transplantation. Each bar represents an individual mouse. 

Consistent with the original data, aged LT-HSCs exhibited a lineage output that was nearly identical to that of young LT-HSCs. Nonetheless, as the reviewer rightly pointed out, we cannot completely exclude the possibility that subtle differences may exist but remain undetected. To address this, we have added the following sentence to the manuscript:  

[P9, L200] “These findings unmistakably demonstrated that mixed/bulk-HSCs showed myeloid skewed hematopoiesis in PB with aging. In contrast, LT-HSCs maintained a consistent lineage output throughout life, although subtle differences between aged and young LT-HSCs may exist and cannot be entirely ruled out.”

References

(1) Dykstra, Brad et al. “Clonal analysis reveals multiple functional defects of aged murine hematopoietic stem cells.” The Journal of experimental medicine vol. 208,13 (2011): 2691-703. doi:10.1084/jem.20111490

(2) Beerman, Isabel et al. “Functionally distinct hematopoietic stem cells modulate hematopoietic lineage potential during aging by a mechanism of clonal expansion.” Proceedings of the National Academy of Sciences of the United States of America vol. 107,12 (2010): 5465-70. doi:10.1073/pnas.1000834107

Comment #2-3: It is also unclear why the authors believe that the observed reduction of STHSCs relative to LT-HSCs explains the myeloid-biased phenotype observed in the peripheral blood. This point seems counterintuitive and requires further explanation. 

Response #2-3:  

Thank you for your comment. We apologize for the insufficient explanation. Our data, as shown in Figures 3 and 4, demonstrate that the differentiation potential of LTHSCs remains unchanged with age. Therefore, rather than suggesting that an increase in LT-HSCs with a consistent differentiation capacity leads to myeloid biased hematopoiesis, it seems more accurate to highlight that the relative decrease in the proportion of ST-HSCs, which remain in peripheral blood as lymphocytes, leads to a relative increase in myeloid cells in peripheral blood and thus causes myeloid-biased hematopoiesis. However, if we focus on the increase in the ratio of LT-HSCs, it is also plausible to explain that "with aging, the proportion of LT-HSCs capable of long-term myeloid hematopoiesis increases. As a result, from 16 weeks after transplantation, the influence of LT-HSCs maintaining the long-term ability to produce myeloid cells becomes relatively more significant, leading to an increase in the ratio of myeloid cells in the peripheral blood and causing myeloid-biased hematopoiesis." 

[Comment for authors] 

While this interpretation of the data might make sense the shown data do not exclude alternative explanations. The authors do not exclude the possibility that LTHSCs expand with age and that this expansion in combination with an aging microenvironment drives myeloid bias. The authors should quantify the frequency [%] and absolute number of LT-HSCs and ST-HSCs in young vs. aged animals. Especially analyzing the abs. numbers of cells will be important to support their claims as % can be affected by changes in the frequency of other populations. 

Thank you for your very important point. As this reviewer pointed out, we do not exclude the possibility that the combination of aged microenvironment drives myeloid bias. Additionally, we acknowledge that myeloid-biased hematopoiesis with age is a complex process likely influenced by multiple factors. We would like to discuss the mechanism mentioned as a future research direction. Thank you for the insightful feedback. Regarding the point about the absolute cell numbers mentioned in the latter half of the paragraph, we will address this in detail in our subsequent response (Response #2-4).

Comment #2-4: Based on my understanding of the presented data, the authors argue that myeloid-biased HSCs do not exist, as a) they detect no difference between young/aged HSCs after transplant (mind low n-numbers and large std!); b) myeloid progenitors downstream of HSCs only show minor or no changes in frequency and c) aged LT-HSCs do not outperform young LT-HSCs in myeloid output LTHSCs in competitive transplants (mind low n-numbers and large std!). However, given the low n-numbers and high variance of the results, the argument seems weak and the presented data does not support the claims sufficiently. That the number of downstream progenitors does not change could be explained by other mechanisms, for instance, the frequently reported differentiation short-cuts of HSCs and/or changes in the microenvironment. 

Response #2-4:  

We appreciate the comments. As mentioned above, we will correct the manuscript regarding the sample size. Regarding the interpreting of the lack of increase in the percentage of myeloid progenitor cells in the bone marrow with age, it is instead possible that various confounding factors, such as differentiation shortcuts or changes in the microenviroment, are involved. However, even when aged LT-HSCs and young LT-HSCs are transplanted into the same recipient mice, the timing of the appearance of different cell fractions in peripheral blood is similar (Figure 3 of this paper). Therefore, we have not obtained data suggesting that clear shortcuts exist in the differentiation process of aged HSCs into neutrophils or monocytes. Additionally, it is currently consensually accepted that myeloid cells, including neutrophils and monocytes, differentiate from GMPs1. Since there are no changes in the proportion of GMPs in the bone marrow with age, we concluded that the differentiation potential into myeloid cells remains consistent with aging. 

Reference 

(1) Akashi K and others, 'A Clonogenic Common Myeloid Progenitor That Gives Rise to All Myeloid Lineages', Nature, 404.6774 (2000), 193-97. 

[Comment for authors] 

As the relative frequency of cell population can be misleading, the authors should compare the absolute numbers of progenitors in young vs. aged mice to strengthen their argument. It would also be helpful to quantify the absolute numbers and relative frequencies in WT mice to exclude the possibility the HoxB5-trimcherry mouse model suffers from unexpected aging phenotypes and the hematopoietic system differs from wild-type animals.

Thank you for your valuable feedback. We understand the importance of comparing the absolute numbers of progenitors in young versus aged mice to provide a more accurate representation of the changes in cell populations.

Therefore, we quantified the absolute cell count of hematopoietic cells in the bone marrow using flow cytometry data. 

Author response image 3.

As previously reported, we observed a 10-fold increase in the number of pHSCs in aged mice compared to young mice. Additionally, our analysis revealed a statistically significant decrease in the number of Flk2+ progenitors and CLPs in aged mice. On the other hand, there was no statistically significant change in the number of myeloid progenitors between the two age groups. We appreciate the suggestion and hope that this additional information strengthens our argument and addresses your concerns.

Comment #2-5:  

"Then, we found that the myeloid lineage proportions from young and aged LT-HSCs were nearly comparable during the observation period after transplantation (Figure 3, B and C)." Given the large standard deviation and low n-numbers, the power of the analysis to detect differences between experimental groups is very low. Experimental groups with too large standard deviations (as displayed here) are difficult to interpret and might be inconclusive. The absence of clearly detectable differences between young and aged transplanted HSCs could thus simply be a false-negative result. The shown experimental results hence do not provide strong evidence for the author's interpretation of the data. The authors should add additional transplants and include a detailed power analysis to be able to detect differences between experimental groups with reasonable sensitivity. 

Response #2-5:  

Thank you for providing these insights. Regarding the sample size, we have addressed this in Response #2-1. 

[Comment for authors]  

As explained in detail in the response to #2-1 the provided arguments are not convincing. As the authors pointed out, the power of these experiments is too low to make strong claims. If the author does not intend to provide new data, the language of the manuscript needs to be adjusted to reflect this weakness. A paragraph discussing the limitations of the study mentioning the limited power of the data should be included beyond the above-mentioned rather vague statement that the data should be validated (which is almost always necessary anyway). 

Thank you for your valuable comment. We agree with the importance of discussing potential limitations in our experimental design. In response to the reviewer’s suggestion, we have revised the manuscript to include the following sentences:

[P19, L434] "In the co-transplantation assay shown in Figure 3, the myeloid lineage output derived from young and aged LT-HSCs was comparable (Young LT-HSC: 51.4 ± 31.5% vs. Aged LT-HSC: 47.4 ± 39.0%, p = 0.82). Although no significant difference was detected, the small sample size (n = 8) may limit the sensitivity of the assay to detect subtle myeloid-biased phenotypes."

This addition acknowledges the potential limitations of our analysis and highlights the need for further investigation with larger cohorts.

Comment #2-6:

Line 293: "Based on these findings, we concluded that myeloid biased hematopoiesis observed following transplantation of aged HSCs was caused by a relative decrease in ST-HSC in the bulk-HSC compartment in aged mice rather than the selective expansion of myeloid-biased HSC clones." Couldn't that also be explained by an increase in myeloid-biased HSCs, as repeatedly reported and seen in the expansion of CD150+ HSCs? It is not intuitively clear why a reduction of STHSCs clones would lead to a myeloid bias. The author should try to explain more clearly where they believe the increased number of myeloid cells comes from. What is the source of myeloid cells if the authors believe they are not derived from the expanded population of myeloid-biased HSCs?

Response #2-6:

Thank you for pointing this out. We apologize for the insufficient explanation. We will explain using attached Figure 8 from the paper. First, our data show that LT-HSCs maintain their differentiation capacity with age, while ST-HSCs lose their self-renewal capacity earlier, so that only long-lived memory lymphocytes remain in the peripheral blood after the loss of self-renewal capacity in ST-HSCs (Figure 8, upper panel). In mouse bone marrow, the proportion of LT-HSCs increases with age, while the proportion of STHSCs relatively decreases (Figure 8, lower panel and Figure S5).

Our data show that merely reproducing the ratio of LT-HSCs to ST-HSCs observed in aged mice using young LT-HSCs and ST-HSCs can replicate myeloid-biased hematopoiesis. This suggests that the increase in LT-HSC and the relative decrease in ST-HSC within the HSC compartment with aging are likely to contribute to myeloid-biased hematopoiesis.

As mentioned earlier, since the differentiation capacity of LT-HSCs remain unchanged with age, it seems more accurate to describe that the relative decrease in the proportion of STHSCs, which retain long-lived memory lymphocytes in peripheral blood, leading to a relative increase in myeloid cells in peripheral blood and thus causes myeloid-biased hematopoiesis. However, focusing on the increase in the proportion of LT-HSCs, it is also possible to explain that "with aging, the proportion of LT-HSCs capable of long-term myeloid hematopoiesis increases. As a result, from 16 weeks after transplantation, the influence of LT-HSCs maintaining the long-term ability to produce myeloid cells become relatively more significant, leading to an increase in the ratio of myeloid cells in the peripheral blood and causing myeloid biased hematopoiesis."

[Comment for authors]

While I can follow the logic of the argument, my concerns about the interpretation remain as I see discrepancies in other findings in the published literature. For instance, what the authors call ST-HSCs, differs from the classical functional definition of ST-HSCs. It is thus difficult to relate the described observations to previous reports. ST-HSCs typically can contribute significantly to multiple lineages for several weeks (see for example PMID: 29625072). It is somewhat surprising that the ST-HSC in this study don't show this potential and loose their potential much quicker.

The authors should thus provide a more comprehensive depth of immunophenotypic and molecular characterization to compare their LT-HSCs to ST-HSCs. For instance, are LT-HSCs CD41- HSCs? How do ST-HSCs differ in their surface marker expression from previously used definitions of ST-HSCs? A list of differentially expressed genes between young and old LT-HSCs and ST-HSCs should be done and will likely provide important insights into the molecular programs/markers (beyond the provided GO analysis, which seems superficial).

Thank you for your valuable feedback. As the reviewer noted, there are indeed multiple definitions of ST-HSCs. We appreciate the opportunity to clarify our definitions of ST-HSCs. We define ST-HSCs functionally, rather than by surface antigens, which we believe is the most classical and widely accepted definition [1]. In our study, we define long-term hematopoietic stem cells (LT-HSCs) as those HSCs that continue to contribute to hematopoiesis after a second transplantation and possess long-term self-renewal potential. Conversely, we define short-term hematopoietic stem cells (ST-HSCs) as those HSCs that do not contribute to hematopoiesis after a second transplantation and only exhibit self-renewal potential in the short term. 

Next, in the paper referenced by the reviewer[2], the chimerism of each fraction of ST-HSCs also peaked at 4 weeks and then decreased to approximately 0.1% after 12 weeks post-transplantation. Author response image 5 illustrates our ST-HSC donor chimerism in Figure 2. We believe that data in the paper referenced by the reviewer2 is consistent with our own observations of the hematopoietic pattern following ST-HSC transplantation, indicating a characteristic loss of hematopoietic potential 4 weeks after the transplantation. Furthermore, as shown in Figures 2D and 2F, the fraction of ST-HSCs does not exhibit hematopoietic activity after the second transplantation. Therefore, we consider this fraction to be ST-HSCs.

Author response image 4.

Additionally, the RNAseq data presented in Figures 4 and S4 revealed that the GSEA results vary among the different myeloid gene sets analyzed (Fig. 4, D–F; Fig. S4, C–D). Moreover, a comprehensive analysis of mouse HSC aging using multiple RNA-seq datasets reported that nearly 80% of differentially expressed genes show poor reproducibility across datasets[3]. From the above, while RNAseq data is indeed helpful, we believe that emphasizing functional experimental results is more critical than incorporating an additional dataset to support our claim. Thank you once again for your insightful feedback.

References

(1) Kiel, Mark J et al. “SLAM family receptors distinguish hematopoietic stem and progenitor cells and reveal endothelial niches for stem cells.” Cell vol. 121,7 (2005): 1109-21. doi:10.1016/j.cell.2005.05.026

(2) Yamamoto, Ryo et al. “Large-Scale Clonal Analysis Resolves Aging of the Mouse Hematopoietic Stem Cell Compartment.” Cell stem cell vol. 22,4 (2018): 600-607.e4. doi:10.1016/j.stem.2018.03.013

(3) Flohr Svendsen, Arthur et al. “A comprehensive transcriptome signature of murine hematopoietic stem cell aging.” Blood vol. 138,6 (2021): 439-451. doi:10.1182/blood.2020009729

Reviewer #3 (Public review): 

Although the topic is appropriate and the new model provides a new way to think about lineage-biased output observed in multiple hematopoietic contexts, some of the experimental design choices, as well as some of the conclusions drawn from the results could be substantially improved. Also, they do not propose any potential mechanism to explain this process, which reduces the potential impact and novelty of the study. 

The authors have satisfactorily replied to some of my comments. However, there are multiple key aspects that still remain unresolved.

Reviewer #3 (Recommendations for the authors): 

Comment #3-1,2:  

Although the additional details are much appreciated the core of my original comments remains unanswered. There are still no details about the irradiation dose for each particular experiment. Is any transplant performed using a 9.1 Gy dose? If yes, please indicate it in text or figure legend. If not, please remove this number from the corresponding method section. 

Again, 9.5 Gy (split in two doses) is commonly reported as sublethal. The fact that the authors used a methodology that deviates from the "standard" for the field makes difficult to put these results in context with previous studies. It is not possible to know if the direct and indirect effects of this conditioning method in the hematopoietic system have any consequences in the presented results. 

Thank you for your clarification. We confirm that none of the transplantation experiments described were performed using a 9.1 Gy irradiation dose. We have therefore removed the mention of "9.1 Gy" from the relevant section of the Materials and Methods. We appreciate helpful suggestion to improve the clarity of the manuscript.

[P22, L493] “12-24 hours prior to transplantation, C57BL/6-Ly5.1 mice, or aged C57BL/6J recipient mice were lethally irradiated with single doses of 8.7 Gy.”

Regarding the reviewer’s concern about the radiation dose used in our experiments, we will address this point in more detail in our subsequent response (see Response #3-4).

Comment #3-4(Original): When representing the contribution to PB from transplanted cells, the authors show the % of each lineage within the donor-derived cells (Figures 3B-C, 5B, 6B-D, 7C-E, and S3 B-C). To have a better picture of total donor contribution, total PB and BM chimerism should be included for each transplantation assay. Also, for Figures 2C-D and Figures S2A-B, do the graphs represent 100% of the PB cells? Are there any radioresistant cells?

Response #3-4 (Original): Thank you for highlighting this point. Indeed, donor contribution to total peripheral blood (PB) is important information. We have included the donor contribution data for each figure above mentioned.

In Figure 2C-D and Figure S2A-B, the percentage of donor chimerism in PB was defined as the percentage of CD45.1-CD45.2+ cells among total CD45.1-CD45.2+ and CD45.1+CD45.2+ cells as described in method section.

Comment for our #3-4 response:  

Thanks for sharing these data. These graphs should be included in their corresponding figures along with donor contribution to BM. 

Regarding Figure2 C-D, as currently shown, the graphs only account for CD45.1CD45.2+ (donor-derived) and CD45.1+CD45.2+ (supporting-derived). What is the percentage of CD45.1+CD45.2- (recipient-derived)? Since the irradiation regiment is atypical, including this information would help to know more about the effects of this conditioning method. 

Thank you for your insightful comment regarding Figure 2C-D. To address the concern that the reviewer pointed out, we provide the kinetics of the percentage of CD45.1+CD45.2- (recipient-derived) in Author response image 7.

Author response image 5.

As the reviewer pointed out, we observed the persistence of recipient-derived cells, particularly in the secondary transplant. As noted, this suggests that our conditioning regimen may have been suboptimal. In response, we will include the donor chimerism analysis in the total cells and add the following statement in the study limitations section to acknowledge this point:

[P19, L439] “Additionally, in this study, we purified LT-HSCs using the Hoxb5 reporter system and employed a moderate conditioning regimen (8.7 Gy). To have a better picture of total donor contribution, total PB chimerism are presented in Figure S7 and we cannot exclude the possibility that these factors may have influenced the results. Therefore, it would be ideal to validate our findings using alternative LT-HSC markers and different conditioning regimens.”

Comment #3-5: For BM progenitor frequencies, the authors present the data as the frequency of cKit+ cells. This normalization might be misleading as changes in the proportion of cKit+ between the different experimental conditions could mask differences in these BM subpopulations. Representing this data as the frequency of BM single cells or as absolute numbers (e.g., per femur) would be valuable.

Response #3-5:

We appreciate the reviewer's comment on this point. 

Firstly, as shown in Supplemental Figures S1B and S1C, we analyze the upstream (HSC, MPP, Flk2+) and downstream (CLP, MEP, CMP, GMP) fractions in different panels. Therefore, normalization is required to assess the differentiation of HSCs from upstream to downstream.

Additionally, the reason for normalizing by c-Kit+ is that the bone marrow analysis was performed after enrichment using the Anti-c-Kit antibody for both upstream and downstream fractions. Based on this, we calculated the progenitor populations as a frequency within the c-Kit positive cells. Next, the results of normalizing the whole bone marrow cells (live cells) are shown below. 

Author response image 6.

Similar to the results of normalizing c-Kit+ cells, myeloid progenitors remained unchanged, including a statistically significant decrease in CMP in aged mice. Additionally, there were no significant differences in CLP. In conclusion, similar results were obtained between the normalization with c-Kit and the normalization with whole bone marrow cells (live cells).

However, as the reviewer pointed out, it is necessary to explain the reason for normalization with c-Kit. Therefore, we will add the following description.

[P21, L502] For the combined analysis of the upstream (HSC, MPP, Flk2+) and downstream (CLP, MEP, CMP, GMP) fractions in Figures 1B, we normalized by cKit+ cells because we performed a c-Kit enrichment for the bone marrow analysis.

Comment for our #3-5 response:

I understand that normalization is necessary to compare across different BM populations. However, the best way would be to normalize to single cells. As I mentioned in my original comment, normalizing to cKit+ cells could be misleading, as the proportion of cKit+ cells could be different across the experimental conditions. Further, enriching for cKit+ cells when analyzing BM subpopulation frequencies could introduce similar potential errors. The enrichment would depend on the level of expression of cKit for each of these population, what would alter the final quantification. Indeed, CLP are typically defined as cKit-med/low. Thus, cKit enrichment would not be a great method to analyze the frequency of these cells. 

The graph in the authors' response to my comment, show similar trend to what is represented Figure 1B for some populations. However, there are multiple statistically significant changes that disappear in this new version. This supports my original concern and, in consequence, I would encourage to represent this data as the frequency of BM single cells or as absolute numbers (e.g., per femur). 

Thank you for your thoughtful follow-up comment. In response to the reviewer’s suggestion, we will represent the data as the frequency among total BM single cells. These revised graphs have been incorporated into the updated Figure 7F and corresponding figure legend have been revised accordingly to accurately reflect these representations. We appreciate your valuable input, which has helped us improve the clarity and rigor of our data presentation.

Comment #3-6: Regarding Figure 1B, the authors argue that if myeloid-biased HSC clones increase with age, they should see increased frequency of all components of the myeloid differentiation pathway (CMP, GMP, MEP). This would imply that their results (no changes or reduction in these myeloid subpopulations) suggest the absence of myeloid-biased HSC clones expansion with age. This reviewer believes that differentiation dynamics within the hematopoietic hierarchy can be more complex than a cascade of sequential and compartmentalized events (e.g., accelerated differentiation at the CMP level could cause exhaustion of this compartment and explain its reduction with age and why GMP and MEP are unchanged) and these conclusions should be considered more carefully.

Response #3-6:

We wish to thank the reviewer for this comment. We agree with that the differentiation pathway may not be a cascade of sequential events but could be influenced by various factors such as extrinsic factors.

In Figure 1B, we hypothesized that there may be other mechanisms causing myeloid-biased hematopoiesis besides the age-related increase in myeloid-biased HSCs, given that the percentage of myeloid progenitor cells in the bone marrow did not change with age. However, we do not discuss the presence or absence of myeloid-biased HSCs based on the data in Figure 1B. 

Our newly proposed theories—that the differentiation capacity of LT-HSCs remains unchanged with age and that age-related myeloid-biased hematopoiesis is due to changes in the ratio of LT-HSCs to ST-HSCs—are based on functional experiment results. As the reviewer pointed out, to discuss the presence or absence of myeloid-biased HSCs based on the data in Figure 1B, it is necessary to apply a system that can track HSC differentiation at single-cell level. The technology would clarify changes in the self-renewal capacity of individual HSCs and their differentiation into progenitor cells and peripheral blood cells. The authors believe that those single-cell technologies will be beneficial in understanding the differentiation of HSCs. Based on the above, the following statement has been added to the text.

[P19, L440] In contrast, our findings should be considered in light of some limitations. In this report, we primarily performed ten to twenty cell transplantation assays. Therefore, the current theory should be revalidated using single-cell technology with lineage tracing system1-2. This approach will investigate changes in the self-renewal capacity of individual HSCs and their subsequent differentiation into progenitor cells and peripheral blood cells. 

Comment for our #3-6 response:

Thanks for the response. My original comments referred to the statement "On the other hand, in contrast to what we anticipated, the frequency of GMP was stable, and the percentage of CMP actually decreased significantly with age, defying our prediction that the frequency of components of the myeloid differentiation pathway, such as CMP, GMP, and MEP would increase in aged mice if myeloid-biased HSC clones increase with age (Fig. 1 B)" (lines #129-133). Again, the absence of an increase in CMP, GMP and MEP with age does not mean the absence of and increase in myeloid-biased HSC clones. This statement should be considered more carefully. 

Thank you for the insightful comment. We agree that the absence of an increase in CMP, GMP and MEP with age does not mean the absence of an increase in myeloid-biased HSC clones. In our revised manuscript, we have refined the statement to acknowledge this nuance more clearly. The updated text now reads as follows:

P6, L129] On the other hand, in contrast to what we anticipated, the frequency of GMP was stable, and the percentage of CMP actually decreased significantly with age, defying our prediction that the frequency of components of the myeloid differentiation pathway, such as CMP, GMP, and MEP may increase in aged mice, if myeloid-biased HSC clones increase with age. 

Comment #3-7: Within the few recipients showing good donor engraftment in Figure 2C, there is a big proportion of T cells that are "amplified" upon secondary transplantation (Figure 2D). Is this expected?

Response #3-7:

We wish to express our deep appreciation to the reviewer for insightful comment on this point. As the reviewers pointed out, in Figure 2D, a few recipients show a very high percentage of T cells. The authors had the same question and considered this phenomenon as follows:

(1) One reason for the very high percentage of T cells is that we used 1 x 107 whole bone marrow cells in the secondary transplantation. Consequently, the donor cells in the secondary transplantation contained more T-cell progenitor cells, leading to a greater increase in T cells compared to the primary transplantation.

(2) We also consider that this phenomenon may be influenced by the reduced selfrenewal capacity of aged LT-HSCs, resulting in decreased sustained production of myeloid cells in the secondary recipient mice. As a result, long-lived memorytype lymphocytes may preferentially remain in the peripheral blood, increasing the percentage of T cells in the secondary recipient mice.

We have discussed our hypothesis regarding this interesting phenomenon. To further clarify the characteristics of the increased T-cell count in the secondary recipient mice, we will analyze TCR clonality and diversity in the future.

Comment for our #3-7 response:

Thanks for the potential explanations to my question. This fact is not commonly reported in previous transplantation studies using aged HSCs. Could Hoxb5 label fraction of HSCs that is lymphoid/T-cell biased upon secondary transplantation? The number of recipients with high frequency of lymphoid cells in the peripheral blood (even from young mice) is remarkable. 

Response:

Thank you for your insightful suggestion. Based on this comment, we calculated the percentage of lymphoid cells in the donor fraction at 16 weeks following the secondary transplantation, which was 56.1 ± 25.8% (L/M = 1.27). According to the Müller-Sieburg criteria, lymphoid-biased hematopoiesis is defined as having an L/M ratio greater than 10. 

Given our findings, we concluded that the Hoxb5-labeled fraction does not specifically indicate lymphoid-biased hematopoiesis. We sincerely appreciate the valuable input, which helped us to further clarify the interpretation of our results.

Comment #3-8: Do the authors have any explanation for the high level of variabilitywithin the recipients of Hoxb5+ cells in Figure 2C?

Response #3-8:

We appreciate the reviewer's comment on this point. As noted in our previous report, transplantation of a sufficient number of HSCs results in stable donor chimerism, whereas a small number of HSCs leads to increased variability in donor chimerism1. Additionally, other studies have observed high variability when fewer than 10 HSCs are transplanted2-3. Based on this evidence, we consider that the transplantation of a small number of cells (10 cells) is the primary cause of the high level of variability observed.

Comment for our #3-8 response:

I agree that transplanting low number of HSC increases the mouse-to-mouse variability. For that reason, a larger cohort of recipients for this kind of experiment would be ideal. 

Response:

Thank you for the insightful comment. We agree that a larger cohort of recipients would be ideal for this type of experiment. In Figure 2, the difference between Hoxb5<suup>+</sup> and Hoxb5⁻ cells are robust, allowing for a clear statistical distinction despite the cohort size. However, we also recognize that a larger cohort would be necessary to detect more subtle differences, particularly in Figure 3. In response, we have added the following statement to the main text to acknowledge this limitation.

P9, L200] These findings unmistakably demonstrated that mixed/bulk-HSCs showed myeloid skewed hematopoiesis in PB with aging. In contrast, LT-HSCs maintained a consistent lineage output throughout life, although subtle differences between aged and young LT-HSCs may exist and cannot be entirely ruled out.

Comment #3-10: Is Figure 2G considering all primary recipients or only the ones that were used for secondary transplants? The second option would be a fairer comparison.

Response #3-10:

We appreciate the reviewer's comment on this point. We considered all primary recipients in Figure 2G to ensure a fair comparison, given the influence of various factors such as the radiosensitivity of individual recipient mice[1]. Comparing only the primary recipients used in the secondary transplantation would result in n = 3 (primary recipient) vs. n = 12 (secondary recipient). Including all primary recipients yields n = 11 vs. n = 12, providing a more balanced comparison. Therefore, we analyzed all primary recipient mice to ensure the reliability of our results.

Comment for our #3-10 response:

I respectfully disagree. Secondary recipients are derived from only 3 of the primary recipients. Therefore, the BM composition is determined by the composition of their donors. Including primary recipients that are not transplanted into secondary recipients for is not the fairest comparison for this analysis. 

Thank you for your comment and for highlighting this important issue. We acknowledge the concern that including primary recipients that are not transplanted into secondary recipients is not the fairest comparison for this analysis. In response, we have reanalyzed the data using only the primary recipients whose bone marrow was actually transplanted into secondary recipients. 

Author response image 7.

Importantly, the reanalysis confirmed that the kinetics of myeloid cell proportions in peripheral blood were consistent between primary and secondary transplant recipients. We sincerely appreciate your thoughtful feedback, which has helped us improve the clarity.

Comment #3-11: When discussing the transcriptional profile of young and aged HSCs, the authors claim that genes linked to myeloid differentiation remain unchanged in the LT-HSC fraction while there are significant changes in the STHSCs. However, 2 out of the 4 genes shown in Figure S4B show ratios higher than 1 in LT-HSCs.

Response #3-11:

Thank you for highlighting this important point. As the reviewer pointed out, when we analyze the expression of myeloid-related genes, some genes are elevated in aged LT-HSCs compared to young LT-HSCs. However, the GSEA analysis using myeloid-related gene sets, which include several hundred genes, shows no significant difference between young and aged LT-HSCs (see Figure S4C in this paper). Furthermore, functional experiments using the co-transplantation system show no difference in differentiation capacity between young and aged LT-HSCs (see Figure 3 in this paper). Based on these results, we conclude that LT-HSCs do not exhibit any change in differentiation capacity with aging.

Comment for our #3-11 response:

The authors used the data in Figure S4 to claim that "myeloid genes were tended to be enriched in aged bulk-HSCs but not in aged LT-HSCs compared to their respective controls" (this is the title of the figure; line # 1326). This is based on an increase in gene expression of CD150, vWF, Selp, Itgb3 in aged cells compared to young cells (Figure S4B). However, an increase in Selp and Itgb3 is also observed for LT-HSCs (lower magnitude, but still and increase). 

Also, regarding the GSEA, the only term showing statistical significance in bulk HSCs is "Myeloid gene set", which does not reach significance in LT-HSCs, but present a trend for enrichment (q = 0.077). None of the terms in shown in this panel present statistical significance in ST-HSCs. 

Thank you for your valuable point. As the reviewer noted, the current title may cause confusion. Therefore, we propose changing it to the following:

[P52, L1331] “Figure S4. Compared to their respective young controls, aged bulk-HSCs exhibit greater enrichment of myeloid gene expression than aged LT-HSCs”

Author response:

The following is the authors’ response to the previous reviews.

Reviewer #1 (Public Review):

Original comment: There is no explanation for how this work could be a breakthrough in simulation gregarious feeding as is stated in the manuscript.

Reviewer response: I think I understand where the authors are trying to take this next step. If the authors were to follow up on this study with the proposed implementation of inhalant/exhalent velocities profiles (or more preferably velocity/pressure fields), then that study would be a breakthrough in simulating such gregarious feeding. Based on what has been done within the present study, I think the term "breakthrough" is instead overly emphatic. An additional note on this. The authors are correct that incorporating additional models could be used to simulation a population (as has been successfully done for several Ediacaran taxa despite computational limitations), but it's not the only way. The authors 1 might explore using periodic boundary conditions on the external faces of the flow domain. This could require only a single Olivooid model to assess gregarious impacts - see the abundant literature of modeling flow through solar array fields.

We appreciate the reviewer 1 for the suggestion. Modeling gregarious feeding via periodic boundary conditions is surely a practical way with limited computational resources. Modeling flow through solar array fields can also be an inspiring case. However, to realism the simulation of gregarious feeding behavior on an uneven seabed and with irregular organism spatial distribution, just using periodic boundary conditions may not be sufficient (see Author response image 1 for a simple example). We will go on exploring the way of realizing the simulations of large-scale gregarious feeding.

Author response image 1.

An example of modeling gregarious feeding behavior on an uneven seabed.

Original comment: The claim that olivooid-type feeding was most likely a prerequisite transitional form to jet-propelled swimming needs much more support or needs to be tailored to olivooids. This suggests that such behavior is absent (or must be convergent) before olivooids, which is at odds with the increasing quantities of pelagic life (whose modes of swimming are admittedly unconstrained) documented from Cambrian and Neoproterozoic deposits. Even among just medusozoans, ancestral 1 state reconstruction suggests that they would have been swimming during the Neoproterozoic (Kayal et al., 2018; BMC Evolutionary Biology) with no knowledge of the mechanics due to absent preservation. Author response: Thanks for your suggestions. Yes, we agree with you that the ancestral swimming medusae may appear before the early Cambrian, even at the Neoproterozoic deposits. However, discussions on the affinities of Ediacaran cnidarians are severely limited because of the lack of information concerning their soft anatomy. So, it is hard to detect the mechanics due to absent preservation. Olivooids found from the basal Cambrian Kuanchuanpu Formation can be reasonably considered as cnidarians based on their radial symmetry, external features, and especially the internal anatomies (Bengtson and Yue 1997; Dong et al. 2013; 2016; Han et al. 2013; 2016; Liu et al. 2014; Wang et al. 2017; 2020; 2022). The valid simulation experiment here was based on the soft tissue preserved in olivooids.

Reviewer response: This response does not sufficiently address my earlier comment. While the authors are correct that individual Ediacaran affinities are an area of active research and that Olivooids can reasonably be considered cnidarians, this doesn't address the actual critique in my comment. Most (not all) Ediacaran soft-bodied fossils are considered to have been benthic, but pelagic cnidarian life is widely acknowledged to at least be present during later White Sea and Nama assemblages (and earlier depending on molecular clock interpretations). The authors have certainly provided support for the mechanics of this type of feeding being co-opted for eventual jet propulsion swimming in Olivooids. They have not provided sufficient justifications within the manuscript for this to be broadened beyond this group.

Thanks for your sincere commentary. We of course agree with the possibility of the emergence of swimming cnidarians before the lowermost Cambrian Fortunian Stage. See lines 16-129: “Ediacaran fossil assemblages with complex ecosystems consist of exceptionally preserved soft-bodied eukaryotes of enigmatic morphology, which their affinities are mostly unresolved (Tarhan et al., 2018, Integrative and Comparative Biology, 58 (4), 688–702; Evans et al., 2022, PNAS, 11(46), e220747511).” Undoubtedly Olivooids belong to cnidarians charactered by their external and internal biological structures. Limited by the fossil records, we could only speculate on the transition from the benthic to the swimming of ancestral cnidarians via the valid fossil preservation, e.g. olivooids. The transition may require processes such as increasing body size, thickening the mesoglea, and degenerating the periderm, etc. And these processes may also evolve independently or comprehensively. Moreover, the ecological behaviors of the ancestral cnidarians may evolve independently at different stages from Ediacaran to Cambrian. We therefore could not provide more sufficient justifications beyond olivooids.

Original comment: L446: two layers of hexahedral elements is a very low number for meshing boundary layer flow

Reviewer response: As the authors point out in the main text, these organisms are small (millimeters in scale) and certainly lived within the boundary layer range of the ocean. While the boundary layer is not the main point, it still needs to be accurately resolved as it should certainly affect the flow further towards the far field at this scale. I'm not suggesting the authors need to perfectly resolve the boundary layer or focus on using turbulence models more tailored to boundary layer flows (such as k-w), but the flow field still needs sufficient realism for a boundary bounded flow. The authors really should consider quantitatively assessing the number of hexahedral elements within their mesh refinement study.

To address this concern, we run another four simulations based on mesh4 within our mesh refinement study to assess the number of hexahedral elements (five layers and eight layers of hexahedral elements with different thickness of boundary layer mesh (controlled by thickness adjustment factor), respectively). the results had been supplemented to Table supplement 2. As shown in the results, the number of layers of hexahedral elements seems does not significant influence the result, but the thickness of boundary layer mesh can influence the maximum flow velocity of the contraction phase. However, the results of all the simulations were generally consistent, as shown in Author response image 2. The description of the results above were added to section “Mesh sensitivity analysis”.

Author response image 2.

Results of mesh refinement study of different boundary layer mesh parameters.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public Review):

Summary:

This paper explores how diverse forms of inhibition impact firing rates in models for cortical circuits. In particular, the paper studies how the network operating point affects the balance of direct inhibition from SOM inhibitory neurons to pyramidal cells, and disinhibition from SOM inhibitory input to PV inhibitory neurons. This is an important issue as these two inhibitory pathways have largely been studies in isolation. Support for the main conclusions is generally solid, but could be strengthened by additional analyses.

Strengths

The paper has improved in revision, and the new intuitive summary statements added to the end of each results section are quite helpful. Weaknesses

The concern about whether the results hold outside of the range in which neural responses are linear remains. This is particularly true given the discontinuity observed in the stability measure. I appreciate the concern (provided in the response to the first round of reviews) that studying nonlinear networks requires a lot of work. A more limited undertaking would be to test the behavior of a spiking network at a few key points identified by your linearization approach. Such tests could use relatively simple (and perhaps imperfect) measures of gain and stability. This could substantially enhance the paper, regardless of the outcome.

We appreciate the reviewer’s concern and in our resubmission we explore if networks dynamics that operate outside of the case where linearization is possible would continue to show our main result on the (dis)entanglement of stability and gain; the short answer is yes. To this end we have added a new section and Figure to our main text.

“Gain and stability in stochastically forced E – PV – SOM circuits

To confirm that our results do not depend on our approach of a linearization around a fixed point, we numerically simulate similar networks as shown above (Figure 2) in which the E and PV population receive slow varying, large amplitude noise (Figure 6A). This leads to noisy rate dynamics sampling a large subspace of the full firing rate grid (r_E,r_P) and thus any linearization would fail to describe the network response. In this stochastically forced network we explore how adding an SOM modulation or a stimulus affects this subspace (Figure 6B). To quantify stability without linearization, we assume that a network is more stable the lower the mean and variance of E rates. This is because very stable networks can better quench input fluctuations [Kanashiro et al., 2017; Hennequin et al., 2018]. To quantify gain, we calculate the change in E rates when adding the stimulus, yet having identical noise realizations for stimulated and non-stimulated networks (Methods).

For the disinhibitory network without feedback a positive SOM modulation decreases stability due to increases of the mean and variance of E rates (Figure 6Ci) while the network gain increases (Figure 6Cii). As seen before (Figure 2A,B), stability and gain change in opposite directions in a disinhibitory circuit without feedback. Adding feedback PV → SOM and applying a negative SOM modulation increases both, stability and gain and therefore disentangles the inverse relation also in a noisy circuit (Figure 6D-F). This gives numerical support that our results do not depend on the assumption of linearization.

“Methods: Noisy input and numerical measurement of stability and gain

We consider a temporally smoothed input process ξ_X with white noise ζ (zero mean, standard deviation one): for populations X ∈{E,P} with timescale τ_ξ = 50ms, σ_X \= 6 and fixed mean input IX. To quantify the stability of the network without linearization, we assume that a network is more stable if the mean and variance of excitatory rates are low. To quantify network gain, we freeze the white noise process ζ for the case of with and without stimulus presentation and calculate the difference of E rates at each time point, leading to a distribution of network gains (Figure 6Cii,Fii). Total simulation time is 1000 seconds.”

We decided against using a spiking network because sufficiently asynchronous spiking network dynamics can still obey a linearized mean field theory (if the fluctuations in population firing rates are small). In our new analysis the firing rate deviations from the time averaged firing rate are sizable, making a linearization ineffective.

In summary, based on our additional analysis of recurrent circuits with noisy inputs we conclude that our results also hold in fluctuating networks, without the need of assuming realization aroud a stable fixed point.

Reviewer #2 (Public Review):

Summary:

Bos and colleagues address the important question of how two major inhibitory interneuron classes in the neocortex differentially affect cortical dynamics. They address this question by studying Wilson-Cowan-type mathematical models. Using a linearized fixed point approach, they provide convincing evidence that the existence of multiple interneuron classes can explain the counterintuitive finding that inhibitory modulation can increase the gain of the excitatory cell population while also increasing the stability of the circuit’s state to minor perturbations. This effect depends on the connection strengths within their circuit model, providing valuable guidance as to when and why it arises.

Overall, I find this study to have substantial merit. I have some suggestions on how to improve the clarity and completeness of the paper.

Strengths:

(1) The thorough investigation of how changes in the connectivity structure affect the gain-stability relationship is a major strength of this work. It provides an opportunity to understand when and why gain and stability will or will not both increase together. It also provides a nice bridge to the experimental literature, where different gain-stability relationships are reported from different studies.

(2) The simplified and abstracted mathematical model has the benefit of facilitating our understanding of this puzzling phenomenon. (I have some suggestions for how the authors could push this understanding further.) It is not easy to find the right balance between biologically-detailed models vs simple but mathematically tractable ones, and I think the authors struck an excellent balance in this study.

We thank the reviewer for their support of our work.

Weaknesses:

(1) The fixed-point analysis has potentially substantial limitations for understanding cortical computations away from the steady-state. I think the authors should have emphasized this limitation more strongly and possibly included some additional analyses to show that their conclusions extend to the chaotic dynamical regimes in which cortical circuits often live.

In the response to reviewer 1 we have included model analyses that addresses the limitations of linearization. Rather than use a chaotic model, which would require significant effort, we opted for a stochastically forced network, where the sizable fluctuations in rate dynamics preclude linearization.

(2) The authors could have discussed – even somewhat speculatively – how VIP interneurons fit into this picture. Their absence from this modelling framework stands out as a missed opportunity.

We agree that including VIP neurons into the framework would be an obvious and potentially interesting next step. At this point we only include them as potential modulators of SOM neurons. Modeling their dynamics without them receiving inputs from E, PV, or SOM neurons would be uninteresting. However, including them properly into the circuit would be outside the scope of the paper.

(3) The analysis is limited to paths within this simple E, PV, SOM circuit. This misses more extended paths (like thalamocortical loops) that involve interactions between multiple brain areas. Including those paths in the expansion in Eqs. 11-14 (Fig. 1C) may be an important consideration.

We agree that our pathway expansion can be used to study more than just the E – PV – SOM circuit. However, properly investigating full thalamocortcial loops should be done in a subsequent study.

Comments on revisions:

I think the authors have done a reasonable job of responding to my critiques, and the paper is in pretty good shape. (Also, thanks for correctly inferring that I meant VIP interneurons when I had written SST in my review! I have updated the public review accordingly.)

I still think this line of research would benefit substantially from considering dynamic regimes including chaotic ones. I strongly encourage the authors to consider such an extension in future work.

Please see our response above to Reviewer 1.

Reviewer #3 (Public Review):

Summary:

Bos et al study a computational model of cortical circuits with excitatory (E) and two subtypes of inhibition parvalbumin (PV) and somatostatin (SOM) expressing interneurons. They perform stability and gain analysis of simplified models with nonlinear transfer functions when SOM neurons are perturbed. Their analysis suggests that in a specific setup of connectivity, instability and gain can be untangled, such that SOM modulation leads to both increases in stability and gain, in contrast to the typical direction in neuronal networks where increased gain results in decreased stability.

Strengths:

- Analysis of the canonical circuit in response to SOM perturbations. Through numerical simulations and mathematical analysis, the authors have provided a rather comprehensive picture of how SOM modulation may affect response changes.

- Shedding light on two opposing circuit motifs involved in the canonical E-PV-SOM circuitry - namely, direct inhibition (SOM -¿ E) vs disinhibition (SOM -¿ PV -¿ E). These two pathways can lead to opposing effects, and it is often difficult to predict which one results from modulating SOM neurons. In simplified circuits, the authors show how these two motifs can emerge and depend on parameters like connection weights.

- Suggesting potentially interesting consequences for cortical computation. The authors suggest that certain regimes of connectivity may lead to untangling of stability and gain, such that increases in network gain are not compromised by decreasing stability. They also link SOM modulation in different connectivity regimes to versatile computations in visual processing in simple models.

We thank the reviewer for their support of our work.

Weaknesses

Computationally, the analysis is solid, but it’s very similar to previous studies (del Molino et al, 2017). Many studies in the past few years have done the perturbation analysis of a similar circuitry with or without nonlinear transfer functions (some of them listed in the references). This study applies the same framework to SOM perturbations, which is a useful computational analysis, in view of the complexity of the high-dimensional parameter space.

Link to biology: the most interesting result of the paper with regard to biology is the suggestion of a regime in which gain and stability can be modulated in an unconventional way - however, it is difficult to link the results to biological networks:

- A general weakness of the paper is a lack of direct comparison to biological parameters or experiments. How different experiments can be reconciled by the results obtained here, and what new circuit mechanisms can be revealed? In its current form, the paper reads as a general suggestion that different combinations of gain modulation and stability can be achieved in a circuit model equipped with many parameters (12 parameters). This is potentially interesting but not surprising, given the high dimensional space of possible dynamical properties. A more interesting result would have been to relate this to biology, by providing reasoning why it might be relevant to certain circuits (and not others), or to provide some predictions or postdictions, which are currently missing in the manuscript.

- For instance, a nice motivation for the paper at the beginning of the Results section is the different results of SOM modulation in different experiments - especially between L23 (inhibition) and L4 (disinhibition). But no further explanation is provided for why such a difference should exist, in view of their results and the insights obtained from their suggested circuit mechanisms. How the parameters identified for the two regimes correspond to different properties of different layers?

Please see our answer to the previous round of revision.

- One of the key assumptions of the model is nonlinear transfer functions for all neuron types. In terms of modelling and computational analysis, a thorough analysis of how and when this is necessary is missing (an analysis similar to what has been attempted in Figure 6 for synaptic weights, but for cellular gains). A discussion of this, along with the former analysis to know which nonlinearities would be necessary for the results, is needed, but currently missing from the study. The nonlinearity is assumed for all subtypes because it seems to be needed to obtain the results, but it’s not clear how the model would behave in the presence or absence of them, and whether they are relevant to biological networks with inhibitory transfer functions.

Please see our answer to the previous round of revision.

- Tuning curves are simulated for an individual orientation (same for all), not considering the heterogeneity of neuronal networks with multiple orientation selectivity (and other visual features) - making the model too simplistic.

Please see our answer to the previous round of revision.

Reviewer #1 (Recommendations For The Authors):

Introduction, first paragraph, last sentence: suggest ”sense,” -¿ ”sense” (no comma)

Introduction, second paragraph, first sentence: suggest ”is been” -¿ ”has been”

Introduction, very end of next to last paragraph: clarify ”modulate the circuit”

Figure 1 legend: can you make the ”Change ...” in the legend for 1D clearer - e.g. ”strenghen SOM → E connections and eliminate SOM → P connections”.

Paragraph immediately below Figure 1: In sentence starting ”Specifically ...” can you relate the cases described here back to the equation in Figure 1C?

Sentence right below equation 2: This sentence does not separate the network gain from the cellular gain as clearly as it could.

Page 7, second full paragraph: sentence starting ”Therefore, with ...” could be split into two or otherwise made clearer.

Sentence starting ”Furthermore” right below Figure 5 has an extra comma

We thank the reviewer for their additional comments, we made the respective changes in the manuscript.

Reviewer #3 (Recommendations For The Authors):

There is a long part in the reply letter discussing the link to biology - but the revised manuscript doesn’t seem to reflect that.

The information in the reply letter discussing the link to biology has been added at multiple points in the discussion. In the section ‘decision of labor between PV and SOM neurons’ we mention Ferguson and Carding 2020, in the section ‘impact of SOM neuron modulation on tuning curves’ we discuss Phillups and Hasenstaub 2016, and in the section ‘limitations and future directions’ we mention Tobin et al., 2023.

The writing can be improved - for example, see below instances:

P. 7: Intuitively, the inverse relationship follows for inhibitory and disinhibitory pathways (and their mixture) because the firing rate grid (heatmap) does not depend on how the SOM neurons inhibit the E - PV circuit.

P.8: We first remark that by adding feedback E connections onto SOM neurons, changes in SOM rates can now affect the underlying heatmaps in the (rE, rP) grid.

Not clear how ”rates can affect the heatmaps”. It’s too colloquial and not scientifically rigorous or sound.

We added further explanations at the respective places in the manuscript to improve the writing.

Author Response

The following is the authors’ response to the previous reviews.

Public Reviews:

Reviewer #2 (Public Review):

I would like to express my appreciation for the authors' dedication to revising the manuscript. It is evident that they have thoughtfully addressed numerous concerns I previously raised, significantly contributing to the overall improvement of the manuscript.

Response: We appreciate the reviewers’ recognition of our efforts in revising the manuscript.

My primary concern regarding the authors' framing of their findings within the realm of habitual and goal-directed action control persists. I will try explain my point of view and perhaps clarify my concerns. While acknowledging the historical tendency to equate procedural learning with habits, I believe a consensus has gradually emerged among scientists, recognizing a meaningful distinction between habits and skills or procedural learning. I think this distinction is crucial for a comprehensive understanding of human action control. While these constructs share similarities, they should not be used interchangeably. Procedural learning and motor skills can manifest either through intentional and planned actions (i.e., goal-directed) or autonomously and involuntarily (habitual responses).

Response: We would like to clarify that, contrary to the reviewer’s assertion of a scientific consensus on this matter, the discussion surrounding the similarities and differences between habits and skills remains an ongoing and unresolved topic of interest among scientists (Balleine and Dezfouli, 2019; Du and Haith, 2023; Graybiel and Grafton, 2015; Haith and Krakauer, 2018; Hardwick et al., 2019; Kruglanski and Szumowska, 2020; Robbins and Costa, 2017). We absolutely agree with the reviewer that “Procedural learning and motor skills can manifest either through intentional and planned actions (i.e., goal-directed) or autonomously and involuntarily (habitual responses)”. But so do habits. Some researchers also highlight the intentional/goal-directed nature of habits (e.g., Du and Haith, 2023, “Habits are not automatic” (preprint) or Kruglanski and Szumowska, 2020, “Habitual behavior is goal-driven”: “definitions of habits that include goal independence as a foundational attribute of habits are begging the question; they effectively define away, and hence dispose of, the issue of whether habits are goal-driven (p 1258).” Therefore, there is no clear consensus concerning the concept of habit.

While we acknowledge the meaningful distinctions between habits and skills, we also recognize a substantial body of literature supporting the overlap between these concepts (cited in our manuscript), particularly at the neural level. The literature clearly indicates that both habits and skills are mediated by subcortical circuits, with a progressive disengagement of cognitive control hubs in frontal and cingulate cortices as repetition evolves. We do not use these concepts interchangeably. Instead, we simply present evidence supporting the assertion that our trained app sequences meet several criteria for their habitual nature.

Our choice of Balleine and Dezfouli (2018)'s criteria stemmed from the comprehensive nature of their definitions, which effectively synthesized insights from various researchers (Mazar and Wood, 2018; Verplanken et al., 1998; Wood, 2017, etc). Importantly, their list highlights the positive features of habits that were previously overlooked. However, these authors still included a controversial criterion ("habits as insensitive to changes in their relationship to their individual consequences and the value of those consequences"), even though they acknowledged the problems of using outcome devaluation methods and of relying on a null-effect. According to Kruglanski and Szumowska (2020), this criterion is highly problematic as “If, by definition, habits are goalindependent, then any behavior found to be goal-dependent could not be a habit on sheer logical grounds” (p. 1257). In their definition, “habitual behavior is sensitive to the value of the reward (i.e., the goal) it is expected to mediate and is sensitive to the expectancy of goal attainment (i.e., obtainment of the reward via the behavior, p.1265). In fact, some recent analyses of habitual behavior are not using devaluation or revaluation as a criterion (Du and Haith, 2023). This article, for example, ascertains habits using different criteria and provides supporting evidence for trained action sequences being understood as skills, with both goal-directed and habitual components.

In the discussion of our manuscript, we explicitly acknowledge that the app sequences can be considered habitual or goal-directed in nature and that this terminology does not alter the fact that our overtrained sequences exhibit clear habitual features.

Watson et al. (2022) aptly detailed my concerns in the following statements: "Defining habits as fluid and quickly deployed movement sequences overlaps with definitions of skills and procedural learning, which are seen by associative learning theorists as different behaviors and fields of research, distinct from habits."

"...the risk of calling any fluid behavioral repertoire 'habit' is that clarity on what exactly is under investigation and what associative structure underpins the behavior may be lost." I strongly encourage the authors, at the very least, to consider Watson et al.'s (2022) suggestion: "Clearer terminology as to the type of habit under investigation may be required by researchers to ensure that others can assess at a glance what exactly is under investigation (e.g., devaluationinsensitive habits vs. procedural habits)", and to refine their terminology accordingly (to make this distinction clear). I believe adopting clearer terminology in these respects would enhance the positioning of this work within the relevant knowledge landscape and facilitate future investigations in the field.

Response: We would like to highlight that we have indeed followed Watson et al (2022)’s recommendations on focusing on other features/criteria of habits at the expense of the outcome devaluation/contingency degradation paradigm, which has been more controversial in the human literature. Our manuscript clearly aligns with Watson et al. (2022) ‘s recommendations: “there are many other features of habits that are not captured by the key metrics from outcome devaluation/contingency degradation paradigms such as the speed at which actions are performed and the refined and invariant characteristics of movement sequences (Balleine and Dezfouli, 2019). Attempts are being made to develop novel behavioral tasks that tap into these positive features of habits, and this should be encouraged as should be tasks that are not designed to assess whether that behavior is sensitive to outcome devaluation, but capture the definition of habits through other measures”.

Regarding the authors' use of Balleine and Dezfouli's (2018) criteria to frame recorded behavior as habitual, as well as to acknowledgment the study's limitations, it's important to highlight that while the authors labelled the fourth criterion (which they were not fulfilling) as "resistance to devaluation," Balleine and Dezfouli (2018) define it as "insensitive to changes in their relationship to their individual consequences and the value of those consequences." In my understanding, this definition is potentially aligned with the authors' re-evaluation test, namely, it is conceptually adequate for evaluating the fourth criterion (which is the most accepted in the field and probably the one that differentiate habits from skills). Notably, during this test, participants exhibited goaldirected behavior.

The authors characterized this test as possibly assessing arbitration between goal-directed and habitual behavior, stating that participants in both groups "demonstrated the ability to arbitrate between prior automatic actions and new goal-directed ones." In my perspective, there is no justification for calling it a test of arbitration. Notably, the authors inferred that participants were habitual before the test based on some criteria, but then transitioned to goal-directed behavior based on a different criterion. While I agree with the authors' comment that: "Whether the initiation of the trained motor sequences in experiment 3 (arbitration) is underpinned by an action-outcome association (or not) has no bearing on whether those sequences were under stimulus-response control after training (experiment 1)." they implicitly assert a shift from habit to goal-directed behavior without providing evidence that relies on the same probed mechanism. Therefore, I think it would be more cautious to refer to this test as solely an outcome revaluation test. Again, the results of this test, if anything, provide evidence that the fourth criterion was tested but not met, suggesting participants have not become habitual (or at least undermines this option).

Response: In our previously revised manuscript, we duly acknowledged that the conventional (perhaps nowadays considered outdated) goal devaluation criterion was not met, primarily due to constraints in designing the second part of the study. We did cite evidence from another similar study that had used devaluation app-trained action sequences to demonstrate habitual qualities (but the reviewer ignored this).

The reviewer points out that we did use a manipulation of goal revaluation in one of the follow-up tests conducted (although this was not a conventional goal revaluation test inasmuch that it was conducted in a novel context). In this test, please note that we used 2 manipulations: monetary and physical effort. Although we did show that subjects, including OCD patients, were apparently goaldirected in the monetary reward manipulation, this was not so clear when goal re-evaluation involved the physical effort expended. In this effort manipulation, participants were less goaloriented and OCD patients preferred to perform the longer, familiar, to the shorter, novel sequence, thus exhibiting significantly greater habitual tendencies, as compared to controls. Hence, we cannot decisively conclude that the action sequence is goal-directed as the reviewer is arguing. In fact, the evidence is equivocal and may reflect both habitual and goal-directed qualities in the performance of this sequence, consistent with recent interpretations of skilled/habitual sequences (Du and Haith, 2023). Relying solely on this partially met criterion to conclude that the app-trained sequences are goal-directed, and therefore not habitual, would be an inaccurate assessment for several reasons: 1) the action sequences did satisfy all other criteria for being habitual; 2) this approach would rest on a problematic foundation for defining habits, as emphasized by Kruglanski & Szumowska (2020); and 3) it would succumb to the pitfall of subscribing to a zero-sum game perspective, as cautioned by various researchers, including the review by Watson et al. (2022) cited by the referee, thus oversimplifying the nuanced nature of human behavior.

While we have previously complied with the reviewer’s suggestion on relabelling our follow-up test as a “revaluation test” instead of an “arbitration test”, we have now explicitly removed all mentions of the term “arbitration” (which seems to raise concerns) throughout the manuscript. As the reviewer has suggested, we now use a more refined terminology by explicitly referring to the measured behavior as "procedural habits", as he/she suggested. We have also extensively revised the discussion section of our manuscript to incorporate the reviewer’s viewpoint. We hope that these adjustments enhance the clarity and accuracy of our manuscript, addressing the concerns raised during this review process.

In essence, this is an ontological and semantic matter, that does not alter our findings in any way. Whether the sequences are consider habitual or goal directed, does not change our findings that 1) Both groups displayed equivalent procedural learning and automaticity attainment; 2) OCD patients exhibit greater subjective habitual tendencies via self-reported questionnaires; 3) Patients who had elevated compulsivity and habitual self-reported tendencies engaged significantly more with the motor habit-training app, practiced more and reported symptom relief at the end of the study; 4) these particular patients also show an augmented inclination to attribute higher intrinsic value to familiar actions, a possible mechanism underlying compulsions.

Reviewer #2 (Recommendations For The Authors):

A few more small comments (with reference to the point numbers indicated in the rebuttal):

(14) I am not entirely sure why the suggested analysis is deemed impractical (i.e., why it cannot be performed by "pretending" participants received the points they should have received according to their performance). This can further support (or undermine) the idea of effect of reward on performance rather than just performance on performance.

Response: We have now conducted this analysis, generating scores for each trial of practices after day 20, when participants no longer gained points for their performance. This analysis assesses whether participants trial-wise behavioral changes exhibit a similar pattern following simulated relative increases or decrease in scores, as if they had been receiving points at this stage. Note that this analysis has fewer trials available, around 50% less on average.

Before presenting our results, we wish to emphasize the importance of distinguishing between the effects of performance on performance and the effects of reward on performance. In response to a reviewer's suggestion, we assessed the former in the first revision of our manuscript. We normalized the movement time variable and evaluated how normalized behavioral changes responded to score increments and decrements. The results from the original analyses were consistent with those from the normalized data.

Regarding the phase where participants no longer received scores, we believe this phase primarily helps us understand the impact of 'predicted' or 'learned' rewards on performance. Once participants have learned the simple association between faster performance and larger scores, they can be expected to continue exhibiting the reward sensitivity effects described in our main analysis. We consider it is not feasible to assess the effects of performance on performance during the reward removal phase, which occurs after 20 days. Therefore, the following results pertain to how the learned associations between faster movement times and scores persist in influencing behavior, even when explicit scores are no longer displayed on the screen.

Results: The main results of the effect of reward on behavioral changes persist, supporting that relative increases or decreases in scores (real or imagined/inferred) modulate behavioral adaptations trial-by-trial in a consistent manner across both cohorts. The direction of the effects of reward is the same as in the main analyses presented in the manuscript: larger mean behavioral changes (smaller std) following ∆R- . First, concerning changes in “normalized” movement time (MT) trial-by-trial, we conducted a 2 x 2 factorial analysis of the centroid of the Gaussian distributions with the same factors Reward, Group and Bin. This analysis demonstrated a significant main effect of Reward (P = 2e-16), but not of Group (P = 0.974) or Bin (P = 0.281). There were no significant interactions between factors. The main Reward effect can be observed in the top panel of the figure below. The same analysis applied to the spread (std) of the Gaussian distributions revealed a significant main effect of Reward (P = 0.000213), with no additional main effects or interactions.

Author response image 1.

Next, conducting the same 2 x 2 factorial analyses on the centroid and spread of the Gaussian distributions fitted to the Consistency data, we also obtained a robust significant main effect of Reward. For the centroid variable, we obtained a significant main effect of Reward (P = 0.0109) and Group (P = 0.0294), while Bin and the factor interactions were non-significant. See the top panel of the figure below.

On the other hand, Reward also modulated significantly the spread of the Gaussian distributions fitted to the Consistency data, P = 0.00498. There were no additional significant main effects or interactions. See the bottom panel in the figure below.

Note that here the factorial analysis was performed on the logarithmic transformation of the std.

Author response image 2.

(16) I find this result interesting and I think it might be worthwhile to include it in the paper.

Response: We have now included this result in our revised manuscript (page 28)

(18) I referred to this sentence: "The app preferred sequence was their preferred putative habitual sequence while the 'any 6' or 'any 3'-move sequences were the goal-seeking sequences." In my understanding, this implies one choice is habitual and another indicates goal-directedness.

One last small comment:
In the Discussion it is stated: "Moreover, when faced with a choice between the familiar and a new, less effort-demanding sequence, the OCD group leaned toward the former, likely due to its inherent value. These insights align with the theory of goal-direction/habit imbalance in OCD (Gillan et al., 2016), underscoring the dominance of habits in particular settings where they might hold intrinsic value."

This could equally be interpreted as goal-directed behavior, so I do not think there is conclusive support for this claim.

Response: The choice of the familiar/trained sequence, as opposed to the 'any 6' or 'any 3'-move sequences cannot be explicitly considered goal-directed: firstly, because the app familiar sequences were associated with less monetary reward (in the any-6 condition), and secondly, because participants would clearly need more effort and time to perform them. Even though these were automatic, it would still be much easier and faster to simply tap one finger sequentially 6 times (any6) or 3 times (any-3). Therefore, the choice for the app-sequence would not be optimal/goaldirected. In this sense, that choice aligns with the current theory of goal-direction/habit imbalance of OCD. We found that OCD patients prefer to perform the trained app sequences in the physical effort manipulation (any-3 condition). While this, on one hand cannot be explicitly considered a goal-directed choice, we agree that there is another possible goal involved here, which links to the intrinsic value associated to the familiar sequence. In this sense the action could potentially be considered goal-directed. This highlights the difficulty of this concept of value and agrees with: 1) Hommel and Wiers (2017): “Human behavior is commonly not driven by one but by many overlapping motives . . . and actions are commonly embedded into larger-scale activities with multiple goals defined at different levels. As a consequence, even successful satiation of one goal or motive is unlikely to also eliminate all the others(p. 942) and 2) Kruglanski & Szumowska (2020)’s account that “habits that may be unwanted from the perspective of an outsider and hence “irrational” or purposeless, may be highly wanted from the perspective of the individual for whom a habit is functional in achieving some goal” (p. 1262) and therefore habits are goal-driven.

References:

Balleine BW, Dezfouli A. 2019. Hierarchical Action Control: Adaptive Collaboration Between Actions and Habits. Front Psychol 10:2735. doi:10.3389/fpsyg.2019.02735

Du Y, Haith A. 2023. Habits are not automatic. doi:10.31234/osf.io/gncsf Graybiel AM, Grafton ST. 2015. The Striatum: Where Skills and Habits Meet. Cold Spring Harb Perspect Biol 7:a021691. doi:10.1101/cshperspect.a021691

Haith AM, Krakauer JW. 2018. The multiple effects of practice: skill, habit and reduced cognitive load. Current Opinion in Behavioral Sciences 20:196–201. doi:10.1016/j.cobeha.2018.01.015

Hardwick RM, Forrence AD, Krakauer JW, Haith AM. 2019. Time-dependent competition between goal-directed and habitual response preparation. Nat Hum Behav 1–11. doi:10.1038/s41562019-0725-0

Hommel B, Wiers RW. 2017. Towards a Unitary Approach to Human Action Control. Trends Cogn Sci 21:940–949. doi:10.1016/j.tics.2017.09.009

Kruglanski AW, Szumowska E. 2020. Habitual Behavior Is Goal-Driven. Perspect Psychol Sci 15:1256– 1271. doi:10.1177/1745691620917676

Mazar A, Wood W. 2018. Defining Habit in Psychology In: Verplanken B, editor. The Psychology of Habit: Theory, Mechanisms, Change, and Contexts. Cham: Springer International Publishing. pp. 13–29. doi:10.1007/978-3-319-97529-0_2

Robbins TW, Costa RM. 2017. Habits. Current Biology 27:R1200–R1206. doi:10.1016/j.cub.2017.09.060

Verplanken B, Aarts H, van Knippenberg A, Moonen A. 1998. Habit versus planned behaviour: a field experiment. Br J Soc Psychol 37 ( Pt 1):111–128. doi:10.1111/j.2044-8309.1998.tb01160.x

Watson P, O’Callaghan C, Perkes I, Bradfield L, Turner K. 2022. Making habits measurable beyond what they are not: A focus on associative dual-process models. Neurosci Biobehav Rev 142:104869. doi:10.1016/j.neubiorev.2022.104869

Wood W. 2017. Habit in Personality and Social Psychology. Pers Soc Psychol Rev 21:389–403. doi:10.1177/1088868317720362

Author response:

The following is the authors’ response to the previous reviews

We have thoroughly addressed all the reviewers’ comments and meticulously revised the manuscript. Key modifications include the following:

(a) Organizing the Logic and Highlighting Key Findings: We have revised the manuscript to emphasize key findings (especially the distinctions between the SEC and WOI groups) according to the following logic: constructing a receptive endometrial organoid, comparing its molecular characteristics with those of the receptive endometrium, highlighting its main features (hormone response, enhanced energy metabolism, ciliary assembly and motility, epithelial-mesenchymal transition), and exploring the function involved in embryo interaction.

(b) Clarity and Better Description of Bioinformatic Analyses: We have revised the sections involving bioinformatic analyses to provide a more streamlined and comprehensible explanation. Instead of overwhelming the reader with excessive details, we focused on the most important findings, and performed additional experimental validation.

(c) Rationale for Gene Selection: We have clarified the rationale for selecting certain genes and pathways for inclusion in the analysis and manuscript. The associated gene expression data for all figures have been provided in the attached Dataset.

(d) In the response letter, we have provided the detailed presentation of the methodological optimization for constructing this endometrial assembloids, along with optimization and comparison of endometrial organoid culture media. Furthermore, in the Limitations section, we have explicitly stated that stromal cells and immune cells gradually diminish with increasing passage numbers. Therefore, this study primarily utilized endometrial assembloids within the first three passages for all investigations.

Below, we provide a point-by-point response to each comment, with all modifications highlighted in the revised manuscript. We respectfully hope that these revisions effectively address the concerns raised by the reviewers.

Public Reviews:

Reviewer #1 (Public Review):

This study generated 3D cell constructs from endometrial cell mixtures that were seeded in the Matrigel scaffold. The cell assemblies were treated with hormones to induce a "window of implantation" (WOI) state. The authors did their best to revise their study according to the reviewers' comments. However, the study remains unconvincing and at the same time too dense and not focused enough.

(1) The use of the term organoids is still confusing and should be avoided. Organoids are epithelial tissue-resembling structures. Hence, the multiplecell aggregates developed here are rather "coculture models" (or "assembloids"). It is still unexpected (unlikely) that these structures containing epithelial, stromal and immune cells can be robustly passaged in the epithelial growth conditions used. All other research groups developing real organoids from endometrium have shown that only the epithelial compartment remains in culture at passaging (while the stromal compartment is lost). If authors keep to their idea, they should perform scRNA-seq on both early and late (passage 6-10) "organoids". And they should provide details of culturing/passaging/plating etc that are different with other groups and might explain why they keep stromal and immune cells in their culture for such a long time. In other words, they should then in detail compare their method to the standard method of all other researchers in the field, and show the differences in survival and growth of the stromal and immune cells.

(1) We appreciate your feedback and have revised the term 'organoids' to 'assembloids'. 2)

I. Due to budget constraints, this study did not perform scRNA-seq on both early and late passages (P6-P10). Instead, immunofluorescence staining confirmed the persistence of stromal cells at passage 6 (as shown below).

Author response image 1.

Whole-mount immunofluorescence showed that Vimentin+ F-actin+ cells (stromal cells) were arranged around the glandular spheres that were only F-actin+(passage 6).

II. Improvements in this study include the following.

a. Optimization of endometrial tissue processing: The procedures for tissue collection, pretreatment, digestion, and culture were refined to maximize the retention of endometrial epithelial cells, stromal cells, and immune cells (detailed optimizations are provided in Response Table 1).

b. Enhanced culture medium formulation: Based on previous protocols, WNT3A was added to promote organoid development and differentiation (PMID: 27315476), while FGF2 was supplemented to improve stromal cell survival (PMID: 35224622) (see Response Table 2 for medium comparisons). Representative culture outcomes are shown in the figure below.

We acknowledge that the stromal and immune cells in this system still exhibit differences compared to their in vivo counterparts. In this study, we utilized the first three passages, which offer optimal cell diversity and viability, to meet experimental needs. However, replicating and maintaining the full complexity of endometrial cell types in vitro remains a major challenge in the field—one that we are actively working to address.

Author response table 1.

Methodological Optimization of Endometrial Organoids (Construction, Passaging, and Cryopreservation)

Author response table 2.

Optimization and comparison of endometrial organoid culture media

Author response image 2.

Bright-field microscopy captures the expansion of glands and surrounding stromal cells across passages 0 to 2 (scar bar=200μm) (Yellow arrows: stromal cells; White arrows: glands).

(2) The paper is still much too dense, touching upon all kind of conclusions from the manifold bioinformatic analyses. The latter should be much clearer and better described, and then some interesting findings (pathways/genes) should be highlighted without mentioning every single aspect that is observed. The paper needs a lot of editing to better focus and extract take-home messages, not bombing the reader with a mass of pathways, genes etc which makes the manuscript just not readable or 'digest-able'. There is no explanation whatever and no clear rationale why certain genes are included in a list while others are not. There is the impression that mass bioinformatics is applied without enough focus.

Thanks for your suggestions. We have made improvements and revisions in the following areas:

(a) Clarity and Better Description of Bioinformatic Analyses: We have revised the sections involving bioinformatic analyses to provide a more streamlined and comprehensible explanation. Instead of overwhelming the reader with excessive details, we focused on the most important findings.

(b) Organizing the Logic and Highlighting Key Findings: We have revised the manuscript to emphasize key findings according to the following logic: constructing a receptive endometrial organoid, comparing its molecular characteristics with those of the receptive endometrium, highlighting its main features (hormone response, enhanced energy metabolism, ciliary assembly and motility, epithelial-mesenchymal transition), and exploring the function involved in embryo interaction.

(c) Rationale for Gene Selection: We have clarified the rationale for selecting certain genes and pathways for inclusion in the analysis and manuscript.

We hope these revisions address your concerns and improve the overall quality and clarity of the manuscript. Thank you once again for your valuable input.

(3) The study is much too descriptive and does not show functional validation or exploration (except glycogen production). Some interesting findings extracted from the bioinformatics must be functionally tested.

Thanks for your suggestions. We have restructured the logic and revised the manuscript, incorporating functional validation. The focus is on the following points: highlighting its main features (hormone response, enhanced energy metabolism, ciliary assembly and motility, epithelial-mesenchymal transition), and exploring the functions involved in embryo interaction.

(4) In contrast to what was found in vivo (Wang et al. 2020), no abrupt change in gene expression pattern is mentioned here from the (early-) secretory to the WoI phase. Should be discussed. Although the bioinformatic analyses point into this direction, there are major concerns which must be solved before the study can provide the needed reliability and credibility for revision.

To further investigate the abrupt change, the Mfuzz algorithm was utilized to analyze gene expression across the three groups, focusing on gene clusters that were progressively upregulated or downregulated. It was observed that mitochondrial and cilia-related genes exhibited the highest expression levels in WOI endometrial organoids, as well as cell junction and negative regulation of cell differentiation were downregulated (Figure 4A).

(5) All data should be benchmarked to the Wang et al 2020 and Garcia-Alonso et al. 2021 papers reporting very detailed scRNA-seq data, and not only the Stephen R. Quake 2020 paper.

We appreciate your suggestion. By integrating data from Garcia-Alonso et al. (2021) (shown in the figure below), we observed that both WOI organoids and SEC organoids exhibit increased glandular secretory epithelium and developed ciliated epithelium, mirroring features of mid-secretory endometrium. The findings exhibit parallels when contrasting these two papers.

Author response image 3.

UMAP visualization of integrated scRNA-seq data (our dataset and Garcia-Alonso et al. 2021) showing: (A) cell types, (B) WOI-org, (C)CTRL-org, (D)SEC-org versus published midsecretory samples.

(6) Fig. 2B: Vimentin staining is not at all clear. F-actin could be used to show the typical morphology of the stromal cells?

We appreciate your suggestion. We performed additional staining for F-actin based on Vimentin, and found that Vimentin+ F-actin+ cells (stromal cells) were arranged around the glandular spheres that were only F-actin+.

(7) Where does the term "EMT-derived stromal cells" come from? On what basis has this term been coined?

Within endometrial biology, stromal cells in the transition from epithelial to mesenchymal phenotype are specifically referred to as 'stromal EMT transition cells' (PMID: 39775038, PMID: 39968688).

In certain cancers or fibrotic diseases, epithelial cells can transition into a mesenchymal phenotype, contributing to the stromal environment that supports tumor growth or tissue remodeling (PMID: 20572012).

(8) CD44 is shown in Fig. 2D but the text mentions CD45 (line 159)?

In Fig 2D, T cells are defined as a cluster of CD45+CD3+ cells, further subdivided into CD4+ and CD8+ T cells based on their expression of CD4 and CD8. This figure does not include data on CD44.

(9) All quantification experiments (of stainings etc) should be in detail described how this was done. It looks very difficult (almost not feasible) when looking at the provided pictures to count the stained cells.

a. Manual Measurement:

For TEM-observed pinopodes, glycogen particles, microvilli, and cilia, manual region-of-interest (ROI) selection was performed using ImageJ software for quantitative analysis of counts, area, and length. Twenty randomly selected images per experimental group were analyzed for each morphological parameter.

b. Automated Measurement:

We quantified the fluorescence images using ImageJ. Firstly, preprocess them by adjusting brightness and contrast, and removing background noise with the “Subtract Background” feature.

Secondly, set the threshold to highlight the cells, then select the regions of interest (ROI) using selection tools. Thirdly, as for counting the cells, navigate to Analyze > Analyze Particles. AS for measuring the influence intensity and area, set the “Measurement” options as mean gray value. Adjust parameters as needed, and view results in the “Results” window. Save the data for further analysis and ensure consistency throughout your measurements for reliable results.

For 3D fluorescence quantification, ZEN software (Carl Zeiss) was exclusively used, with 11 images analyzed per experimental group. This part has been incorporated into “Supporting Information”

Line 94-100.

c. Normalization Method：

For fluorescence quantification, DAPI was used as an internal reference for normalization, where both DAPI and target fluorescence channel intensities were quantified simultaneously. The normalized target signal intensity (target/DAPI ratio) was then compared across experimental groups. A minimum of 15 images were analyzed for each parameter per group. This part has been incorporated into “Supporting Information” Line 101-104.

(10) Fig. 3C: it is unclear how quantification can be reliably done. Moreover, OLFM4 looks positive in all cells of Ctrl, but authors still see an increase?

(a) Fluorescence images were quantitatively analyzed using ImageJ by measuring the mean gray values. For normalization, DAPI staining served as an internal reference, with simultaneous measurement of mean gray values in both the target fluorescence channel and the DAPI channel. The relative fluorescence intensity was then calculated as the ratio of target channel to DAPI signal for inter-group quantitative comparisons.

(b) OLFM4 is an E2-responsive gene. Its expression in endometrial organoids of the CTRL group is physiologically normal (PMID: 31666317). However, its fluorescence intensity (quantified as mean gray value) was significantly stronger in both the SEC and WOI groups compared to the CTRL group (quantitative method as described above).

(11) Fig. 3F: Met is downregulated which is not in accordance with the mentioned activation of the PI3K-AKT pathway.

We appreciate your careful review. Our initial description was imprecise. In the revised manuscript, this statement has been removed entirely.

(12) Lines 222-226: transcriptome and proteome differences are not significant; so, how meaningful are the results then? Then, it is very hard to conclude an evolution from secretory phase to WoI.

We appreciate your feedback. The manuscript has been comprehensively revised, and the aforementioned content has been removed.

(13) WoI organoids show an increased number of cilia. However, some literature shows the opposite, i.e. less ciliated cells in the endometrial lining at WoI (to keep the embryo in place). How to reconcile?

Thank you for raising this question. We conducted a statistical analysis of the proportion of ciliated cells across endometrial phases.

(a) Based on the 2020 study by Stephen R. Quake and Carlos Simon’s team published in Nature Medicine (PMID: 32929266), the mid-secretory phase (Days 19–23) exhibited a higher proportion of ciliated cells compared to the early-secretory (Days 15–18) and late-secretory phases (Days 24– 28) (Fig. R13 A).

(b) According to the 2021 study by Roser Vento-Tormo’s team in Nature Genetics, ciliated cell abundance peaked in the early-to-mid-secretory endometrium across all phases (Fig. R13 B-C).

Data were sourced from the Reproductive Cell Atlas.

(14) How are pinopodes distinguished from microvilli? Moreover, Fig. 3 does not show the typical EM structure of cilia.

Thank you for this insightful question.

(a) Pinopodes are large, bulbous protrusions with a smooth apical membrane. Under transmission electron microscopy (TEM), it can be observed that the pinopodes contain various small particles, which are typically extracellular fluid and dissolved substances.

Microvilli are elongated, finger-like projections that typically exhibit a uniform and orderly arrangement, forming a "brush border" structure. Under transmission electron microscopy, dense components of the cytoskeleton, such as microfilaments and microtubules, can be seen at the base of the microvilli.

(b) You may refer to the ciliated TEM structure shown in the current manuscript's Fig. 2E (originally labeled as Fig. 2H in the draft). The cilium is composed of microtubules. The cross-section shows that the periphery of the cilium is surrounded by nine pairs of microtubules arranged in a ring. The longitudinal section shows that the cilium has a long cylindrical structure, with the two central microtubules being quite prominent and located at the center of the cilium.

(15) There is a recently published paper demonstrating another model for implantation. This paper should be referenced as well (Shibata et al. Science Advances, 2024).

Thanks for your valuable comments. We have cited this reference in the manuscript at Line 77-78.

(16) Line 78: two groups were the first here (Turco and Borreto) and should both be mentioned.

Thanks for your valuable comments. We have cited this reference in the manuscript at Line 74-76.

(17) Line 554: "as an alternative platform" - alternative to what? Authors answer reviewers' comments by just changing one word, but this makes the text odd.

Thank you for your review. Here, we propose that this WOI organoid serves as an alternative research platform for studying endometrial receptivity and maternal-fetal interactions, compared to current secretory-phase organoids. In the revised manuscript, we have supplemented the data by co-culturing this WOI organoid with blastoid, demonstrating its robust embryo implantation potential.

Reviewer #2 (Public Review):

In this research, Zhang et al. have pioneered the creation of an advanced organoid culture designed to emulate the intricate characteristics of endometrial tissue during the crucial Window of Implantation (WOI) phase. Their method involves the incorporation of three distinct hormones into the organoid culture, coupled with additives that replicate the dynamics of the menstrual cycle. Through a series of assays, they underscore the striking parallels between the endometrial tissue present during the WOI and their crafted organoids. Through a comparative analysis involving historical endometrial tissue data and control organoids, they establish a system that exhibits a capacity to simulate the intricate nuances of the WOI. The authors made a commendable effort to address the majority of the statements. Developing an endometrial organoid culture methodology that mimics the window of implantation is a game-changer for studying the implantation process. However, the authors should strive to enhance the results to demonstrate how different WOI organoids are from SEC organoids, ensuring whether they are worth using in implantation studies, or a proper demonstration using implantation experiments.

Thank you for your valuable suggestions. The WOI organoids differ from SEC organoids in the following aspects.

(1) Structurally, WOI endometrial organoids exhibit subcellular features characteristic of the implantation window: densely packed pinopodes on the luminal side of epithelial cells, abundant glycogen granules, elongated and tightly arranged microvilli, and increased cilia (Figure 2F).

(2) At the molecular level, WOI organoids show enlarged and functionally active mitochondria, enhanced ciliary assembly and motility, and single-cell signatures resembling mid-secretory endometrium.

Specifically, mitochondrial- and cilia-related genes/proteins are most highly expressed in WOI organoids (Figure 4A,B). TEM analysis revealed that WOI organoids have the largest average mitochondrial area (Figure 4C). Mitochondrial-related genes display an increasing trend across the three organoid groups, and WOI organoids produce more ATP and IL-8 (Figure 4D,E).

For cilia, WOI organoids upregulate genes/proteins involved in ciliary assembly, basal bodies, and motile cilia, while downregulating non-motile cilia markers (Figure 5A-C).

Single-cell analysis further confirms that WOI organoids recapitulate mid-secretory endometrial traits in mitochondrial metabolism and cell adhesion (Figure 2G).

(3) Functionally, WOI organoids demonstrate superior embryo implantation potential. Given the scarcity and ethical constraints of human embryos, we used blastoids for implantation assays (Figure 6A). These blastoids successfully grew within endometrial organoids, established interactions (Figure 6B), and exhibited normal trilineage differentiation (epiblast: OCT4; hypoblast: GATA6; trophoblast: KRT18) (Figure 6C). WOI organoids achieved significantly higher blastoid survival (66% vs. 19% in CTRL and 28% in SEC) and interaction rates (90% vs. 47% in CTRL and 53% in SEC), confirming their robust embryo-receptive capacity (Figure 6D,E).

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

In conclusion, it is needed to first meet all the concerns of the reviewers and then submit an appropriately adapted and comprehensive paper (also showing the robustness of the "organoids" and functionality of the findings) instead of this still fully descriptive paper. Further comments are included in the rebuttal document of the authors and will be provided by the editor as PDF.

Reviewer #2 (Recommendations For The Authors):

The authors made a good effort to reply all the statements. However, there are some points that the authors need to address.

• There is an inconsistency in the manuscript regarding the number of passages in which the organoids are used; in the response to the reviewers, it mentions 5 passages, while in the Materials and Methods section, it states 3 passages.

We sincerely appreciate your thorough review. In this study, organoids within the first three passages were used. To address the reviewer's question comprehensively, we have now provided a detailed account of the organoid passage history in our response.

• We agree that the difference between SEC and WOI organoids may be subtle, but in response to this, the authors should explain what they mean by "the most notable differences lie in the more comprehensive differentiation and varied cellular functions exhibited by WOI organoids..."

In the original manuscript, this statement indicated that, at the single-cell level, WOI endometrial organoids exhibited more functionally mature and thoroughly differentiated characteristics compared to SEC endometrial organoids (See details below).

In the revised version, we have restructured this section to focus on following aspects: hormone response, energy metabolism, ciliary assembly and motility, epithelial-mesenchymal transition, and embryo implantation potential. Consequently, the "the most notable differences lie in the more comprehensive differentiation and varied cellular functions exhibited by WOI organoids..."has been removed.

(1) Varied cellular functions:

a. Secretory Epithelium: Compared to SEC organoids, WOI organoids exhibit enhanced peptide metabolism and mitochondrial energy metabolism in their secretory epithelium, supporting endometrial decidualization and embryo implantation (Figure 3F).

b. Proliferative Epithelium: Compared to SEC organoids, WOI organoids demonstrate enhanced GTPase activity, angiogenesis, cytoskeletal assembly, cell differentiation, and RAS protein signaling in their proliferative epithelium (Figure S2G).

c. Ciliated Epithelium: The ciliated epithelium of WOI endometrial organoids is associated with the regulation of vascular development and exhibits higher transcriptional activity compared to SEC organoids (Figure 5E).

d. Stromal Cells: Compared to SEC organoids, WOI organoids exhibit enhanced cell junctions, cell migration, and cytoskeletal regulation in EMT-derived stromal cells (Figure S4A right panel). Similarly, cell junctions are also strengthened in stromal cells (Figure S4A left panel).

(2) comprehensive differentiation:

a. Compared to SEC organoids, WOI organoids exhibit more complete differentiation from proliferative epithelium to secretory epithelium (Figure 3G).

b. The WOI organoids demonstrate more robust ciliary differentiation compared to SEC organoids (Figure 5F).

c. The proliferative epithelium progressively differentiates into EMT-derived cells. Compared to SEC organoids, WOI organoids are predominantly localized at the terminal end of the differentiation trajectory, indicating more complete differentiation (Figure S4B).

• What do the authors mean by "average intensity" when referring to the extra reagents added to the WOI? The results that the authors show in response to Reviewer 2's Q1 must be included as part of the results and explain how it was done in the materials and methods section.

This parameter indicates the growth status of organoids. It measures the gray value of organoids through long-term live-cell tracking. When organoids undergo apoptosis, they progressively condense into denser solid spheres, leading to an increase in gray value (average intensity). This content has been incorporated into the Results section (Line 129) and is further explained in the Supporting Information "Materials and Methods" (Lines 70-77).

• In panel 1C, it is not possible to see the stromal cells around because they are brightfield images.

You are partly right. Bright-field images alone indeed make it difficult to distinguish stromal cells. However, by combining whole-mount immunofluorescence staining with the characteristic elongated spindle-shaped morphology of stromal cells, we were able to roughly determine their distribution in the bright-field images.

• Responding to Reviewer 2's question Q7, the authors indicate how they establish the cluster. However, they do not specify whether they extrapolate the data from a database or create the cluster themselves based on the literature. It should be stated from which classification list (or classification database) the extrapolation has been made.

Within endometrial biology, stromal cells in the transition from epithelial to mesenchymal phenotype are specifically referred to as 'stromal EMT transition cells' (PMID: 39775038, PMID: 39968688).

In certain cancers or fibrotic diseases, epithelial cells can transition into a mesenchymal phenotype, contributing to the stromal environment that supports tumor growth or tissue remodeling (PMID: 20572012).

• Regarding Reviewer 2's question Q8, if the authors have not been able to make comparisons with, at least, SEC organoids, unfortunately, the ERT loses much of its strength and should not serve as support.

We agree with you at this point. These results have been moved to the supplementary figures.

• If the differences in the transcriptome and proteome between SEC and WOI organoids are not significant, the result does not support the authors' model. If there are barely any differences at the proteome and transcriptome level between SEC and WOI organoids, why would anyone choose to use their model over SEC organoids?

We sincerely appreciate your valuable feedback. In this revised manuscript, we have further integrated transcriptomic and proteomic analyses, revealing that WOI organoids exhibit enlarged and functionally active mitochondria, along with enhanced cilia assembly and motility compared to SEC organoids. Additionally, using a blastoid model, we demonstrated that WOI organoids possess superior embryo implantation potential, significantly outperforming SEC organoids. Our research group aims to develop an embryo co-culture model. Through systematic comparisons of structural, molecular, and co-culture characteristics between SEC and WOI organoids, we ultimately confirmed the superior performance of WOI organoids.

• SEC and WOI organoids must be different enough to establish a new model, and the authors do not demonstrate that they are.

Thank you for your valuable feedback. In the revised manuscript, we have emphasized the distinctions between SEC and WOI organoids in terms of structure, molecular characteristics, and functionality (co-culture with blastoid), as detailed below.

(1) Structurally, WOI endometrial organoids exhibit subcellular features characteristic of the implantation window: densely packed pinopodes on the luminal side of epithelial cells, abundant glycogen granules, elongated and tightly arranged microvilli, and increased cilia (Figure 2F).

(2) At the molecular level, WOI organoids show enlarged and functionally active mitochondria, enhanced ciliary assembly and motility, and single-cell signatures resembling mid-secretory endometrium.

Specifically, mitochondrial- and cilia-related genes/proteins are most highly expressed in WOI organoids (Figure 4A,B). TEM analysis revealed that WOI organoids have the largest average mitochondrial area (Figure 4C). Mitochondrial-related genes display an increasing trend across the three organoid groups, and WOI organoids produce more ATP and IL-8 (Figure 4D,E).

For cilia, WOI organoids upregulate genes/proteins involved in ciliary assembly, basal bodies, and motile cilia, while downregulating non-motile cilia markers (Figure 5A-C).

Single-cell analysis further confirms that WOI organoids recapitulate mid-secretory endometrial traits in mitochondrial metabolism and cell adhesion (Figure 2G).

(3) Functionally, WOI organoids demonstrate superior embryo implantation potential. Given the scarcity and ethical constraints of human embryos, we used blastoids for implantation assays (Figure 6A). These blastoids successfully grew within endometrial organoids, established interactions (Figure 6B), and exhibited normal trilineage differentiation (epiblast: OCT4; hypoblast: GATA6; trophoblast: KRT18) (Figure 6C). WOI organoids achieved significantly higher blastoid survival (66% vs. 19% in CTRL and 28% in SEC) and interaction rates (90% vs. 47% in CTRL and 53% in SEC), confirming their robust embryo-receptive capacity (Figure 6D,E).

• Regarding Q16, Boretto et al. 2017 and Turco et al. 2017 also manage to isolate stromal cells, but they lose them between passages. It's not a matter of isolating them from the tissue or not, but rather how they justify their maintenance in culture. In the images added by the authors, it can be seen that the majority of stromal cells are lost from P0 to P1 after thawing. I still believe that the epithelial part can be passed and maintained, but the rest cannot, and that should be mentioned in the paper as a limitation. However, the authors can demonstrate the maintenance of stromal cells by performing immunostaining with vimentin from passages 4, 5, and 6.

Thank you for your valuable comments. We have added the statement 'Stromal cells and immune cells are difficult to pass down stably and their proportion is lower than that in the in vivo endometrium' to the Limitations section (Line 364-365). Additionally, we performed immunostaining with vimentin starting from passage 6 and confirmed the presence of Vimentin+ F-actin+ stromal cells (as shown in Author response image 1).

Author response:

The following is the authors’ response to the original reviews.

eLife assessment

This study presents a new and valuable theoretical account of spatial representational drift in the hippocampus. The evidence supporting the claims is convincing, with a clear and accessible explanation of the phenomenon. Overall, this study will likely attract researchers exploring learning and representation in both biological and artificial neural networks.

We would like to ask the reviewers to consider elevating the assessment due to the following arguments. As noted in the original review, the study bridges two different fields (machine learning and neuroscience), and does not only touch a single subfield (representational drift in neuroscience). In the revision, we also analysed data from four different labs, strengthening the evidence and the generality of the conclusions.

Public Reviews:

Reviewer #1 (Public Review):

The authors start from the premise that neural circuits exhibit "representational drift" -- i.e., slow and spontaneous changes in neural tuning despite constant network performance. While the extent to which biological systems exhibit drift is an active area of study and debate (as the authors acknowledge), there is enough interest in this topic to justify the development of theoretical models of drift.

The contribution of this paper is to claim that drift can reflect a mixture of "directed random motion" as well as "steady state null drift." Thus far, most work within the computational neuroscience literature has focused on the latter. That is, drift is often viewed to be a harmless byproduct of continual learning under noise. In this view, drift does not affect the performance of the circuit nor does it change the nature of the network's solution or representation of the environment. The authors aim to challenge the latter viewpoint by showing that the statistics of neural representations can change (e.g. increase in sparsity) during early stages of drift. Further, they interpret this directed form of drift as "implicit regularization" on the network.

The evidence presented in favor of these claims is concise. Nevertheless, on balance, I find their evidence persuasive on a theoretical level -- i.e., I am convinced that implicit regularization of noisy learning rules is a feature of most artificial network models. This paper does not seem to make strong claims about real biological systems. The authors do cite circumstantial experimental evidence in line with the expectations of their model (Khatib et al. 2022), but those experimental data are not carefully and quantitatively related to the authors' model.

We thank the reviewer for pushing us to present stronger experimental evidence. We now analysed data from four different labs. Two of those are novel analyses of existing data (Karlsson et al, Jercog et al). All datasets show the same trend - increasing sparsity and increasing information per cell. We think that the results, presented in the new figure 3, allow us to make a stronger claim on real biological systems.

To establish the possibility of implicit regularization in artificial networks, the authors cite convincing work from the machine-learning community (Blanc et al. 2020, Li et al., 2021). Here the authors make an important contribution by translating these findings into more biologically plausible models and showing that their core assumptions remain plausible. The authors also develop helpful intuition in Figure 4 by showing a minimal model that captures the essence of their result.

We are glad that these translation efforts are appreciated.

In Figure 2, the authors show a convincing example of the gradual sparsification of tuning curves during the early stages of drift in a model of 1D navigation. However, the evidence presented in Figure 3 could be improved. In particular, 3A shows a histogram displaying the fraction of active units over 1117 simulations. Although there is a spike near zero, a sizeable portion of simulations have greater than 60% active units at the end of the training, and critically the authors do not characterize the time course of the active fraction for every network, so it is difficult to evaluate their claim that "all [networks] demonstrated... [a] phase of directed random motion with the low-loss space." It would be useful to revise the manuscript to unpack these results more carefully. For example, a histogram of log(tau) computed in panel B on a subset of simulations may be more informative than the current histogram in panel A.

The previous figure 3A was indeed confusing. In particular, it lumped together many simulations without proper curation. We redid this figure (now Figure 4), and added supplementary figures (Figures S1, S2) to better explain our results. It is now clear that the simulations with a large number of active units were either due to non-convergence, slow timescale of sparsification or simulations featuring label noise in which the fraction of active units is less affected. Regarding the log(tau) calculation, while it could indeed be an informative plot, it could not be calculated in a simple manner for all simulations. This is because learning curves are not always exponential, but sometimes feature initial plateaus (see also Saxe et al 2013, Schuessler et al 2020). We added a more detailed explanation of this limitation in the methods section, and we believe the current figure exemplifies the effect in a satisfactory manner.

Reviewer #2 (Public Review):

Summary:

In the manuscript "Representational drift as a result of implicit regularization" the authors study the phenomenon of representational drift (RD) in the context of an artificial network that is trained in a predictive coding framework. When trained on a task for spatial navigation on a linear track, they found that a stochastic gradient descent algorithm led to a fast initial convergence to spatially tuned units, but then to a second very slow, yet directed drift which sparsified the representation while increasing the spatial information. They finally show that this separation of timescales is a robust phenomenon and occurs for a number of distinct learning rules.

Strengths:

This is a very clearly written and insightful paper, and I think people in the community will benefit from understanding how RD can emerge in such artificial networks. The mechanism underlying RD in these models is clearly laid out and the explanation given is convincing.

We thank the reviewer for the support.

Weaknesses:

It is unclear how this mechanism may account for the learning of multiple environments.

There are two facets to the topic of multiple environments. First, are the results of the current paper relevant when there are multiple environments? Second, what is the interaction between brain mechanisms of dealing with multiple environments and the results of the current paper?

We believe the answer to the first question is positive. The near-orthogonality of representations between environments implies that changes in one can happen without changes in the other. This is evident, for instance, in Khatib et al and Geva et al - in both cases, drift seems to happen independently in two environments, even though they are visited intermittently and are visually similar.

The second question is a fascinating one, and we are planning to pursue it in future work. While the exact way in which the brain achieves this near-independence is an open question, remapping is one possible window into this process.

We extended the discussion to make these points clear.

The process of RD through this mechanism also appears highly non-stationary, in contrast to what is seen in familiar environments in the hippocampus, for example.

The non-stationarity noted by the reviewer is indeed a major feature of our observations, and is indeed linked to familiarity. We divide learning into three phases (now more clearly stated in Table 1 and Figure 4C). The first, rapid phase, consists of improvement of performance - corresponding to initial familiarity with the environment. The third phase, often reported in the literature of representational drift, is indeed stationary and obtained after prolonged familiarity. Our work focuses on the second phase, which is not as immediate as the first one, and can take several days. We note in the discussion that experiments which include a long familiarization process can miss this phase (see also Table 3). Furthermore, we speculate that real life is less stationary than a lab environment, and this second phase might actually be more relevant there.

Reviewer #3 (Public Review):

Summary:

Single-unit neural activity tuned to environmental or behavioral variables gradually changes over time. This phenomenon, called representational drift, occurs even when all external variables remain constant, and challenges the idea that stable neural activity supports the performance of well-learned behaviors. While a number of studies have described representational drift across multiple brain regions, our understanding of the underlying mechanism driving drift is limited. Ratzon et al. propose that implicit regularization - which occurs when machine learning networks continue to reconfigure after reaching an optimal solution - could provide insights into why and how drift occurs in neurons. To test this theory, Ratzon et al. trained a Feedforward Network trained to perform the oft-utilized linear track behavioral paradigm and compare the changes in hidden layer units to those observed in hippocampal place cells recorded in awake, behaving animals.

Ratzon et al. clearly demonstrate that hidden layer units in their model undergo consistent changes even after the task is well-learned, mirroring representational drift observed in real hippocampal neurons. They show that the drift occurs across three separate measures: the active proportion of units (referred to as sparsification), spatial information of units, and correlation of spatial activity. They continue to address the conditions and parameters under which drift occurs in their model to assess the generalizability of their findings.

However, the generalizability results are presented primarily in written form: additional figures are warranted to aid in reproducibility.

We added figures, and a Github with all the code to allow full reproducibility.

Last, they investigate the mechanism through which sparsification occurs, showing that the flatness of the manifold near the solution can influence how the network reconfigures. The authors suggest that their findings indicate a three-stage learning process: 1) fast initial learning followed by 2) directed motion along a manifold which transitions to 3) undirected motion along a manifold.

Overall, the authors' results support the main conclusion that implicit regularization in machine learning networks mirrors representational drift observed in hippocampal place cells.

We thank the reviewer for this summary.

However, additional figures/analyses are needed to clearly demonstrate how different parameters used in their model qualitatively and quantitatively influence drift.

We now provide additional figures regarding parameters (Figures S1, S2).

Finally, the authors need to clearly identify how their data supports the three-stage learning model they suggest.

Their findings promise to open new fields of inquiry into the connection between machine learning and representational drift and generate testable predictions for neural data.

Strengths:

(1) Ratzon et al. make an insightful connection between well-known phenomena in two separate fields: implicit regularization in machine learning and representational drift in the brain. They demonstrate that changes in a recurrent neural network mirror those observed in the brain, which opens a number of interesting questions for future investigation.

(2) The authors do an admirable job of writing to a large audience and make efforts to provide examples to make machine learning ideas accessible to a neuroscience audience and vice versa. This is no small feat and aids in broadening the impact of their work.

(3) This paper promises to generate testable hypotheses to examine in real neural data, e.g., that drift rate should plateau over long timescales (now testable with the ability to track single-unit neural activity across long time scales with calcium imaging and flexible silicon probes). Additionally, it provides another set of tools for the neuroscience community at large to use when analyzing the increasingly high-dimensional data sets collected today.

We thank the reviewer for these comments. Regarding the hypotheses, these are partially confirmed in the new analyses we provide of data from multiple labs (new Figure 3 and Table 3) - indicating that prolonged exposure to the environment leads to more stationarity.

Weaknesses:

(1) Neural representational drift and directed/undirected random walks along a manifold in ML are well described. However, outside of the first section of the main text, the analysis focuses primarily on the connection between manifold exploration and sparsification without addressing the other two drift metrics: spatial information and place field correlations. It is therefore unclear if the results from Figures 3 and 4 are specific to sparseness or extend to the other two metrics. For example, are these other metrics of drift also insensitive to most of the Feedforward Network parameters as shown in Figure 3 and the related text? These concerns could be addressed with panels analogous to Figures 3a-c and 4b for the other metrics and will increase the reproducibility of this work.

We note that the results from figures 3 and 4 (original manuscript) are based on abstract tasks, while in figure 2 there is a contextual notion of spatial position. Spatial position metrics are not applicable to the abstract tasks as they are simple random mapping of inputs, and there isn’t necessarily an underlying latent variable such as position. This transition between task types is better explained in the text now. In essence the spatial information and place field correlation changes are simply signatures of the movements in parameter space. In the abstract tasks their change becomes trivial, as the spatial information becomes strongly correlated with sparsity and place fields are simply the activity vectors of units. These are guaranteed to change as long as there are changes in the activity statistics. We present here the calculation of these metrics averaged over simulations for completeness.

Author response image 1.

PV correlation between training time points averaged over 362 simulations. (B) Mean SI of units normalized to first time step, averaged over 362 simulations. Red line shows the average time point of loss convergence, the shaded area represents one standard deviation.

(2) Many caveats/exceptions to the generality of findings are mentioned only in the main text without any supporting figures, e.g., "For label noise, the dynamics were qualitatively different, the fraction of active units did not reduce, but the activity of the units did sparsify" (lines 116-117). Supporting figures are warranted to illustrate which findings are "qualitatively different" from the main model, which are not different from the main model, and which of the many parameters mentioned are important for reproducing the findings.

We now added figures (S1, S2) that show this exactly. We also added a github to allow full reproduction.

(3) Key details of the model used by the authors are not listed in the methods. While they are mentioned in reference 30 (Recanatesi et al., 2021), they need to be explicitly defined in the methods section to ensure future reproducibility.

The details of the simulation are detailed in the methods sections. We also added a github to allow full reproducibility.

(4) How different states of drift correspond to the three learning stages outlined by the authors is unclear. Specifically, it is not clear where the second stage ends, and the third stage begins, either in real neural data or in the figures. This is compounded by the fact that the third stage - of undirected, random manifold exploration - is only discussed in relation to the introductory Figure 1 and is never connected to the neural network data or actual brain data presented by the authors. Are both stages meant to represent drift? Or is only the second stage meant to mirror drift, while undirected random motion along a manifold is a prediction that could be tested in real neural data? Identifying where each stage occurs in Figures 2C and E, for example, would clearly illustrate which attributes of drift in hidden layer neurons and real hippocampal neurons correspond to each stage.

Thanks for this comment, which urged us to better explain these concepts.

The different processes (reduction in loss, reduction in Hessian) happen in parallel with different timescales. Thus, there are no sharp transitions between the phases. This is now explained in the text in relation to figure 4C, where the approximate boundaries are depicted.

The term drift is often used to denote a change in representation without a change in behavior. In this sense, both the second and third phases correspond to drift. Only the third stage is stationary. This is now emphasized in the text and in the new Table 1. Regarding experimental data, apart from the new figure 3 with four datasets, we also summarize in Table 3 the relation between duration of familiarity and stationarity of the data.

Recommendations for the authors:

The reviewers have raised several concerns. They concur that the authors should address the specific points below to enhance the manuscript.

(1) The three different phases of learning should be clearly delineated, along with how they are determined. It remains unclear in which exact phase the drift is observed.

This is now clearly explained in the new Table 1 and Figure 4C. Note that the different processes (reduction in loss, reduction in Hessian) happen in parallel with different timescales. Thus, there are no sharp transitions between the phases. This is now explained in the text in relation to figure 4C, where the approximate boundaries are depicted.

The term drift is often used to denote a change in representation without a change in behavior. In this sense, both the second and third phases correspond to drift. Only the third stage is stationary. This is now emphasized in the text and in the new Table 1. Regarding experimental data, apart from the new figure 3 with four datasets, we also summarize in Table 3 the relation between duration of familiarity and stationarity of the data.

(2) The term "sparsification" of unit activity is not fully clear. Its meaning should be more explicitly explained, especially since, in the simulations, a significant number of units appear to remain active (Fig. 3A).

We now define precisely the two measures we use - Active Fraction, and Fraction Active Units. There is a new section with an accompanying figure in the Methods section. As Figure S2 shows, the noise statistics (label noise vs. update noise) differentially affects these two measures.

(3) While the study primarily focuses on one aspect of representational drift-the proportion of active units-it should also explore other features traditionally associated with representational drift, such as spatial information and the correlation between place fields.

This absence of features is related to the abstract nature of some of the tasks simulated in our paper. In our original submission the transition between a predictive coding task to more abstract tasks was not clearly explained, creating some confusion regarding the measured metrics. We now clarified the motivation for this transition.

Both the initial simulation and the new experimental data analysis include spatial information (Figures 2,3). The following simulations (Figure 4) with many parameter choices use more abstract tasks, for which the notion of correlation between place cells and spatial information loses its meaning as there is no spatial ordering of the inputs, and every input is encountered only once. Spatial information becomes strongly correlated with the inverse of the active fraction metric. The correlation between place cells is also directly linked to increase in sparseness for these tasks.

(4) There should be a clearer illustration of how labeling noise influences learning dynamics and sparsification.

This was indeed confusing in the original submission. We removed the simulations with label noise from Figure 4, and added a supplementary figure (S2) illustrating the different effects of label noise.

(5) The representational drift observed in this study's simulations appears to be nonstationary, which differs from in vivo reports. The reasons for this discrepancy should be clarified.

We added experimental results from three additional labs demonstrating a change in activity statistics (i.e. increase in spatial information and increase in sparseness) over a long period of time. We suggest that such a change long after the environment is already familiar is an indication for the second phase, and stress that this change seems to saturate at some point, and that most drift papers start collecting data after this saturation, hence this effect was missed in previous in vivo reports. Furthermore, these effects are become more abundant with the advent on new calcium imaging methods, as the older electrophysiological regording methods did not usually allow recording of large amounts of cells for long periods of time. The new Table 3 surveys several experimental papers, emphasizing the degree of familiarity with the environment.

(6) A distinctive feature of the hippocampus is its ability to learn different spatial representations for various environments. The study does not test representational drift in this context, a topic of significant interest to the community. Whether the authors choose to delve into this is up to them, but it should at least be discussed more comprehensively, as it's only briefly touched upon in the current manuscript version.

There are two facets to the topic of multiple environments. First, are the results of the current paper relevant when there are multiple environments? Second, what is the interaction between brain mechanisms of dealing with multiple environments and the results of the current paper?

We believe the answer to the first question is positive. The near-orthogonality of representations between environments implies that changes in one can happen without changes in the other. This is evident, for instance, in Khatib et al and Geva et al - in both cases, drift seems to happen independently in two environments, even though they are visited intermittently and are visually similar.

The second question is a fascinating one, and we are planning to pursue it in future work. While the exact way in which the brain achieves this near-independence is an open question, remapping is one possible window into this process.

We extended the discussion to make these points clear.

(7) The methods section should offer more details about the neural nets employed in the study. The manuscript should be explicit about the terms "hidden layer", "units", and "neurons", ensuring they are defined clearly and not used interchangeably..

We changed the usage of these terms to be more coherent and made our code publicly available. Specifically, “units” refer to artificial networks and “neurons” to biological ones.

In addition, each reviewer has raised both major and minor concerns. These are listed below and should be addressed where possible.

Reviewer #1 (Recommendations For The Authors):

I recommend that the authors edit the text to soften their claims. For example:

In the abstract "To uncover the underlying mechanism, we..." could be changed to "To investigate, we..."

Agree. Done

On line 21, "Specifically, recent studies showed that..." could be changed to "Specifically, recent studies suggest that..."

Agree. Done

On line 100, "All cases" should probably be softened to "Most cases" or more details should be added to Figure 3 to support the claim that every simulation truly had a phase of directed random motion.

The text was changed in accordance with the reviewer’s suggestion. In addition, the figure was changed and only includes simulations in which we expected unit sparsity to arise (without label noise). We also added explanations and supplementary figures for label noise.

Unless I missed something obvious, there is no new experimental data analysis reported in the paper. Thus, line 159 of the discussion, "a phenomenon we also observed in experimental data" should be changed to "a phenomenon that recently reported in experimental data."

We thank the reviewer for drawing our attention to this. We now analyzed data from three other labs, two of which are novel analyses on existing data. All four datasets show the same trends of sparseness with increasing spatial information. The new Figure 3 and text now describe this.

On line 179 of the Discussion, "a family of network configurations that have identical performance..." could be softened to "nearly identical performance." It would be possible for networks to have minuscule differences in performance that are not detected due to stochastic batch effects or limits on machine precision.

The text was changed in accordance with the reviewer’s suggestion.

Other minor comments:

Citation 44 is missing the conference venue, please check all citations are formatted properly.

Corrected.

In the discussion on line 184, the connection to remapping was confusing to me, particularly because the cited reference (Sanders et al. 2020) is more of a conceptual model than an artificial network model that could be adapted to the setting of noisy learning considered in this paper. How would an RNN model of remapping (e.g. Low et al. 2023; Remapping in a recurrent neural network model of navigation and context inference) be expected to behave during the sparsifying portion of drift?

We now clarified this section. The conceptual model of Sanders et al includes a specific prediction (Figure 7 there) which is very similar to ours - a systematic change in robustness depending on duration of training. Regarding the Low et al model, using such mechanistic models is an exciting avenue for future research.

Reviewer #2 (Recommendations For The Authors):

I only have two major questions.

(1) Learning multiple representations: Memory systems in the brain typically must store many distinct memories. Certainly, the hippocampus, where RD is prominent, is involved in the ongoing storage of episodic memories. But even in the idealized case of just two spatial memories, for example, two distinct linear tracks, how would this learning process look? Would there be any interference between the two learning processes or would they be largely independent? Is the separation of time scales robust to the number of representations stored? I understand that to answer this question fully probably requires a research effort that goes well beyond the current study, but perhaps an example could be shown with two environments. At the very least the authors could express their thoughts on the matter.

There are two facets to the topic of multiple environments. First, are the results of the current paper relevant when there are multiple environments? Second, what is the interaction between brain mechanisms of dealing with multiple environments and the results of the current paper?

We believe the answer to the first question is positive. The near-orthogonality of representations between environments implies that changes in one can happen without changes in the other. This is evident, for instance, in Khatib et al and Geva et al - in both cases, drift seems to happen independently in two environments, even though they are visited intermittently and are visually similar.

The second question is a fascinating one, and we are planning to pursue it in future work. While the exact way in which the brain achieves this near-independence is an open question, remapping is one possible window into this process.

We extended the discussion to make these points clear.

(2) Directed drift versus stationarity: I could not help but notice that the RD illustrated in Fig.2D is not stationary in nature, i.e. the upper right and lower left panels are quite different. This appears to contrast with findings in the hippocampus, for example, Fig.3e-g in (Ziv et al, 2013). Perhaps it is obvious that a directed process will not be stationary, but the authors note that there is a third phase of steady-state null drift. Is the RD seen there stationary? Basically, I wonder if the process the authors are studying is relevant only as a novel environment becomes familiar, or if it is also applicable to RD in an already familiar environment. Please discuss the issue of stationarity in this context.

The non-stationarity noted by the reviewer is indeed a major feature of our observations, and is indeed linked to familiarity. We divide learning into three phases (now more clearly stated in Table 1 and Figure 4C). The first, rapid, phase consists of improvement of performance - corresponding to initial familiarity with the environment. The third phase, often reported in the literature of representational drift, is indeed stationary and obtained after prolonged familiarity. Our work focuses on the second phase, which is not as immediate as the first one, and can take several days. We note in the discussion that experiments which include a long familiarization process can miss this phase (see also Table 3). Furthermore, we speculate that real life is less stationary than a lab environment, and this second phase might actually be more relevant there.

Reviewer #3 (Recommendations For The Authors):

Most of my general recommendations are outlined in the public review. A large portion of my comments regards increasing clarity and explicitly defining many of the terms used which may require generating more figures (to better illustrate the generality of findings) or modifying existing figures (e.g., to show how/where the three stages of learning map onto the authors' data).

Sparsification is not clearly defined in the main text. As I read it, sparsification is meant to refer to the activity of neurons, but this needs to be clearly defined. For example, lines 262-263 in the methods define "sparseness" by the number of active units, but lines 116-117 state: "For label noise, the dynamics were qualitatively different, the fraction of active units did not reduce, but the activity of the units did sparsify." If the fraction of active units (defined as "sparseness") did not change, what does it mean that the activity of the units "sparsified"? If the authors mean that the spatial activity patterns of hidden units became more sharply tuned, this should be clearly stated.

We now defined precisely the two measures we use - Active Fraction, and Fraction Active Units. There is a new section with an accompanying figure in the Methods section. As Figure S2 shows, the noise statistics (label noise vs. update noise) differentially affects these two measures.

Likewise, it is unclear which of the features the authors outlined - spatial information, active proportion of units, and spatial correlation - are meant to represent drift. The authors should clearly delineate which of these three metrics they mean to delineate drift in the main text rather than leave it to the reader to infer. While all three are mentioned early on in the text (Figure 2), the authors focus more on sparseness in the last half of the text, making it unclear if it is just sparseness that the authors mean to represent drift or the other metrics as well.

The main focus of our paper is on the non-stationarity of drift. Namely that features (such as these three) systematically change in a directed manner as part of the drift process. This is in The new analyses of experimental data show sparseness and spatial information.

The focus on sparseness in the second half of the paper is because we move to more abstract These are also easy to study in the more abstract tasks in the second part of the paper. In our original submission the transition between a predictive coding task to more abstract tasks was not clearly explained, creating some confusion regarding the measured metrics. We now clarified the motivation for this transition.

It is not clear if a change in the number of active units alone constitutes "drift", especially since Geva et al. (2023) recently showed that both changes in firing rate AND place field location drive drift, and that the passage of time drives changes in activity rate (or # cells active).

Our work did not deal with purely time-dependent drift, but rather focused on experience-dependence. Furthermore, Geva et al study the stationary phase of drift, where we do not expect a systematic change in the total number of cells active. They report changes in the average firing rate of active cells in this phase, as a function of time - which does not contradict our findings.

"hidden layer", "units", and "neurons" seem to be used interchangeably in the text (e.g., line 81-85). However, this is confusing in several places, in particular in lines 83-85 where "neurons" is used twice. The first usage appears to refer to the rate maps of the hidden layer units simulated by the authors, while the second "neurons" appears to refer to real data from Ziv 2013 (ref 5). The authors should make it explicit whether they are referring to hidden layer units or actual neurons to avoid reader confusion.

We changed the usage of these terms to be more coherent. Specifically, “units” refer to artificial networks and “neurons” to biological ones.

The authors should clearly illustrate which parts of their findings support their three-phase learning theory. For example, does 2E illustrate these phases, with the first tenth of training time points illustrating the early phase, time 0.1-0.4 illustrating the intermediate phase, and 0.4-1 illustrating the last phase? Additionally, they should clarify whether the second and third stages are meant to represent drift, or is it only the second stage of directed manifold exploration that is considered to represent drift? This is unclear from the main text.

The different processes (reduction in loss, reduction in Hessian) happen in parallel with different timescales. Thus, there are no sharp transitions between the phases. This is now explained in the text in relation to figure 4C, where the approximate boundaries are depicted.

The term drift is often used to denote a change in representation without a change in behavior. In this sense, both the second and third phases correspond to drift. Only the third stage is stationary. This is now emphasized in the text and in the new Table 1. Regarding experimental data, apart from the new figure 3 with four datasets, we also summarize in Table 3 the relation between duration of familiarity and stationarity of the data.

Line 45 - It appears that the acronym ML is not defined above here anywhere.

Added.

Line 71: the ReLU function should be defined in the text, e.g., sigma(x) = x if x > 0 else 0.

Added.

106-107: Figures (or supplemental figures) to demonstrate how most parameters do not influence sparsification dynamics are warranted. As written, it is unclear what "most parameters" mean - all but noise scale. What about the learning rule? Are there any interactions between parameters?

We now removed the label noise from Figure 4, and added two supplementary figures to clearly explain the effect of parameters. Figure 4 itself was also redone to clarify this issue.

2F middle: should "change" be omitted for SI?

The panel was replaced by a new one in Figure 3.

116-119: A figure showing how results differ for label noise is warranted.

This is now done in Figure S1, S2.

124: typo, The -> the

Corrected.

127-129: This conclusion statement is the first place in the text where the three stages are explicitly outlined. There does not appear to be any support or further explanation of these stages in the text above.

We now explain this earlier at the end of the Introduction section, along with the new Table 1 and marking on Figure 4C.

132-133 seems to be more of a statement and less of a prediction or conclusion - do the authors mean "the flatness of the loss landscape in the vicinity of the solution predicts the rate of sparsification?"

We thank the reviewer for this observation. The sentence was rephrased:

Old: As illustrated in Fig. 1, different solutions in the zero-loss manifold might vary in some of their properties. The specific property suggested from theory is the flatness of the loss landscape in the vicinity of the solution.

New: As illustrated in Fig. 1, solutions in the zero-loss manifold have identical loss, but might vary in some of their properties. The authors of [26] suggest that noisy learning will slowly increase the flatness of the loss landscape in the vicinity of the solution.

135: typo, it's -> its

Corrected.

Line 135-136 "Crucially, the loss on the 136 entire manifold is exactly zero..." This appears to contradict the Figure 4A legend - the loss appears to be very high near the top and bottom edges of the manifold in 4A. Do the authors mean that the loss along the horizontal axis of the manifold is zero?

The reviewer is correct. The manifold mentioned in the sentence is indeed the horizontal axis. We changed the text and the figure to make it clearer.

Equation 6: This does not appear to agree with equation 2 - should there be an E_t term for an expectation function?

Corrected.

Line 262-263: "Sparseness means that a unit has become inactive for all inputs." This should also be stated explicitly as the definition of sparseness/sparsification in the main text.

We now define precisely the two measures we use - Active Fraction, and Fraction Active Units. There is a new section with an accompanying figure in the Methods section. As Figure S2 shows, the noise statistics (label noise vs. update noise) differentially affects these two measures.

Author response:

The following is the authors’ response to the current reviews.

Public Reviews:

Reviewer #1 (Public review):

I applaud the authors' for providing a thorough response to my comments from the first round of review. The authors' have addressed the points I raised on the interpretation of the behavioral results as well as the validation of the model (fit to the data) by conducting new analyses, acknowledging the limitations where required and providing important counterpoints. As a result of this process, the manuscript has considerably improved. I have no further comments and recommend this manuscript for publication.

We are pleased that our revisions have addressed all the concerns raised by Reviewer #1.

Reviewer #2 (Public review):

Summary:

This manuscript proposes that the use of a latent cause model for assessment of memory-based tasks may provide improved early detection in Alzheimer's Disease as well as more differentiated mapping of behavior to underlying causes. To test the validity of this model, the authors use a previously described knock-in mouse model of AD and subject the mice to several behaviors to determine whether the latent cause model may provide informative predictions regarding changes in the observed behaviors. They include a well-established fear learning paradigm in which distinct memories are believed to compete for control of behavior. More specifically, it's been observed that animals undergoing fear learning and subsequent fear extinction develop two separate memories for the acquisition phase and the extinction phase, such that the extinction does not simply 'erase' the previously acquired memory. Many models of learning require the addition of a separate context or state to be added during the extinction phase and are typically modeled by assuming the existence of a new state at the time of extinction. The Niv research group, Gershman et al. 2017, have shown that the use of a latent cause model applied to this behavior can elegantly predict the formation of latent states based on a Bayesian approach, and that these latent states can facilitate the persistence of the acquisition and extinction memory independently. The authors of this manuscript leverage this approach to test whether deficits in production of the internal states, or the inference and learning of those states, may be disrupted in knock-in mice that show both a build-up of amyloid-beta plaques and a deterioration in memory as the mice age.

Strengths:

I think the authors' proposal to leverage the latent cause model and test whether it can lead to improved assessments in an animal model of AD is a promising approach for bridging the gap between clinical and basic research. The authors use a promising mouse model and apply this to a paradigm in which the behavior and neurobiology are relatively well understood - an ideal situation for assessing how a disease state may impact both the neurobiology and behavior. The latent cause model has the potential to better connect observed behavior to underlying causes and may pave a road for improved mapping of changes in behavior to neurobiological mechanisms in diseases such as AD.

The authors also compare the latent cause model to the Rescorla-Wagner model and a latent state model allowing for better assessment of the latent cause model as a strong model for assessing reinstatement.

Weaknesses:

I have several substantial concerns which I've detailed below. These include important details on how the behavior was analyzed, how the model was used to assess the behavior, and the interpretations that have been made based on the model.

(1) There is substantial data to suggest that during fear learning in mice separate memories develop for the acquisition and extinction phases, with the acquisition memory becoming more strongly retrieved during spontaneous recovery and reinstatement. The Gershman paper, cited by the authors, shows how the latent causal model can predict this shift in latent causes by allowing for the priors to decay over time, thereby increasing the posterior of the acquisition memory at the time of spontaneous recovery. In this manuscript, the authors suggest a similar mechanism of action for reinstatement, yet the model does not appear to return to the acquisition memory after reinstatement, at least based on the simulation and examples shown in figures 1 and 3. More specifically, in figure 1, the authors indicate that the posterior probability of the latent cause,z_A (the putative acquisition memory), increases, partially leading to reinstatement. This does not appear to be the case as test 3 (day 36) appears to have similar posterior probabilities for z_A as well as similar weights for the CS as compared to the last days of extinction. Rather, the model appears to mainly modify the weights in the most recent latent cause, z_B - the putative the 'extinction state', during reinstatement. The authors suggest that previous experimental data have indicated that spontaneous recovery or reinstatement effects are due to an interaction of the acquisition and extinction memory. These studies have shown that conditioned responding at a later time point after extinction is likely due to a balance between the acquisition memory and the extinction memory, and that this balance can shift towards the acquisition memory naturally during spontaneous recovery, or through artificial activation of the acquisition memory or inhibition of the extinction memory (see Lacagnina et al. for example). Here the authors show that the same latent cause learned during extinction, z_B, appears to dominate during the learning phase of reinstatement, with rapid learning to the context - the weight for the context goes up substantially on day 35 - in z_B. This latent cause, z_B, dominates at the reinstatement test, and due to the increased associative strength between the context and shock, there is a strong CR. For the simulation shown in figure 1, it's not clear why a latent cause model is necessary for this behavior. This leads to the next point.

We would like to first clarify that our behavioral paradigm did not last for 36 days, as noted by the reviewer. Our reinstatement paradigm contained 7 phases and 36 trials in total: acquisition (3 trials), test 1 (1 trial), extinction 1 (19 trials), extinction 2 (10 trials), test 2 (1 trial), unsignaled shock (1 trial), test 3 (1 trial). The day is labeled under each phase in Figure 2A. 

We have provided explanations on how the reinstatement is explained by the latent cause model in the first round of the review. Briefly, both acquisition and extinction latent causes contribute to the reinstatement (test 3). The former retains the acquisition fear memory, and the latter has the updated w_context from unsignaled shock. Although the reviewer is correct that the z_B in Figure 1D makes a great contribution during the reinstatement, we would like to argue that the elevated CR from test 2 (trial 34) to test 3 (trial 36) is the result of the interaction between z_A and z_B.

We provided Author response image 1 using the same data in Figure 1D and 1E to further clarify this point. The posterior probability of z_A increased after an unsignaled shock (trial 35), which may be attributed to the return of acquisition fear memory. The posterior probability of z_A then decreased again after test 3 (trial 36) because there was no shock in this trial. Along with the weight change, the expected shock change substantially in these three trials, resulting in reinstatement. Note that the mapping of expected shock to CR in the latent cause model is controlled by parameter θ and λ. Once the expected shock exceeds the threshold θ, the CR will increase rapidly if λ is smaller.

Lastly, accepting the idea that separate memories are responsible for acquisition and extinction in the memory modification paradigm, the latent cause model (LCM) is a rational candidate modeling this idea. Please see the following reply on why a simple model like the Rescorla-Wagner (RW) model is not sufficient to fully explain the behaviors observed in this study.

Author response image 1.

The sum posterior probability (A), the sum of associative weight of CS (B), and the sum of associative weight of context (C) of acquisition and extinction latent causes in Figure 1D and 1E.

(2) The authors compared the latent cause model to the Rescorla-Wagner model. This is very commendable, particularly since the latent cause model builds upon the RW model, so it can serve as an ideal test for whether a more simplified model can adequately predict the behavior. The authors show that the RW model cannot successfully predict the increased CR during reinstatement (Appendix figure 1). Yet there are some issues with the way the authors have implemented this comparison:

(2A) The RW model is a simplified version of the latent cause model and so should be treated as a nested model when testing, or at a minimum, the number of parameters should be taken into account when comparing the models using a method such as the Bayesian Information Criterion, BIC.

We acknowledge that the number of parameters was not taken into consideration when we compared the models. We thank the reviewer for the suggestion to use the Bayesian Information Criterion (BIC). However, we did not use BIC in this study for the following reasons. We wanted a model that can explain fear conditioning, extinction and reinstatement, so our first priority is to fit the test phases. Models that simulate CRs well in non-test phases can yield lower BIC values even if they fail to capture reinstatement. When we calculate the BIC by using the half normal distribution (μ = 0, σ \= 0.3) as the likelihood for prediction error in each trial, the BIC of the 12-month-old control is -37.21 for the RW model (Appendix 1–figure 1C) and -11.60 for the LCM (Figure 3C). Based on this result, the RW model would be preferred, yet the LCM was penalized by the number of parameters, even though it fit better in trial 36. Because we did not think this aligned with our purpose to model reinstatement, we chose to rely on the practical criteria to determine whether the estimated parameter set is accepted or not for our purpose (see Materials and Methods). The number of accepted samples can thus roughly be seen as the model's ability to explain the data in this study. These exclusion criteria then created imbalances in accepted samples across models (Appendix 1–figure 2). In the RW model, only one or two samples met the criteria, preventing meaningful statistical comparisons of BIC within each group. Overall, though we agreed that BIC is one of the reasonable metrics in model comparison, we did not think it aligns with our purpose in this study.

(2B) The RW model provides the associative strength between stimuli and does not necessarily require a linear relationship between V and the CR. This is the case in the original RW model as well as in the LCM. To allow for better comparison between the models, the authors should be modeling the CR in the same manner (using the same probit function) in both models. In fact, there are many instances in which a sigmoid has been applied to RW associative strengths to predict CRs. I would recommend modeling CRs in the RW as if there is just one latent cause. Or perhaps run the analysis for the LCM with just one latent cause - this would effectively reduce the LCM to RW and keep any other assumptions identical across the models.

Regarding the suggestion to run the analysis using the LCM with one latent cause, we agree that this method is almost identical to the RW model, which is also mentioned in the original paper (Gershman et al., 2017). Importantly, it would also eliminate the RW model’s advantage of assigning distinct learning rates to different stimuli, highlighted in the next comment (2C).

We thank the reviewer for suggesting applying the transformation of associative strength (V) to CR as in the LCM. We examined this possibility by heuristically selecting parameter values to test how such a transformation would influence the RW model (Author response image 2A). Specifically, we set α_CS = 0.5, α_context \= 1, β = 1, and introduced the additional parameters θ and λ, as in the LCM. This parameter set is determined heuristically to address the reviewer’s concern about a higher learning rate of context. The dark blue line is the plain associative strength. The remaining lines are CR curves under different combinations of θ and λ.

Consistent with the reviewer’s comment, under certain parameter settings (θ \= 0.01, λ = 0.01), the extended RW model can reproduce higher CRs at test 3, thereby approximating the discrimination index observed in the 12-month-old control group. However, this modification changes the characteristics of CRs in other phases from those in the plain RW model. In the acquisition phase, the CRs rise more sharply. In the extinction phase, the CRs remain high when θ is small. Though changing λ can modulate the steepness, the CR curve is flat on the second day of the extinction phase, which does not reproduce the pattern in observed data (Figure 2B). These trade-offs suggest that the RW model with the sigmoid transformation does not improve fit quality and, in fact, sacrifices features that were well captured by simpler RW simulations (Appendix 1–figure 1A to 1D). To further evaluate this extended RW model (RW*), we applied the same parameter estimation method used in the LCM for individual data (see Materials and Methods). For each animal, α_CS, α_context, β, θ, and λ were estimated with their lower and upper bounds set as previously described (see Appendix 1, Materials and Methods). The results showed that the number of accepted samples slightly increased compared to the RW model without sigmoidal transformation of CR (RW* vs. RW in Author response image 2B, 2C). However, this improvement did not surpass the LCM (RW* vs. LCM in Author response image 2B, Author response image 1C). Overall, these results suggest that while using the same method to map the expected shock to CR, the RW model does not outperform the LCM. Practically, further extension, such as adding novel terms, might improve the fitting level. We would like to note that such extensions should be carefully validated if they are reasonable and necessary for an internal model, which is beyond the scope of this study. We hope this addresses the reviewer's concerns about the implementation of the RW model. 

Author response image 2.

Simulation (A) and parameter estimation (B and C) in the extended Rescorla-Wagner model.

(2C) In the paper, the model fits for the alphas in the RW model are the same across the groups. Were the alphas for the two models kept as free variables? This is an important question as it gets back to the first point raised. Because the modeling of the reinstatement behavior with the LCM appears to be mainly driven by latent cause z_B, the extinction memory, it may be possible to replicate the pattern of results without requiring a latent cause model. For example, the 12-month-old App NL-G-F mice behavior may have a deficit in learning about the context. Within the RW model, if the alpha for context is set to zero for those mice, but kept higher for the other groups, say alpha_context = 0.8, the authors could potentially observe the same pattern of discrimination indices in figure 2G and 2H at test. Because the authors don't explicitly state which parameters might be driving the change in the DI, the authors should show in some way that their results cannot simply be due to poor contextual learning in the 12 month old App NL-G-F mice, as this can presumably be predicted by the RW model. The authors' model fits using RW don't show this, but this is because they don't consider this possibility that the alpha for context might be disrupted in the 12-month-old App NL-G-F mice. Of course, using the RW model with these alphas won't lead to as nice of fits of the behavior across acquisition, extinction, and reinstatement as the authors' LCM, the number of parameters are substantially reduced in the RW model. Yet the important pattern of the DI would be replicated with the RW model (if I'm not mistaken), which is the important test for assessment of reinstatement.

We would like to clarify that we estimated three parameters in the RW model for individuals:  α_CS,  α_context, and β. Even if we did so, many samples did not satisfy our criteria (Appendix 1–figure 2). Please refer to the “Evaluation of model fit” in Appendix 1 and the legend of Appendix 1–figure 1A to 1D, where we have written the estimated parameter values.

We did not agree that paralyzing the contextual learning by setting  α_context  as 0 in the RW model can explain the CR curve of 12-month-old AD mice well. Specifically, the RW model cannot capture the between-day extinction dynamics (i.e., the increase in CR at the beginning of day 2 extinction)  and the higher CR at test 3 relative to test 2 (i.e., DI between test 3 and test 2 is greater than 0.5). In addition, because the context input (= 0.2) was relatively lower than the CS input (= 1), and there is only a single unsignaled shock trial, even setting  α_context = 1 results in only a limited increase in CR (Appendix 1–figure 1A to 1D; see also Author response image 2 9). Thus, the RW model cannot replicate the reinstatement effect or the critical pattern of discrimination index, even under conditions of stronger contextual learning.  

(3) As stated by the authors in the introduction, the advantage of the fear learning approach is that the memory is modified across the acquisition-extinction-reinstatement phases. Although perhaps not explicitly stated by the authors, the post-reinstatement test (test 3) is the crucial test for whether there is reactivation of a previously stored memory, with the general argument being that the reinvigorated response to the CS can't simply be explained by relearning the CS-US pairing, because re-exposure the US alone leads to increase response to the CS at test. Of course there are several explanations for why this may occur, particularly when also considering the context as a stimulus. This is what I understood to be the justification for the use of a model, such as the latent cause model, that may better capture and compare these possibilities within a single framework. As such, it is critical to look at the level of responding to both the context alone and to the CS. It appears that the authors only look at the percent freezing during the CS, and it is not clear whether this is due to the contextual-US learning during the US re-exposure or to increased responding to the CS - presumably caused by reactivation of the acquisition memory. The authors do perform a comparison between the preCS and CS period, but it is not clear whether this is taken into account in the LCM. For example, the instance of the model shown in figure 1 indicates that the 'extinction cause', or cause z6, develops a strong weight for the context during the reinstatement phase of presenting the shock alone. This state then leads to increased freezing during the final CS probe test as shown in the figure. If they haven't already, I think the authors must somehow incorporate these different phases (CS vs ITI) into their model, particularly since this type of memory retrieval that depends on assessing latent states is specifically why the authors justified using the latent causal model. In more precise terms, it's not clear whether the authors incorporate a preCS/ITI period each day the cue is presented as a vector of just the context in addition to the CS period in which the vector contains both the context and the CS. Based on the description, it seemed to me that they only model the CRs during the CS period on days when the CS is presented, and thereby the context is only ever modeled on its own (as just the context by itself in the vector) on extinction days when the CS is not presented. If they are modeling both timepoints each day that the CS I presented, then I would recommend explicitly stating this in the methods section.

In this study, we did not model the preCS freezing rate, and we thank the reviewer for the suggestion to model preCS periods as separate context-only trials. In our view, however, this approach is not consistent with the assumptions of the LCM. Our rationale is that the available periods of context and the CS are different. We assume that observation of the context lasts from preCS to CS. If we simulate both preCS (context) and CS (context and tone), the weight of context would be updated twice. Instead, we follow the same method as described in the original code from Gershman et al. (2017) to consider the context effect. We agree that explicitly modeling preCS could provide additional insights, but we believe it would require modifying or extending the LCM. We consider this an important direction for future research, but it is outside the scope of this study.

(4) The authors fit the model using all data points across acquisition and learning. As one of the other reviewers has highlighted, it appears that there is a high chance for overfitting the data with the LCM. Of course, this would result in much better fits than models with substantially fewer free parameters, such as the RW model. As mentioned above, the authors should use a method that takes into account the number of parameters, such as the BIC.

Please refer to the reply to public review (2A) for the reason we did not take the suggestion to use BIC. In addition, we feel that we have adequately addressed the concern of overfitting in the first round of the review. 

(5) The authors have stated that they do not think the Barnes maze task can be modeled with the LCM. Whether or not this is the case, if the authors do not model this data with the LCM, the Barnes maze data doesn't appear valuable to the main hypothesis. The authors suggest that more sophisticated models such as the LCM may be beneficial for early detection of diseases such as Alzheimer's, so the Barnes maze data is not valuable for providing evidence of this hypothesis. Rather, the authors make an argument that the memory deficits in the Barnes maze mimic the reinstatement effects providing support that memory is disrupted similarly in these mice. Although, the authors state that the deficits in memory retrieval are similar across the two tasks, the authors are not explicit as to the precise deficits in memory retrieval in the reinstatement task - it's a combination of overgeneralizing latent causes during acquisition, poor learning rate, over differentiation of the stimuli.

We would like to clarify that we valued the latent cause model not solely because it is more sophisticated and fits more data points, but it is an internal model that implicates the cognitive process. Please also see the reply to the recommendations to authors (3) about the reason why we did not take the suggestion to remove this data.

Reviewer #3 (Public review):

Summary:

This paper seeks to identify underlying mechanisms contributing to memory deficits observed in Alzheimer's disease (AD) mouse models. By understanding these mechanisms, they hope to uncover insights into subtle cognitive changes early in AD to inform interventions for early-stage decline.

Strengths:

The paper provides a comprehensive exploration of memory deficits in an AD mouse model, covering early and late stages of the disease. The experimental design was robust, confirming age-dependent increases in Aβ plaque accumulation in the AD model mice and using multiple behavior tasks that collectively highlighted difficulties in maintaining multiple competing memory cues, with deficits most pronounced in older mice.

In the fear acquisition, extinction, and reinstatement task, AD model mice exhibited a significantly higher fear response after acquisition compared to controls, as well as a greater drop in fear response during reinstatement. These findings suggest that AD mice struggle to retain the fear memory associated with the conditioned stimulus, with the group differences being more pronounced in the older mice.

In the reversal Barnes maze task, the AD model mice displayed a tendency to explore the maze perimeter rather than the two potential target holes, indicating a failure to integrate multiple memory cues into their strategy. This contrasted with the control mice, which used the more confirmatory strategy of focusing on the two target holes. Despite this, the AD mice were quicker to reach the target hole, suggesting that their impairments were specific to memory retrieval rather than basic task performance.

The authors strengthened their findings by analyzing their data with a leading computational model, which describes how animals balance competing memories. They found that AD mice showed somewhat of a contradiction: a tendency to both treat trials as more alike than they are (lower α) and similar stimuli as more distinct than they are (lower σx) compared to controls.

Weaknesses:

While conceptually solid, the model struggles to fit the data and to support the key hypothesis about AD mice's inability to retain competing memories. These issues are evident in Figure 3:

(1) The model misses trends in the data, including the gradual learning of fear in all groups during acquisition, the absence of a fear response at the start of the experiment, and the faster return of fear during reinstatement compared to the gradual learning of fear during acquisition. It also underestimates the increase in fear at the start of day 2 of extinction, particularly in controls.

(2) The model explains the higher fear response in controls during reinstatement largely through a stronger association to the context formed during the unsignaled shock phase, rather than to any memory of the conditioned stimulus from acquisition (as seen in Figure 3C). In the experiment, however, this memory does seem to be important for explaining the higher fear response in controls during reinstatement (as seen in Author Response Figure 3). The model does show a necessary condition for memory retrieval, which is that controls rely more on the latent causes from acquisition. But this alone is not sufficient, since the associations within that cause may have been overwritten during extinction. The Rescorla-Wagner model illustrates this point: it too uses the latent cause from acquisition (as it only ever uses a single cause across phases) but does not retain the original stimulus-shock memory, updating and overwriting it continuously. Similarly, the latent cause model may reuse a cause from acquisition without preserving its original stimulus-shock association.

These issues lead to potential overinterpretation of the model parameters. The differences in α and σx are being used to make claims about cognitive processes (e.g., overgeneralization vs. over differentiation), but the model itself does not appear to capture these processes accurately.

The authors could benefit from a model that better matches the data and captures the retention and retrieval of fear memories across phases. While they explored alternatives, including the Rescorla-Wagner model and a latent state model, these showed no meaningful improvement in fit. This highlights a broader issue: these models are well-motivated but may not fully capture observed behavior.

Conclusion:

Overall, the data support the authors' hypothesis that AD model mice struggle to retain competing memories, with the effect becoming more pronounced with age. While I believe the right computational model could highlight these differences, the current models fall short in doing so.

We thank the reviewer for the insightful comments. For the comments (1) and (2), please refer to our previous author response to comments #26 and #27. We recognize that the models tested in this study have limitations and, as noted, do not fully capture all aspects of the observed behavioral data. We see this as an important direction for future research and value the reviewer’s suggestions.

Recommendations for the authors:

Reviewer #2 (Recommendations for the authors):

I have maintained some of the main concerns included in the first round of reviews as I think they remain concerns with the new draft, even though the authors have included substantially more analysis of their data, which is appreciated. I particularly found the inclusion of the comparative modeling valuable, although I think the analysis comparing the models should be improved.

(1) This relates to point 1 in the public assessment or #16 in the response to reviewers from the authors. The authors raise the point that even a low posterior can drive behavioral expression (lines 361-365 in the response to authors), and so the acquisition latent cause may partially drive reinstatement. Yet in the stimulation shown in figure 1D, this does not seem to be the case. As I mentioned in the public response, in figure 1, the posteriors for z_A are similar on day 34 and day 36, yet only on day 36 is there a strong CR. At least in this example, it does not appear that z_A contributes to the increased responding from day 34 (test 2) to day 36 (test 3). There may be a slight increase in z1 in figure 3C, but the dominant change from day 34 to day 36 appears to be the increase in the posterior of z3 and the substantial increase in w3. The authors then cite several papers which have shown the shift in balance between what it is the putative acquisition memory and extinction memory (i.e. Lacagnina et al.). Yet I do not see how this modeling fits with most of the previous findings. For example, in the Lacagnina et al. paper, activation of the acquisition ensemble or inhibition of the extinction ensemble drives freezing, whereas the opposite pattern reduces freezing. What appears to be the pattern in the modeling in this paper is primarily learning of context in the extinction latent cause to predict the shock. As I mention in point 2C of the public review, it's not clear why this pattern of results would require a latent cause model. Would a high alpha for context and not the CS not give a similar pattern of results in the RW model? At least for giving similar results of the DIs in figure 2?

First, we would like to clarify that the x-axis in Figure 1D is labeled “Trial,” not “Day.” Please refer to the reply to public review (1), where we clarified the posterior probability of the latent cause from trials 34 to 36. Second, although we did not have direct neural circuit evidence in this study, we discussed the similarities between previous findings and the modeling in the first review. Briefly, our main point focuses on the interaction between acquisition and extinction memory. In other words, responses at different times arise from distinct internal states made up of competing memories. We assume that the reviewer expects a modeling result showing nearly full recovery of acquisition memory, which aligns with previous findings where optogenetic activation of the acquisition engram can partially mimic reinstatement (Zaki et al., 2022; see also the response to comment #12 in the first round of review). We acknowledge that such a modeling result cannot be achieved with the latent cause model and see it as a potential future direction for model improvement.

Please also refer to the reply to public review (2) about how a high alpha for context in the RW model cannot explain the pattern we observed in the reinstatement paradigm.

(2) This is related to point 3 in the public comments and #13 in the response to reviewers. I raised the question of comparing the preCS/ITI period with the CS period, but my main point was why not include these periods in the LCM itself as mentioned in more detail in point 3 in the current public review. The inclusion of the comparisons the authors performed helped, but my main point was that the authors could have a better measure of wcontext if they included the preCS period as a stimulus each day (when only the context is included in the stimulus). This would provide better estimates of wcontext. As stated in the public review, perhaps the authors did this, but my understanding of the methods this was not the case, rather, it seems the authors only included the CS period for CRs within the model (at least on days when the CS was present).

Please refer to the reply to public review (3) about the reason why we did not model the preCS freezing rate.

(3) This relates to point 4 in the public review and #15 and #24 in the response to authors. The authors have several points for why the two experiments are similar and how results may be extrapolated - lines 725-733. The first point is that associative learning is fundamental in spatial learning. I'm not sure that this broad connection between the two studies is particularly insightful for why one supports the other as associative learning is putatively involved in most behavioral tasks. In the second point about reversals, why not then use a reversal paradigm that would be easier to model with LCM? This data is certainly valuable and interesting, yet I don't think it's helpful for this paper to state qualitatively the similarities in the potential ways a latent cause framework might predict behavior on the Barnes maze. I would recommend that the authors either model the behavior with LCM, remove the experiment from the paper, or change the framing of the paper that LCM might be an ideal approach for early detection of dementia or Alzheimer's disease.

We would like to clarify that our aim was not to present the LCM as an ideal tool for early detection of AD symptoms. Rather, our focus is on the broader idea of utilizing internal models and estimating individual internal states in early-stage AD. Regarding using a reversal paradigm that would be easier to model with LCM, the most straightforward approach is to use another type of paradigm for fear conditioning, then to examine the extent to which similar behavioral characteristics are observed between paradigms within subjects. However, re-exposing the same mice to such paradigms is constrained by strong carry-over effects, limiting the feasibility of this experiment. Other behavioral tasks relevant to AD that avoid shock generally involve action selection for subsequent observation (Webster et al., 2014), which falls outside the structure of LCM. Our rationale for including the Barnes maze task is that spatial memory deficit is implicated in the early stage of AD, making it relevant for translational research. While we acknowledge that exact modeling of Barnes maze behavior would require a more sophisticated model (as discussed in the first round of review), our intention to use the reversal Barnes maze paradigm is to suggest a presumable memory modification learning in a non-fear conditioning paradigm. We also discussed whether similar deficits in memory modification could be observed across two behavioral tasks.

(4) Reviewer # mentioned that the change in pattern of behavior only shows up in the older mice questioning the clinical relevance of early detection. I do think this is a valid point and maybe should be addressed. There does seem to be a bit of a bump in the controls on day 23 that doesn't appear in the 6-month group. Perhaps this was initially a spontaneous recovery test indicated by the dotted vertical line? This vertical line does not appear to be defined in the figure 1 legend, nor in figures 2 and 3.

We would like to emphasize that the App^NL-G-F knock-in mouse is widely considered a model of early-stage AD, characterized by Aβ accumulation with little to no neurofibrillary tangle pathology or neuronal loss (see Introduction). By examining different ages, we can assess the contribution of both the amount and duration of Aβ accumulation as well as age-related factors. Modeling the deficit in the memory modification process in the older App^NL-G-F knock-in mice, we suggested a diverged internal state in early-stage AD in older age, and this does not diminish the relevance of the model for studying early cognitive changes in AD.

We would also like to clarify again that the x-axis in the figure is “Trial,” not “Day.” The vertical dashed lines in these figures indicate phase boundaries, and they were defined in the figure legend: in Figure 1C, “The vertical dashed lines separate the phases.”; in Figure 2B, “The dashed vertical line separates the extinction 1 and extinction 2 phases.”; in Figure 3, “The vertical dashed lines indicate the boundaries of phases.”

(5) Are the examples in figure 3 good examples? The example for the 12-month-old control shows a substantial increase in weights for the context during test 3, but not for the CS. Yet in the bar plots in Figure 4 G and H, this pattern seems to be different. The weights for the context appear to substantially drop in the "after extinction" period as compared to the "extinction" period. It's hard to tell the change from "extinction" to "after extinction" for the CS weights (the authors change the y-axis for the CS weights but not for the context weights from panels G to H).

We would like to clarify that in Figure 3C, the increase in weights for context is not presented during test 3 (trial 36), noted by the reviewer; rather, it is the unsignaled shock phase (trial 35).

We assumed that the reviewer might misunderstand that the labels on the left in Figure 4, “Acquisition”, “Extinction”, and “After extinction”, indicate the time point. However, the data shown in Figure 4C to 4H are all from the same time point: test 3 (trial 36). The grouping reflects the classification of latent causes based on the trial in which they were inferred. In addition, for Figures 4G and 4H, the y‐axis limits were not set identically because the data range for “Sum of w_CS” varied. This was done to ensure the visibility of all data points. In Figure 4, each dot represents one animal. Take Figure 3D as an example. The point in Figure 4G is the sum of w3 and w4 in trial 36, and the point in Figure 4H is w5 in trial 36, note that the subscript numerals indicate latent cause index. We hope this addresses the reviewer’s question about the difference between the two figures.

The following is the authors’ response to the original reviews

Reviewer #1 (Public review):

Summary:

The authors show certain memory deficits in a mouse knock-in model of Alzheimer's Disease (AD). They show that the observed memory deficits can be explained by a computational model, the latent cause model of associative memory. The memory tasks used include the fear memory task (CFC) and the 'reverse' Barnes maze. Research on AD is important given its known huge societal burden. Likewise, better characterization of the behavioral phenotypes of genetic mouse models of AD is also imperative to advance our understanding of the disease using these models. In this light, I applaud the authors' efforts.

Strengths:

(1) Combining computational modelling with animal behavior in genetic knock-in mouse lines is a promising approach, which will be beneficial to the field and potentially explain any discrepancies in results across studies as well as provide new predictions for future work.

(2) The authors' usage of multiple tasks and multiple ages is also important to ensure generalization across memory tasks and 'modelling' of the progression of the disease.

Weaknesses:

[#1] (1) I have some concerns regarding the interpretation of the behavioral results. Since the computational model then rests on the authors' interpretation of the behavioral results, it, in turn, makes judging the model's explanatory power difficult as well. For the CFC data, why do knock-in mice have stronger memory in test 1 (Figure 2C)? Does this mean the knock-in mice have better memory at this time point? Is this explained by the latent cause model? Are there some compensatory changes in these mice leading to better memory? The authors use a discrimination index across tests to infer a deficit in re-instatement, but this indicates a relative deficit in re-instatement from memory strength in test 1. The interpretation of these differential DIs is not straightforward. This is evident when test 1 is compared with test 2, i.e., the time point after extinction, which also shows a significant difference across groups, Figure 2F, in the same direction as the re-instatement. A clarification of all these points will help strengthen the authors' case.

We appreciate the reviewer for the critical comments. According to the latent cause framework, the strength of the memory is influenced by at least 2 parameters: associative weight between CS and US given a latent cause and posterior probability of the latent cause. The modeling results showed that a higher posterior probability of acquisition latent cause, but not higher associative weight, drove the higher test 1 CR in App^NL-G-F mice (Results and Discussion; Figure 4 – figure supplement 3B, 3C). In terms of posterior, we agree that App^NL-G-F mice have strong fear memory. On the other hand, this suggests that App^NL-G-F mice exhibited a tendency toward overgeneralization, favoring modification of old memories, which adversely affected the ability to retain competing memories. The strong memory in test 1 would be a compensatory effect of overgeneralization.    

To estimate the magnitude of reinstatement, at least, one would have to compare CRs between test 2 (extinction) and test 3 (reinstatement), as well as those between test 1 (acquisition) and test 3. These comparisons represent the extent to which the memory at the reinstatement is far from that in the extinction, and close to that in the acquisition. Since discrimination index (DI) has been widely used as a normalized measure to evaluate the extent to which the system can distinguish between two conditions, we applied DI consistently to behavioral and simulated data in the reinstatement experiment, and the behavioral data in the reversal Barnes maze experiment, allowing us to evaluate the discriminability of an agent in these experiments. In addition, we used DI to examine its correlation with estimated parameters, enabling us to explore how individual discriminability may relate to the internal state. We have already discussed the differences in DI between test 3 and test 1, as well as CR in test 1 between control and App^NL-G-F in the manuscript and further elaborated on this point in Line 232, 745-748.   

[#2] (2) I have some concerns regarding the interpretation of the Barnes maze data as well, where there already seems to be a deficit in the memory at probe test 1 (Figure 6C). Given that there is already a deficit in memory, would not a more parsimonious explanation of the data be that general memory function in this task is impacted in these mice, rather than the authors' preferred interpretation? How does this memory weakening fit with the CFC data showing stronger memories at test 1? While I applaud the authors for using multiple memory tasks, I am left wondering if the authors tried fitting the latent cause model to the Barnes maze data as well.

While we agree that the deficits shown in probe test 1 may imply impaired memory function in App^NL-G-F mice in this task, it would be difficult to explain this solely in terms of impairments in general memory function. The learning curve and the daily strategy changes suggested that App^NL-G-F mice would have virtually intact learning ability in the initial training phase (Figure 6B, 6F, Figure 6 – figure supplement 1 and 3). For the correspondence relationship between the reinstatement and the reversal Barnes maze learning from the aspect of memory modification process, please also see our reply to comment #24. We have explained why we did not fit the latent cause model to the Barnes maze data in the provisional response.

[#3] (3) Since the authors use the behavioral data for each animal to fit the model, it is important to validate that the fits for the control vs. experimental groups are similar to the model (i.e., no significant differences in residuals). If that is the case, one can compare the differences in model results across groups (Figures 4 and 5). Some further estimates of the performance of the model across groups would help.

We have added the residual (i.e., observed CR minus simulated CR) in Figure 3 – figure supplement 1D and 1E. The fit was similar between control and App^NL-G-F mice groups in the test trials, except test 3 in the 12-month-old group. The residual was significantly higher in the 12-month-old control mice than App^NL-G-F mice, suggesting the model underestimated the reinstatement in the control, yet the DI calculated from the simulated CR replicates the behavioral data (Figure 3 – figure supplement 1A to 1C). These results suggest that the latent cause model fits our data with little systematic bias such as an overestimation of CR for the control group in the reinstatement, supporting the validity of the comparisons in estimated parameters between groups. These results and discussion have been added in the manuscript Line 269-276.

One may notice that the latent cause model overestimated the CR in acquisition trials in all groups in Figure 3 – figure supplement 1D and 1E. We have discussed this point in the reply to comment #26, 34 questioned by reviewer 3.

[#4] (4) Is there an alternative model the authors considered, which was outweighed in terms of prediction by this model? 

Yes, we have further evaluated two alternative models: the Rescorla-Wagner (RW; Rescorla & Wagner, 1972) model and the latent state model (LSM; Cochran & Cisler, 2019). The RW model serves as a baseline, given its known limitations in explaining fear return after extinction. The LSM is another contemporary model that shares several concepts with the latent cause model (LCM) such as building upon the RW model, assuming a latent variable inferred by Bayes’ rule, and involving a ruminative update for memory modification. We evaluated the three models in terms of the prediction accuracy and reproducibility of key behavioral features. Please refer to the Appendix 1 for detailed methods and results for these two models.

As expected, the RW model fit well to the data till the end of extinction but failed to reproduce reinstatement (Appendix 1 – figure 1A to 1D). Due to a large prediction error in test 3, few samples met the acceptance criteria we set (Appendix 1 – figure 2 and 3A). Conversely, the LSM reproduced reinstatement, as well as gradual learning in acquisition and extinction phases, particularly in the 12month-old control (Appendix 1 – figure 1G). The number of accepted samples in the LSM was higher than in the RW model but generally lower than in the LCM (Appendix 1 – figure 2). The sum of prediction errors over all trials in the LSM was comparable to that in the LCM in the 6-month-old group (Appendix 1 – figure 4A), it was significantly lower in the 12-month-old group (Appendix 1 – figure 4B). Especially the LSM generated smaller prediction errors during the acquisition trials than in the LCM, suggesting that the LSM might be better at explaining the behaviors of acquisition (Appendix 1 – figure 4A and 4B; but see the reply for comment #34). While the LSM generated smaller prediction errors than the LCM in test 2 of the control group, it failed to replicate the observed DIs, a critical behavioral phenotype difference between control and App^NL-G-F mice (Appendix 1 – figure 6A to 6C; cf. Figure 2F to 2H, Figure 3 – figure supplement 1A to 1C).

Thus, although each model could capture different aspects of reinstatement, standing on the LCM to explain the reinstatement better aligns with our purpose. It should also be noted that we did not explore all parameter spaces of the LSM, hence we cannot rule out the possibility that alternative parameter sets could provide a better fit and explain the memory modification process well. A more comprehensive parameter search in the LSM may be a valuable direction for future research. 

[#5] One concern here is also parameter overfitting. Did the authors try leaving out some data (trials/mice) and predicting their responses based on the fit derived from the training data?

Following the reviewer’s suggestion, we confirmed if overfitting occurred using all trials to estimate parameters. Estimating parameters while actually leaving out trials would disorder the time lapse across trials, and thereby the prior of latent causes in each trial. Instead, we removed the constraint of prediction error by setting the error threshold to 1 for certain trials to virtually leave these trials out. We treated these trials as a virtual “training” dataset, while the rest of the trials were a “test” dataset. For the median CR data of each group (Figure 3), we estimated parameters under 6 conditions with unique training and test trials, then evaluated the prediction error for the training and test trials. Note that training and test trials were arbitrarily decided. Also, the error threshold for the acquisition trial was set to 1 as described in Materials and Methods, which we have further discussed the reason in the reply to comment #34 and treated acquisition trials separately from the test trials. We expect that the contribution of the data from the acquisition and test trials for parameter estimation could be discounted compared to those from the training trials with the constraint, and if overfitting occurred, the prediction error in the test data would be worse than that in the training trials.

Author response image 1A to 1F showed the simulated and observed CR under each condition, where acquisition trials were in light-shaded areas, test trials were in dark-shaded areas, and the rest of the trials were training trials. Author response image 1G showed mean squared prediction error across the acquisition, training and test trials under each condition. The dashed gray line showed the mean squared prediction error of training trials in Figure 3 as a baseline.

In conditions i and ii, where two or four trials in the extinction were used for training (Author response image 1A and 1B), the prediction error was generally higher in test trials than in training trials. In conditions iii and iv where ten trials in the extinction were used for training (Author response image 1C and 1D), the difference in prediction error between testing and training trials became smaller. These results suggest that providing more extinction trial data would reduce overfitting. In condition v (Author response image 1E), the results showed that using trials until extinction can predict reinstatement in control mice but not App^NL-G-F mice. Similarly, in condition vi (Author response image 1F), where test phase trials were left out, the prediction error differences were greater in App^NL-G-F mice. These results suggest that the test trials should be used for the parameter estimation to minimize prediction error for all groups. Overall, this analysis suggests that using all trials would reduce prediction error with few overfitting. 

Author response image 1.

Leaving trials out in parameter estimation in the latent cause model. (A – F) The observed CR (colored line) is the median freezing rate during the CS presentation over the mice within each group, which is the same as that in Figure 3. The colors indicate different groups: orange represents 6-month-old control, light blue represents 6-month-old App^NL-G-F mice, pink represents 12-month-old control, and dark blue represents 12-month-old App^NL-G-F mice. Under six different leave-out conditions (i – vi), parameters were estimated and used for generating simulated CR (gray line). In each condition, trials were categorized as acquisition (light-shaded area), training data (white area), and test data (dark-shaded area) based on the error threshold during parameter estimation. Only the error threshold of the test data trial was different from the original method (see Material and Method) and set to 1. In conditions i to vi, the number of test data trials is 27, 25, 19, and 19 in extinction phases. In condition v, the number of test data trials is 2 (trials 35 and 36). In condition vi, test data trials were the 3 test phases (trials 4, 34, and 36). (G) Each subplot shows the mean squared prediction error for the test data trial (gray circles), training data trial (white squares), and acquisition trial (gray triangles) in each group. The left y-axis corresponds to data from test and training trials, and the right y-axis corresponds to data from acquisition trials. The dashed line indicates the results calculated from Figure 3 as a baseline.  

Reviewer #1 (Recommendations for the authors):

Minor:

[#6] (1) I would like the authors to further clarify why 'explaining' the reinstatement deficit in the AD mouse model is important in working towards the understanding of AD i.e., which aspect of AD this could explain etc.

In this study, we utilized the reinstatement paradigm with the latent cause model as an internal model to illustrate how estimating internal states can improve understanding of cognitive alteration associated with extensive Aβ accumulation in the brain. Our findings suggest that misclassification in the memory modification process, manifesting as overgeneralization and overdifferentiation, underlies the memory deficit in the App^NL-G-F knock-in model mice. 

The parameters in the internal model associated with AD pathology (e.g., α and σ_x² in this study) can be viewed as computational phenotypes, filling the explanatory gap between neurobiological abnormalities and cognitive dysfunction in AD. This would advance the understanding of cognitive symptoms in the early stages of AD beyond conventional behavioral endpoints alone.

We further propose that altered internal states in App^NL-G-F knock-in mice may underlie a wide range of memory-related symptoms in AD as we observed that App^NL-G-F knock-in mice failed to retain competing memories in the reversal Barnes maze task. We speculate on how overgeneralization and overdifferentiation may explain some AD symptoms in the manuscript:

- Line 565-569: overgeneralization may explain deficits in discriminating highly similar visual stimuli reported in early-stage AD patients as they misclassify the lure as previously learned object

- Line 576-579: overdifferentiation may explain impaired ability to transfer previously learned association rules in early-stage AD patients as they misclassify them as separated knowledge. 

- Line 579-582: overdifferentiation may explain delusions in AD patients as an extended latent cause model could simulate the emergence of delusional thinking

We provide one more example here that overgeneralization may explain that early-stage AD patients are more susceptible to proactive interference than cognitively normal elders in semantic memory tests (Curiel Cid et al., 2024; Loewenstein et al., 2015, 2016; Valles-Salgado et al., 2024), as they are more likely to infer previously learned material. Lastly, we expect that explaining memory-related symptoms within a unified framework may facilitate future hypothesis generation and contribute to the development of strategies for detecting the earliest cognitive alteration in AD.  

[#7] (2) The authors state in the abstract/introduction that such computational modelling could be most beneficial for the early detection of memory disorders. The deficits observed here are pronounced in the older animals. It will help to further clarify if these older animals model the early stages of the disease. Do the authors expect severe deficits in this mouse model at even later time points?

The early stage of the disease is marked by abnormal biomarkers associated with Aβ accumulation and neuroinflammation, while cognitive symptoms are mild or absent. This stage can persist for several years during which the level of Aβ may reach a plateau. As the disease progresses, tau pathology and neurodegeneration emerge and drive the transition into the late stage and the onset of dementia. The App^NL-G-F knock-in mice recapitulate the features present in the early stage (Saito et al., 2014), where extensive Aꞵ accumulation and neuroinflammation worsen along with ages (Figure 2 – figure supplement 1). Since App^NL-G-F knock-in mice are central to Aβ pathology without tauopathy and neurodegeneration, it should be noted that it does not represent the full spectrum of the disease even at advanced ages. Therefore, older animals still model the early stages of the diseases and are suitable to study the long-term effect of Aβ accumulation and neuroinflammation. 

The age tested in previous reports using App^NL-G-F mice spanned a wide range from 2 months old to 24 months old. Different behavioral tasks have varied sensitivity but overall suggest the dysfunction worsens with aging (Bellio et al., 2024; Mehla et al., 2019; Sakakibara et al., 2018). We have tested the reinstatement experiment with 17-month-old App^NL-G-F mice before (Author response image 2). They showed more advanced deficits with the same trends observed in 12-month-old App^NL-G-F mice, but their freezing rates were overall at a lower level. There is a concern that possible hearing loss may affect the results and interpretation, therefore we decided to focus on 12-month-old data.

Author response image 2.

Freezing rate across reinstatement paradigm in the 17-month-old App^NL-G-F mice. Dashed and solid lines indicate the median freezing rate over 34 mice before (preCS) and during (CS) tone presentation, respectively. Red, blue, and yellow backgrounds represent acquisition, extinction, and unsignaled shock in Figure 2A. The dashed vertical line separates the extinction 1 and extinction 2 phases.

[#8] (3) There are quite a few 'marginal' p-values in the paper at p>0.05 but near it. Should we accept them all as statistically significant? The authors need to clarify if all the experimental groups are sufficiently powered.

For our study, we decided a priori that p < 0.05 would be considered statistically significant, as described in the Materials and Methods. Therefore, in our Results, we did not consider these marginal values as statistically significant but reported the trend, as they may indicate substantive significance.

We described our power analysis method in the manuscript Line 897-898 and have provided the results in Tables S21 and S22.

[#9] (4) The authors emphasize here that such computational modelling enables us to study the underlying 'reasoning' of the patient (in the abstract and introduction), I do not see how this is the case. The model states that there is a latent i.e. another underlying variable that was not previously considered.

Our use of the term “reasoning” was to distinguish the internal model, which describes how an agent makes sense of the world, from other generative models implemented for biomarker and disease progression prediction. However, we agree that using “reasoning” may be misleading and imprecise, so to reduce ambiguity we have removed this word in our manuscript Line 27: Nonetheless, internal models of the patient remain underexplored in AD; Line 85: However, previous approaches did not suppose an internal model of the world to predict future from current observation given prior knowledge.   

[#10] (5) The authors combine knock-in mice with controls to compute correlations of parameters of the model with behavior of animals (e.g. Figure 4B and Figure 5B). They run the risk of spurious correlations due to differences across groups, which they have indeed shown to exist (Figure 4A and 5A). It would help to show within-group correlations between DI and parameter fit, at least for the control group (which has a large spread of data).

We agree that genotype (control, App^NL-G-F) could be a confounder between the estimated parameters and DI, thereby generating spurious correlations. To address this concern, we have provided withingroup correlation in Figure 4 – figure supplement 2 for the 12-month-old group and Figure 5 – figure supplement 2 for the 6-month-old group.

In the 12-month-old group, the significant positive correlation between σx2 and DI remained in both control and App^NL-G-F mice even if we adjusted the genotype effect, suggesting that it is very unlikely that the correlations in Figure 4B are due to the genotype-related confounding. On the other hand, the positive correlation between α and DI was found to be significant in the control mice but not in the App^NL-G-F mice. Most of α were distributed around the lower bound in App^NL-G-F mice, which possibly reduced the variance and correlation coefficient. These results support our original conclusion that α and σ_x² are parameters associated with a lower magnitude of reinstatement in aged App^NL-G-F mice.

In the 6-month-old group, the correlations shown in Figure 5B were not preserved within subgroups, suggesting genotype would be a confounder for α, σ_x², and DI. We recognized that significant correlations in Figure 5B may arise from group differences, increased sample size, or greater variance after combining control and App^NL-G-F mice. 

Therefore, we concluded that α and σ_x² are associated with the magnitude of reinstatement but modulated by the genotype effect depending on the age. 

We have added interpretations of within-group correlation in the manuscript Line 307-308, 375-378.

[#11] (6) It is unclear to me why overgeneralization of internal states will lead to the animals having trouble recalling a memory. Would this not lead to overgeneralization of memory recall instead?

We assume that the reviewer is referring to “overgeneralization of internal states,” a case in which the animal’s internal state remained the same regardless of the observation, thereby leading to “overgeneralization of memory recall.” We agree that this could be one possible situation and appears less problematic than the case in which this memory is no longer retrievable. 

However, in our manuscript, we did not deal with the case of “overgeneralization of internal states”. Rather, our findings illustrated how the memory modification process falls into overgeneralization or overdifferentiation and how it adversely affects the retention of competing memories, thereby causing App^NL-G-F mice to have trouble recalling the same memory as the control mice. 

According to the latent cause model, retrieval failure is explained by a mismatch of internal states, namely when an agent perceives that the current cue does not match a previously experienced one, the old latent cause is less likely to be inferred due to its low likelihood (Gershman et al., 2017). For example, if a mouse exhibited higher CR in test 2, it would be interpreted as a successful fear memory retrieval due to overgeneralization of the fear memory. However, it reflects a failure of extinction memory retrieval due to the mismatch between the internal states at extinction and test 2. This is an example that overgeneralization of memory induces the failure of memory retrieval. 

On the other hand, App^NL-G-F mice exhibited higher CR in test 1, which is conventionally interpreted as a successful fear memory retrieval. When estimating their internal states, they would infer that their observation in test 1 well matches those under the acquisition latent causes, that is the overgeneralization of fear memory as shown by a higher posterior probability in acquisition latent causes in test 1 (Figure 4 – figure supplement 3). This is an example that over-generalization of memory does not always induce retrieval failure as we explained in the reply to comment #1. 

Reviewer #2 (Public review):

Summary:

This manuscript proposes that the use of a latent cause model for the assessment of memory-based tasks may provide improved early detection of Alzheimer's Disease as well as more differentiated mapping of behavior to underlying causes. To test the validity of this model, the authors use a previously described knock-in mouse model of AD and subject the mice to several behaviors to determine whether the latent cause model may provide informative predictions regarding changes in the observed behaviors. They include a well-established fear learning paradigm in which distinct memories are believed to compete for control of behavior. More specifically, it's been observed that animals undergoing fear learning and subsequent fear extinction develop two separate memories for the acquisition phase and the extinction phase, such that the extinction does not simply 'erase' the previously acquired memory. Many models of learning require the addition of a separate context or state to be added during the extinction phase and are typically modeled by assuming the existence of a new state at the time of extinction. The Niv research group, Gershman et al. 2017, have shown that the use of a latent cause model applied to this behavior can elegantly predict the formation of latent states based on a Bayesian approach, and that these latent states can facilitate the persistence of the acquisition and extinction memory independently. The authors of this manuscript leverage this approach to test whether deficits in the production of the internal states, or the inference and learning of those states, may be disrupted in knock-in mice that show both a build-up of amyloid-beta plaques and a deterioration in memory as the mice age.

Strengths:

I think the authors' proposal to leverage the latent cause model and test whether it can lead to improved assessments in an animal model of AD is a promising approach for bridging the gap between clinical and basic research. The authors use a promising mouse model and apply this to a paradigm in which the behavior and neurobiology are relatively well understood - an ideal situation for assessing how a disease state may impact both the neurobiology and behavior. The latent cause model has the potential to better connect observed behavior to underlying causes and may pave a road for improved mapping of changes in behavior to neurobiological mechanisms in diseases such as AD.

Weaknesses:

I have several substantial concerns which I've detailed below. These include important details on how the behavior was analyzed, how the model was used to assess the behavior, and the interpretations that have been made based on the model.

[#12] (1) There is substantial data to suggest that during fear learning in mice separate memories develop for the acquisition and extinction phases, with the acquisition memory becoming more strongly retrieved during spontaneous recovery and reinstatement. The Gershman paper, cited by the authors, shows how the latent causal model can predict this shift in latent states by allowing for the priors to decay over time, thereby increasing the posterior of the acquisition memory at the time of spontaneous recovery. In this manuscript, the authors suggest a similar mechanism of action for reinstatement, yet the model does not appear to return to the acquisition memory state after reinstatement, at least based on the examples shown in Figures 1 and 3. Rather, the model appears to mainly modify the weights in the most recent state, putatively the 'extinction state', during reinstatement. Of course, the authors must rely on how the model fits the data, but this seems problematic based on prior research indicating that reinstatement is most likely due to the reactivation of the acquisition memory. This may call into question whether the model is successfully modeling the underlying processes or states that lead to behavior and whether this is a valid approach for AD.

We thank the reviewer for insightful comments. 

We agree that, as demonstrated in Gershman et al. (2017), the latent cause model accounts for spontaneous recovery via the inference of new latent causes during extinction and the temporal compression property provided by the prior. Moreover, it was also demonstrated that even a relatively low posterior can drive behavioral expression if the weight in the acquisition latent cause is preserved. For example, when the interval between retrieval and extinction was long enough that acquisition latent cause was not dominant during extinction, spontaneous recovery was observed despite the posterior probability of acquisition latent cause (C1) remaining below 0.1 in Figure 11D of Gershman et al. (2017). 

In our study, a high response in test 3 (reinstatement) is explained by both acquisition and extinction latent cause. The former preserves the associative weight of the initial fear memory, while the latter has w_context learned in the unsignaled shock phase. These positive w were weighted by their posterior probability and together contributed to increased expected shock in test 3. Though the posterior probability of acquisition latent cause was lower than extinction latent cause in test 3 due to time passage, this would be a parallel instance mentioned above. To clarify their contributions to reinstatement, we have conducted additional simulations and the discussion in reply to the reviewer’s next comment (see the reply to comment #13).

We recognize that our results might appear to deviate from the notion that reinstatement results from the strong reactivation of acquisition memory, where one would expect a high posterior probability of the acquisition latent cause. However, we would like to emphasize that the return of fear emerges from the interplay of competing memories. Previous studies have shown that contextual or cued fear reinstatement involves a neural activity switch back to fear state in the medial prefrontal cortex (mPFC), including the prelimbic cortex and infralimbic cortex, and the amygdala, including ventral intercalated amygdala neurons (ITCv), medial subdivision of central nucleus of the amygdala (CeM), and the basolateral amygdala (BLA) (Giustino et al., 2019; Hitora-Imamura et al., 2015; Zaki et al., 2022). We speculate that such transition is parallel to the internal states change in the latent cause model in terms of posterior probability and associative weight change.

Optogenetic manipulation experiments have further revealed how fear and extinction engrams contribute to extinction retrieval and reinstatement. For instance, Gu et al. (2022) used a cued fear conditioning paradigm and found that inhibition of extinction engrams in the BLA, ventral hippocampus (vHPC), and mPFC after extinction learning artificially increased freezing to the tone cue. Similar results were observed in contextual fear conditioning, where silencing extinction engrams in the hippocampus dentate gyrus (DG) impaired extinction retrieval (Lacagnina et al., 2019). These results suggest that the weakening extinction memory can induce a return of fear response even without a reminder shock. On the other hand, Zaki et al. (2022) showed that inhibition of fear engrams in the BLA, DG, or hippocampus CA1 attenuated contextual fear reinstatement. However, they also reported that stimulation of these fear engrams was not sufficient to induce reinstatement, suggesting these fear engram only partially account for reinstatement. 

In summary, reinstatement likely results from bidirectional changes in the fear and extinction circuits, supporting our interpretation that both acquisition and extinction latent causes contribute to the reinstatement. Although it remains unclear whether these memory engrams represent latent causes, one possible interpretation is that w_context update in extinction latent causes during unsignaled shock indicates weakening of the extinction memory, while preservation of w in acquisition latent causes and their posterior probability suggests reactivation of previous fear memory. 

[#13] (2) As stated by the authors in the introduction, the advantage of the fear learning approach is that the memory is modified across the acquisition-extinction-reinstatement phases. Although perhaps not explicitly stated by the authors, the post-reinstatement test (test 3) is the crucial test for whether there is reactivation of a previously stored memory, with the general argument being that the reinvigorated response to the CS can't simply be explained by relearning the CS-US pairing, because re-exposure the US alone leads to increase response to the CS at test. Of course there are several explanations for why this may occur, particularly when also considering the context as a stimulus. This is what I understood to be the justification for the use of a model, such as the latent cause model, that may better capture and compare these possibilities within a single framework. As such, it is critical to look at the level of responding to both the context alone and to the CS. It appears that the authors only look at the percent freezing during the CS, and it is not clear whether this is due to the contextual US learning during the US re-exposure or to increased response to the CS - presumably caused by reactivation of the acquisition memory. For example, the instance of the model shown in Figure 1 indicates that the 'extinction state', or state z6, develops a strong weight for the context during the reinstatement phase of presenting the shock alone. This state then leads to increased freezing during the final CS probe test as shown in the figure. By not comparing the difference in the evoked freezing CR at the test (ITI vs CS period), the purpose of the reinstatement test is lost in the sense of whether a previous memory was reactivated - was the response to the CS restored above and beyond the freezing to the context? I think the authors must somehow incorporate these different phases (CS vs ITI) into their model, particularly since this type of memory retrieval that depends on assessing latent states is specifically why the authors justified using the latent causal model.

To clarify the contribution of context, we have provided preCS freezing rate across trials in Figure 2 – figure supplement 2. As the reviewer pointed out, the preCS freezing rate did not remain at the same level across trials, especially within the 12-month-old control and App^NL-G-F group (Figure 2 – figure supplement 2A and 2B), suggesting the effect context. A paired samples t-test comparing preCS freezing (Figure 2 – figure supplement 2E) and CS freezing (Figure 2E) in test 3 revealed significant differences in all groups: 6-month-old control, t(23) = -6.344, p < 0.001, d = -1.295; 6-month-old App^NL-G-F, t(24) = -4.679, p < 0.001, d = -0.936; 12-month-old control, t(23) = -4.512, p < 0.001, d = 0.921; 12-month-old App^NL-G-F, t(24) = -2.408, p = 0.024, d = -0.482. These results indicate that the response to CS was above and beyond the response to context only. We also compared the change in freezing rate (CS freezing rate minus preCS freezing rate) in test 2 and test 3 to examine the net response to the tone. The significant difference was found in the control group, but not in the App^NL-GF group (Author response image 3). The increased net response to the tone in the control group suggested that the reinstatement was partially driven by reactivation of acquisition memory, not solely by the contextual US learning during the unsignaled shock phase. We have added these results and discussion in the manuscript Line 220-231.

Author response image 3.

Net freezing rate in test 2 and test 3. Net freezing rate is defined as the CS freezing rate (i.e., freezing rate during 1 min CS presentation) minus the preCS freezing rate (i.e., 1 min before CS presentation). The dashed horizontal line indicates no freezing rate change from the preCS period to the CS presentation. *p < 0.05 by paired-sample Student’s t-test, and the alternative hypothesis specifies that test 2 freezing rate change is less than test 3. Colors indicate different groups: orange represents 6-month-old control (n = 24), light blue represents 6-month-old App^NL-G-F mice (n = 25), pink represents 12-month-old control (n = 24), and dark blue represents 12-month-old App^NL-G-F mice (n = 25). Each black dot represents one animal. Statistical results were as follows: t(23) = -1.927, p = 0.033, Cohen’s d = -0.393 in 6-month-old control; t(24) = -1.534, p = 0.069, Cohen’s d = -0.307 in 6-month-old App^NL-G-F; t(23) = -1.775, p = 0.045, Cohen’s d = -0.362 in 12-month-old control; t(24) = 0.86, p = 0.801, Cohen’s d = 0.172 in 12-monthold App^NL-G-F. 

According to the latent cause model, if the reinstatement is merely induced by an association between the context and the US in the unsignaled shock phase, the CR given context only and that given context and CS in test 3 should be equal. However, the simulation conducted for each mouse using their estimated parameters confirmed that this was not the case in this study. The results showed that simulated CR was significantly higher in the context+CS condition than in the context only condition (Author response image 4). This trend is consistent with the behavioral results we mentioned above.

Author response image 4.

Simulation of context effect in test 3. Estimated parameter sets of each sample were used to run the simulation that only context or context with CS was present in test 3 (trial 36). The data are shown as median with interquartile range, where white bars with colored lines represent CR for context only and colored bars represent CR for context with CS. Colors indicate different groups: orange represents 6-month-old control (n = 15), light blue represents 6-month-old App^NL-G-F mice (n = 12), pink represents 12-month-old control (n = 20), and dark blue represents 12-month-old App^NL-G-F mice (n = 18). Each black dot represents one animal. **p < 0.01, and ***p < 0.001 by Wilcoxon signed-rank test comparing context only and context + CS in each group, and the alternative hypothesis specifies that CR in context is not equal to CR in context with CS. Statistical results were as follows: W = 15, p = 0.008, effect size r = -0.66 in 6-month-old control; W = 0, p < 0.001, effect size r = -0.88 in 6-month-old App^NL-G-F; W = 25, p = 0.002, effect size r = -0.67 in 12-month-old control; W = 9, p = 0.002 , effect size r = -0.75 in 12-month-old App^NL-G-F. 

[#14] (3) This is related to the second point above. If the question is about the memory processes underlying memory retrieval at the test following reinstatement, then I would argue that the model parameters that are not involved in testing this hypothesis be fixed prior to the test. Unlike the Gershman paper that the authors cited, the authors fit all parameters for each animal. Perhaps the authors should fit certain parameters on the acquisition and extinction phase, and then leave those parameters fixed for the reinstatement phase. To give a more concrete example, if the hypothesis is that AD mice have deficits in differentiating or retrieving latent states during reinstatement which results in the low response to the CS following reinstatement, then perhaps parameters such as the learning rate should be fixed at this point. The authors state that the 12-month-old AD mice have substantially lower learning rate measures (almost a 20-fold reduction!), which can be clearly seen in the very low weights attributed to the AD mouse in Figure 3D. Based on the example in Figure 3D, it seems that the reduced learning rate in these mice is most likely caused by the failure to respond at test. This is based on comparing the behavior in Figures 3C to 3D. The acquisition and extinction curves appear extremely similar across the two groups. It seems that this lower learning rate may indirectly be causing most of the other effects that the authors highlight, such as the low σx, and the changes to the parameters for the CR. It may even explain the extremely high K. Because the weights are so low, this would presumably lead to extremely low likelihoods in the posterior estimation, which I guess would lead to more latent states being considered as the posterior would be more influenced by the prior.

We thank the reviewer for the suggestion about fitting and fixing certain parameters in different phases.

However, this strategy may not be optimal for our study for the following scientific reasons.

Our primary purpose is to explore internal states in the memory modification process that are associated with the deficit found in App^NL-G-F mice in the reinstatement paradigm. We did not restrict the question to memory retrieval, nor did we have a particular hypothesis such that only a few parameters of interest account for the impaired associative learning or structure learning in App^NL-G-F mice while all other parameters are comparable between groups. We are concerned that restricting questions to memory retrieval at the test is too parsimonious and might lead to misinterpretation of the results. As we explain in reply to comment #5, removing trials in extinction during parameter estimation reduces the model fit performance and runs the risk of overfitting within the individual. Therefore, we estimated all parameters for each animal, with the assumption that the estimated parameter set represents individual internal state (i.e., learning and memory characteristics) and should be fixed within the animal across all trials.  

Figure 3 is the parameter estimation and simulation results using the median data of each group as an individual. The estimated parameter value is one of the possible cases in that group to demonstrate how a typical learning curve fits the latent cause model. The reviewer mentioned “20-fold reduction in learning rate” is the comparison of two data points, not the actual comparison between groups. The comparison between control and App^NL-G-F mice in the 12-month-old group for all parameters was provided in Table S7. The Mann-Whitney U test did not reveal a significant difference in learning rate (η): 12-month-old control (Mdn = 0.09, IQR=0.23) vs. 12-month-old App^NL-G-F (Mdn = 0.12, IQR=0.23), U = 199, p = 0.587.  

We agree that lower learning rate could bias the learning toward inferring a new latent cause. However, this tendency may depend on the value of other parameters and varied in different phases in the reinstatement paradigm. Here, we used ⍺ as an example and demonstrate their interaction in Appendix 2 – table 2 with relatively extreme values: ⍺ \= {1, 3} and η \= {0.01, 0.5} while the rest of the parameters fixed at the initial guess value. 

When ⍺ = 1, the number of latent causes across phases (K_acq, K_ext, K_rem) remain unchanged and their posterior probability in test 3 were comparable even if η increased from 0.01 to 0.5. This is an example that lower η does not lead to inferring new latent causes because of low ⍺. The effect of low learning rate manifests in test 3 CR due to low w_{context, acq} and w_{context, ext}. 

When ⍺ = 3, the number of acquisition latent causes (K_acq) was higher in the case of η = 0.01 than that of η = 0.5, showing the effect mentioned by the reviewer. However, test 1 CR is much lower when η = 0.01, indicating unsuccessful learning even after inferring a new latent cause. This is none of the cases observed in this study. During extinction phases, the effect of η is surpassed by the effect of high ⍺, where the number of extinction latent causes (K_ext) is high and not affected by η. After the extinction phases, the effect of K kicks in as the total number of latent causes reaches its value (K = 33 in this example), especially in the case of η = 0.01. A new latent cause is inferred after extinction in the condition of η = 0.5, but the CR 3 is still high as the w_{context, acq} and w_{context, ext} are high. This is an example that a new latent cause is inferred in spite of higher η. 

Overall, the learning rate would not have a prominent effect alone throughout the reinstatement paradigm, and it has a joint effect with other parameters. Note that the example here did not cover our estimated results, as the estimated learning rate was not significantly different between control and App^NL-G-F mice (see above). Please refer to the reply to comment #31 for more discussion about the interaction among parameters when the learning rate is fixed. We hope this clarifies the reviewer’s concern.

[#15] (4) Why didn't the authors use the latent causal model on the Barnes maze task? The authors mention in the discussion that different cognitive processes may be at play across the two tasks, yet reversal tasks have been suggested to be solved using latent states to be able to flip between the two different task states. In this way, it seems very fitting to use the latent cause model. Indeed, it may even be a better way to assess changes in σx as there are presumably 12 observable stimuli/locations.

Please refer to our provisional response about the application of the latent cause model to the reversal Barnes maze task. Briefly, it would be difficult to directly apply the latent cause model to the Barnes maze data because this task involves operant learning, and thereby almost all conditions in the latent cause model are not satisfied. Please also see our reply to comment #24 for the discussion of the link between the latent cause model and Barnes maze task. 

Reviewer #2 (Recommendations for the authors):

[#16] (1) I had a bit of difficulty finding all the details of the model. First, I had to mainly rely on the Gershman 2017 paper to understand the model. Even then, there were certain aspects of the model that were not clear. For instance, it's not quite clear to me when the new internal states are created and how the maximum number of states is determined. After reading the authors' methods and the Gershman paper, it seems that a new internal state is generated at each time point, aka zt, and that the prior for that state decays onwards from alpha. Yet because most 'new' internal states don't ever take on much of a portion of the posterior, most of these states can be ignored. Is that a correct understanding? To state this another way, I interpret the equation on line 129 to indicate that the prior is determined by the power law for all existing internal states and that each new state starts with a value of alpha, yet I don't see the rule for creating a new state, or for iterating k other than that k iterates at each timestep. Yet this seems to not be consistent with the fact that the max number of states K is also a parameter fit. Please clarify this, or point me to where this is better defined.

I find this to be an important question for the current paper as it is unclear to me when the states were created. Most notably, in Figure 3, it's important to understand why there's an increase in the posterior of z₅ in the AD 12-month mice at test. Is state z₅ generated at trial 5? If so, the prior would be extremely small by trial 36, making it even more perplexing why z₅ has such a high posterior. If its weights are similar to z₃ and z₄, and they have been much more active recently, why would z₅ come into play?

We assume that the “new internal state" the reviewer is referring to is the “new latent cause." We would like to clarify that “internal state" in our study refers to all the latent causes at a given time point and observation. As this manuscript is submitted as a Research Advance article in eLife, we did not rephrase all the model details. Here, we explain when a new latent cause is created (i.e., the prior probability of a new latent cause is greater than 0) with the example of the 12-month-old group (Figure 3C and 3D). 

Suppose that before the start of each trial, an agent inferred the most likely latent cause with maximum posterior, and it inferred k latent causes so far. A new latent cause can be inferred at the computation of the prior of latent causes at the beginning of each trial.  

In the latent cause model, it follows a distance-dependent Chinese Restaurant Process (CRP; Blei and Frazier, 2011). The prior of each old latent cause is its posterior probability, which is the final count of the EM update before the current. In addition, the prior of old latent causes is sensitive to the time passage so that it exponentially decreases as a forgetting function modulated by g (see Figure 2 in Gershman et al., 2017). Simultaneously, the prior of a new cause is assigned ⍺. The new latent cause is inferred at this moment. Hence, the prior of latent causes is jointly determined by ⍺, g and its posterior probability. The maximum number of latent causes K is set a priori and does not affect the prior while k < K (see also reply to comment #30 for the discussion of boundary set for K and comment #31 for the discussion of the interaction between ⍺ and K). Note that only one new latent cause can be inferred in each trial, and (k+1)^th latent cause, which has never been inferred so far, is chosen as the new latent cause.

In our manuscript, the subscript number in zₖ denotes the order in which they were inferred, not the trial number. In Figures 3C and 3D, z₃ and z₄ were inferred in trials 5 and 6 during extinction; z₅ is a new latent cause inferred in trial 36. Therefore, the prior of z₅ is not extremely small compared to z₄ and z₃.

In both control and App^NL-G-F mice in the 12-month-old (Figures 3C and 3D), z₃ is dominant until trial 35. The unsignaled shock at trial 35 generates a large prediction error as only context is presented and followed by the US. This prediction error reduces posterior of z₃, while increasing the posterior of z₄ and w_context in z₃ and z₄. This decrease of posterior of z₃ is more obvious in the App^NL-G-F than in the control group, prompting them to infer a new latent cause z₅ (Figure 3C and 3D). Although Figure 3C and 3D are illustrative examples as we explained in the reply to comment #14, this interpretation would be plausible as the App^NL-G-F group inferred a significantly larger number of latent causes after the extinction with slightly higher posteriors of them than those in the control group (Figure 4E).

[#17] (2) Related to the above, Are the states z_A and z_B defined by the authors to help the reader group the states into acquisition and extinction states, or are they somehow grouped by the model? If the latter is true, I don't understand how this would occur based on the model. If the former, could the authors state that these states were grouped together by the author?

We used z_A and z_B annotations to assist with the explanation, so this is not grouped by the model. We have stated this in the manuscript Line 181-182.

[#18] (3) This expands on the third point above. In Figure 3D, internal states z₃, z₄, and z₅ appear to be pretty much identical in weights in the App group. It's not clear to me why then the posterior of z₅ would all of a sudden jump up. If I understand correctly, the posterior is the likelihood of the observations given the internal state (presumably this should be similar across z₃, z₄, and z₅), multiplied by the prior of the state. Z3 and Z4 are the dominant inferred states up to state 36. Why would z₅ become more likely if there doesn't appear to be any error? I'm inferring no error because there are little or no changes in weights on trial 36, most prominently no changes inz₃ which is the dominant internal state in step 36. If there's little change in weights, or no errors, shouldn't the prior dominate the calculation of the posterior which would lead to z₃ and z₄ being most prominent at trial 36?

We have explained how z₅ of the 12-month-old App^NL-G-F was inferred in the reply to comment #16. Here, we explain the process underlying the rapid changes of the posterior of z₃, z₄, and z₅ from trial 35 to 36.

During the extinction, the mice inferred z₃ given the CS and the context in the absence of US. In trial 35, they observed the context and the unsignaled shock in the absence of the CS. This reduced the likelihood for the CS under z₃ and thereby the posterior of z₃, while relatively increasing the posterior of z₄. The associative weight between the context and the US , w_context, indeed increased in both z₃ and z₄, but w_context of z₄ was updated more than that of z₃ due to its higher posterior probability. At the beginning of trial 36, a new latent cause z₅ was inferred with a certain prior (see also the reply for comment #16), and w₅ = w₀, where w₀ is the initial value of weight. After normalizing the prior over latent causes, the emergence of z₅ reduced the prior probability of other latent causes compared to the case where the prior of z₅ is 0. Since the CS was presented while the US was absent in trial 36, the likelihood of the CS and that of the US under z₃, and especially z₄, given the cues and w became lower than the case in which z₅ has not been inferred yet. Consequently, the posterior of z₅ became salient (Figure 3D).

To maintain consistency across panels, we used a uniform y-axis range. However, we acknowledge that this may make it harder to notice the changes of associative weights in Figure 3D. We have provided the subpanel in Figure 3D with a smaller y-axis limit to reveal the weight changes at trial 35 in Author response image 5.

Author response image 5.

Magnified view of w_context and wCS in the last 3 trials in Figure 3D. The graph format is the same as in Figure 3D. The weight for CS (w_CS) and that for context (w_context) in each latent cause across trial 34 (test 2), 35 (unsignaled shock), and 36 (test 3) in 12-month-old App^NL-G-F in Figure 3D was magnified in the upper and lower magenta box, respectively.

[#19] (8) In Figure 4B - The figure legend didn't appear to indicate at which time points the DIs are plotted.

We have amended the figure legend to indicate that DI between test 3 and test 1 is plotted.

[#20] (9) Lines 301-303 state that the posterior probabilities of the acquisition internal states in the 12month AD mice were much higher at test 1 and that this resulted in different levels of CR across the control and 12-month App group. This is shown in the Figure 4A supplement, but this is not apparent in Figure 3 panels C and D. Is the example shown in panel D not representative of the group? The CRs across the two examples in Figure 3 C and D look extremely similar at test 1. Furthermore, the posteriors of the internal states look pretty similar across the two groups for the first 4 trials. Both the App and control have substantial posterior probabilities for the acquisition period, I don't see any additional states at test 1. The pattern of states during acquisition looks strikingly similar across the two groups, whereas the weights of the stimuli are considerably different. I think it would help the authors to use an example that better represents what the authors are referring to, or provide data to illustrate the difference. Figure 4C partly shows this, but it's not very clear how strong the posteriors are for the 3rd state in the controls.

Figure 3 serves as an example to explain the internal states in each group (see also the third paragraph in the reply to comment #14). Figure 4C to H showed the results from each sample for between-group comparison in selected features. Therefore, the results of direct comparisons of the parameter values and internal states between genotypes in Figure 3 are not necessarily the same as those in Figure 4. Both examples in Figure 3C and 3D inferred 2 latent causes during the acquisition. In terms of posterior till test 1 (trial 4), the two could be the same. However, such examples were not rare, as the proportion of the mice that inferred 2 latent causes during the acquisition was slightly lower than 50% in the control, and around 90% in the App^NL-G-F mice (Figure 4C). The posterior probability of acquisition latent cause in test 1 showed a similar pattern (Figure 4 – figure supplement 3), with values near 1 in around 50% of the control mice and around 90% of the App^NL-G-F mice.  

[#21] (10) Line 320: This is a confusing sentence. I think the authors are saying that because the App group inferred a new state during test 3, this would protect the weights of the 'extinction' state as compared to the controls since the strength of the weight updates depends on the probability of the posterior.

In order to address this, we have revised this sentence to “Such internal states in App^NL-G-F mice would diverge the associative weight update from those in the control mice after extinction.” in the manuscript Line 349-351.

[#22] (11) In lines 517-519 the authors address the difference in generalizing the occurrence of stimuli across the App and control groups. It states that App mice with lower alpha generalized observations to an old cause rather than attributing it as a new state. Going back to statement 3 above, I think it's important to show that the model fit of a reduction in alpha does not go hand-in-hand with a reduction in the learning rates and hence the weights. Again, if the likelihoods are diminished due to the low weights, then the fit of alpha might be reduced as well. To reiterate my point above, if the observations in changes in generalization and differentiation occur because of a reduction in the learning rate, the modeling may not be providing a particularly insightful understanding of AD, other than that poor learning leads to ineffectual generalization and differentiation. Do these findings hold up if the learning rates are more comparable across the control and App group?

These findings were explained on the basis of comparable learning rates between control and App^NL-GF mice in the 12-month-old group (see the reply to comment #14). In addition, we have conducted simulation for different ⍺ and σ_x² values under the condition of the fixed learning rate, where overgeneralization and overdifferentaiton still occurred (see the reply to comment #26).  

[#23] (12) Lines 391 - 393. This is a confusing sentence. "These results suggest that App NL-G-F mice could successfully form a spatial memory of the target hole, while the memory was less likely to be retrieved by a novel observation such as the absence of the escape box under the target hole at the probe test 1." The App mice show improved behavior across days of approaching the correct hole. Is this statement suggesting that once they've approached the target hole, the lack of the escape box leads to a reduction in the retention of that memory?

We speculated that when the mice observed the absence of the escape box, a certain prediction error would be generated, which may have driven the memory modification. In App^NL-G-F mice, such modification, either overgeneralization or overdifferentiation, could render the memory of the target hole vulnerable; if overgeneralization occurred, the memory would be quickly overwritten as the goal no longer exists in this position in this maze, while if overdifferentiation occurred, a novel memory such that the goal does not exist in the maze different from previous one would be formed. In either case of misclassification, the probability of retrieving the goal position would be reduced. To reduce ambiguity in this sentence, we have revised the description in the manuscript Line 432-434 as follows: “These results suggest that App^NL-G-F mice could successfully form a spatial memory of the target hole, while they did not retrieve the spatial memory of the target hole as strongly as control mice when they observed the absence of the escape box during the probe test.”

[#24] (13) The connection between the results of Barnes maze and the fear learning paradigm is weak. How can changes in overgeneralization due to a reduction in the creation of inferred states and differentiation due to a reduced σx lead to the observations in the Barnes maze experiment?

We extrapolated our interpretation in the reinstatement modeling to behaviors in a different behavioral task, to explore the explanatory power of the latent cause framework formalizing mechanisms of associative learning and memory modification. Here, we explain the results of the reversal Barnes maze paradigm in terms of the latent cause model, while conferring the reinstatement paradigm.

Whilst we acknowledge that fear conditioning and spatial learning are not fully comparable, the reversal Barnes maze paradigm used in our study shares several key learning components with the reinstatement paradigm. 

First, associative learning is fundamental in spatial learning (Leising & Blaisdell, 2009; Pearce, 2009). Although we did not make any specific assumptions of what kind of associations were learned in the Barnes maze, performance improvements in learning phases likely reflect trial-and-error updates of these associations involving sensory preconditioning or secondary conditioning. Second, the reversal training phases could resemble the extinction phase in the reinstatement paradigm, challenge previously established memory. In terms of the latent cause model, both the reversal learning phase in the reversal Barnes maze paradigm and the extinction phase in the reinstatement paradigm induce a mismatch of the internal state. This process likely introduces large prediction errors, triggering memory modification to reconcile competing memories.  

Under the latent cause framework, we posit that the mice would either infer new memories or modify existing memories for the unexpected observations in the Barnes maze (e.g., changed location or absence of escape box) as in the reinstatement paradigm, but learn a larger number of association rules between stimuli in the maze compared to those in the reinstatement. In the reversal Barnes maze paradigm, the animals would infer that a latent cause generates the stimuli in the maze at certain associative weights in each trial, and would adjust behavior by retaining competing memories.

Both overgeneralization and overdifferentiation could explain the lower exploration time of the target hole in the App^NL-G-F mice in probe test 1. In the case of overgeneralization, the mice would overwrite the existing spatial memory of the target hole with a memory that the escape box is absent. In the case of overdifferentiation, the mice would infer a new memory such that the goal does not exist in the novel field, in addition to the old memory where the goal exists in the previous field. In both cases, the App^NL-G-F mice would not infer that the location of the goal is fixed at a particular point and failed to retain competing spatial memories of the goal, leading to relying on a less precise, non-spatial strategy to solve the task.  

Since there is no established way to formalize the Barnes maze learning in the latent cause model, we did not directly apply the latent cause model to the Barnes maze data. Instead, we used the view above to explore common processes in memory modification between the reinstatement and the Barnes maze paradigm. 

The above description was added to the manuscript on page 13 (Line 410-414) and page 19-20 (Line 600-602, 626-639).

[#25] (14) In the fear conditioning task, it may be valuable to separate responding to the context and the cue at the time of the final test. The mice can learn about the context during the reinstatement, but there must be an inference to the cue as it's not present during the reinstatement phase. This would provide an opportunity for the model to perhaps access a prior state that was formed during acquisition. This would be more in line with the original proposal by Gershman et al. 2017 with spontaneous recovery.

Please refer to the reply to comment #13 regarding separating the response to context in test 3.  

Reviewer #3 (Public review):

Summary:

This paper seeks to identify underlying mechanisms contributing to memory deficits observed in Alzheimer's disease (AD) mouse models. By understanding these mechanisms, they hope to uncover insights into subtle cognitive changes early in AD to inform interventions for early-stage decline.

Strengths:

The paper provides a comprehensive exploration of memory deficits in an AD mouse model, covering the early and late stages of the disease. The experimental design was robust, confirming age-dependent increases in Aβ plaque accumulation in the AD model mice and using multiple behavior tasks that collectively highlighted difficulties in maintaining multiple competing memory cues, with deficits most pronounced in older mice.

In the fear acquisition, extinction, and reinstatement task, AD model mice exhibited a significantly higher fear response after acquisition compared to controls, as well as a greater drop in fear response during reinstatement. These findings suggest that AD mice struggle to retain the fear memory associated with the conditioned stimulus, with the group differences being more pronounced in the older mice.

In the reversal Barnes maze task, the AD model mice displayed a tendency to explore the maze perimeter rather than the two potential target holes, indicating a failure to integrate multiple memory cues into their strategy. This contrasted with the control mice, which used the more confirmatory strategy of focusing on the two target holes. Despite this, the AD mice were quicker to reach the target hole, suggesting that their impairments were specific to memory retrieval rather than basic task performance.

The authors strengthened their findings by analyzing their data with a leading computational model, which describes how animals balance competing memories. They found that AD mice showed somewhat of a contradiction: a tendency to both treat trials as more alike than they are (lower α) and similar stimuli as more distinct than they are (lower σx) compared to controls.

Weaknesses:

While conceptually solid, the model struggles to fit the data and to support the key hypothesis about AD mice's ability to retain competing memories. These issues are evident in Figure 3:

[#26] (1) The model misses key trends in the data, including the gradual learning of fear in all groups during acquisition, the absence of a fear response at the start of the experiment, the increase in fear at the start of day 2 of extinction (especially in controls), and the more rapid reinstatement of fear observed in older controls compared to acquisition.

We acknowledge these limitations and explained why they arise in the latent cause model as follows.

a. Absence of a fear response at the start of the experiment and the gradual learning of fear during acquisition 

In the latent cause model, the CR is derived from a sigmoidal transformation from the predicted outcome with the assumption that its mapping to behavioral response may be nonlinear (see Equation 10 and section “Conditioned responding” in Gershman et al., 2017). 

The magnitude of the unconditioned response (trial 1) is determined by w₀, θ, and λ. An example was given in Appendix 2 – table 3. In general, a higher w₀ and a lower θ produce a higher trial 1 CR when other parameters are fixed. During the acquisition phase, once the expected shock exceeds θ, CR rapidly approaches 1, and further increases in expected shock produce few changes in CR. This rapid increase was also evident in the spontaneous recovery simulation (Figure 11) in Gershman et al. (2017). The steepness of this rapid increase is modulated by λ such that a higher value produces a shallower slope. This is a characteristic of the latent cause model, assuming CR follows a sigmoid function of expected shock, while the ordinal relationship over CRs is maintained with or without the sigmoid function, as Gershman et al. (2017) mentioned. If one assumes that the CR should be proportional to the expected shock, the model can reproduce the gradual response as a linear combination of w and posteriors of latent causes while omitting the sigmoid transformation (Figure 3). 

b. Increase in fear at the start of day 2 extinction

This point is partially reproduced by the latent cause model. As shown in Figure 3, trial 24 (the first trial of day 2 extinction) showed an increase in both posterior probability of latent cause retaining fear memory and the simulated CRs in all groups except the 6-month-old control group, though the increase in CR was small due to the sigmoid transformation (see above). This can be explained by the latent cause model as 24 h time lapse between extinction 1 and 2 decreases the prior of the previously inferred latent cause, leading to an increase of those of other latent causes. 

Unlike other groups, the 6-month-old control did not exhibit increased observed CR at trial 24

but at trial 25 (Figure 3A). The latent cause model failed to reproduce it, as there was no increase in posterior probability in trial 24 (Figure 3A). This could be partially explained by the low value of g, which counteracts the effect of the time interval between days: lower g keeps prior of the latent causes at the same level as those in the previous trial. Despite some failures in capturing this effect, our fitting policy was set to optimize prediction among the test trials given our primary purpose of explaining reinstatement.

c. more rapid reinstatement of fear observed in older controls compared to acquisition

We would like to point out that this was replicated by the latent cause model as shown in Figure 3 – figure supplement 1C. The DI between test 3 and test 1 calculated from the simulated CR was significantly higher in 12-month-old control than in App^NL-G-F mice (cf. Figure 2C to E).  

[#27] (2) The model attributes the higher fear response in controls during reinstatement to a stronger association with the context from the unsignaled shock phase, rather than to any memory of the conditioned stimulus from acquisition. These issues lead to potential overinterpretation of the model parameters. The differences in α and σx are being used to make claims about cognitive processes (e.g., overgeneralization vs. overdifferentiation), but the model itself does not appear to capture these processes accurately. The authors could benefit from a model that better matches the data and that can capture the retention and recollection of a fear memory across phases.

First, we would like to clarify that the latent cause model explains the reinstatement not only by the extinction latent cause with increased w_context but also the acquisition latent cause with preserved wCS and w_context (see also reply to comment #13). Second, the latent cause model primarily attributes the higher fear reinstatement in control to a lower number of latent causes inferred after extinction (Figure 4E) and higher w_context in extinction latent cause (Figure 4G). We noted that there was a trend toward significance in the posterior probability of latent causes inferred after extinction (Figure 4E), which in turn influences those of acquisition latent causes. Although the posterior probability of acquisition latent cause appeared trivial and no significance was detected between control and App^NL-G-F mice (Figure 4C), it was suppressed by new latent causes in App^NL-G-F mice (Author response image 6).

This indicates that App^NL-G-F mice retrieved acquisition memory less strongly than control mice. Therefore, we argue that the latent cause model attributed a higher fear response in control during reinstatement not solely to the stronger association with the context but also to CS fear memory from acquisition. Although we tested whether additional models fit the reinstatement data in individual mice, these models did not satisfy our fitting criteria for many mice compared to the latent cause model (see also reply to comment #4 and #28).

Author response image 6.

Posterior probability of acquisition, extinction, and after extinction latent causes in test 3. The values within each bar indicate the mean posterior probability of acquisition latent cause (darkest shade), extinction latent cause (medium shade), and latent causes inferred after extinction (lightest shade) in test 3 over mice within genotype. Source data are the same as those used in Figure 4C–E (posterior of z).

Conclusion:

Overall, the data support the authors' hypothesis that AD model mice struggle to retain competing memories, with the effect becoming more pronounced with age. While I believe the right computational model could highlight these differences, the current model falls short in doing so.

Reviewer #3 (Recommendations for the authors):

[#28] Other computational models may better capture the data. Ideally, I'd look for a model that can capture the gradual learning during acquisition, and, in some mice, the inferring of a new latent cause during extinction, allowing the fear memory to be retained and referenced at the start of day 2 extinction and during later tests.

We have further evaluated another computational model, the latent state model, and compared it with the latent cause model. The simulation of reinstatement and parameter estimation method of the latent state model were described in the Appendix.

The latent state model proposed by Cochran and Cisler (2019) shares several concepts with the latent cause model, and well replicates empirical data under certain conditions. We expect that it can also explain the reinstatement. 

Following the same analysis flow for the latent cause model, we estimated the parameters and simulated reinstatement in the latent state model from individual CRs and median of them. In the median freezing rate data of the 12-month-old control mice, the simulated CR replicated the observed CR well and exhibited the ideal features that the reviewer looked for: gradual learning during acquisition and an increased fear at the start of the second-day extinction (Appendix 1 – figure 1G). However, a lot of samples did not fit well to the latent state model. The number of anomalies was generally higher than that in the latent cause model (Appendix 1 – figure 2). Within the accepted samples, the sum of squared prediction error in all trials was significantly lower in the latent state model, which resulted from lower prediction error in the acquisition trials (Appendix 1 – figure 4A and 4B). In the three test trials, the squared prediction error was comparable between the latent state model and the latent cause model except for the test 2 trials in the control group (Appendix 1 – figure 4A and 4B, rightmost panel). On the other hand, almost all accepted samples continued to infer the acquisition latent states during extinction without inferring new states (Appendix 1 – figure 5B and 5E, left panel), which differed from the ideal internal states the reviewer expected. While the latent state model fit performance seems to be better than the latent cause model, the accepted samples cannot reproduce the lower DI between test 3 and test 1 in aged App^NL-G-F mice (Appendix 1 – figure 6C). These results make the latent state model less suitable for our purpose and therefore we decided to stay with the latent cause model. It should also be noted that we did not explore all parameter spaces of the latent state model hence we cannot rule out the possibility that alternative parameter sets could provide a better fit and explain the memory modification process well. A more comprehensive parameter search in the LSM may be a valuable direction for future research.

If you decide not to go with a new model, my preference would be to drop the current modeling. However, if you wish to stay with the current model, I'd like to see justification or acknowledgment of the following:

[#29] (1) Lower bound on alpha of 1: This forces the model to infer new latent causes, but it seems that some mice, especially younger AD mice, might rely more on classical associative learning (e.g., Rescorla-Wagner) rather than inferring new causes.

We acknowledge that the default value set in Gershman et al. (2017) is 0.1, and the constraint we set is a much higher value. However, ⍺ = 1 does not always force the model to infer new latent causes.

In the standard form Chinese restaurant process (CRP), the prior that n^th observation is assigned to a new cluster is given by ⍺ / (n - 1 + ⍺) (Blei & Gershman, 2012). When ⍺ = 1, the prior of the new cluster for the 2nd observation will be 0.5; when ⍺ = 3, this prior increases to 0.75. Thus, when ⍺ > 1, the prior of the new cluster is above chance early in the sequence, which may relate to the reviewer’s concern. However, this effect diminishes as the number of observations increases. For instance, the prior of the new cluster drops to 0.1 and 0.25 for the 10th observation when ⍺ = 1 and 3, respectively. Furthermore, the prior in the latent cause model is governed by not only α but also g, a scaling parameter for the temporal difference between successive observations (see Results in the manuscript) following “distance-dependent” CRP, then normalized over all latent causes including a new latent cause. Thus, it does not necessarily imply that ⍺ greater than 1 forces agents to infer a new latent cause_. As shown in Appendix 2 – table 4, the number of latent causes does not inflate in each trial when _α = 1. On the other hand, the high number of latent causes due to α = 2 can be suppressed when g = 0.01. More importantly, the driving force is the prediction error generated in each trial (see also comment #31 about the interaction between ⍺ and σ_x²). Raising the value of ⍺ per se can be viewed as increasing the probability to infer a new latent cause, not forcing the model to do so by higher α alone. 

During parameter exploration using the median behavioral data under a wider range of ⍺ with a lower boundary at 0.1, the estimated value eventually exceeded 1. Therefore, we set the lower bound of ⍺ to be 1 is to reduce inefficient sampling. 

[#30] (2) Number of latent causes: Some mice infer nearly as many latent causes as trials, which seems unrealistic.

We set the upper boundary for the maximum number of latent causes (K) to be 36 to align with the infinite features of CRP. This allowed some mice to infer more than 20 latent causes in total. When we checked the learning curves in these mice, we found that they largely fluctuated or did not show clear decreases during the extinction (Author response image 7, colored lines). The simulated learning curves were almost flat in these trials (Author response image 7, gray lines). It might be difficult to estimate the internal states of such atypical mice if the sampling process tried to fit them by increasing the number of latent causes. Nevertheless, most of the samples have a reasonable total number of latent causes: 12-month-old control mice, Mdn = 5, IQR = 4; 12-month-old App^NL-G-F mice, Mdn = 5, IQR = 1.75; 6-month-old control mice, Mdn = 7, IQR = 12.5; 6-month-old App^NL-G-F mice, Mdn = 5, IQR = 5.25. These data were provided in Tables S9 and S12.  

Author response image 7.

Samples with a high number of latent causes. Observed CR (colored line) and simulated CR (gray line) for individual samples with a total number of inferred latent causes exceeding 20. 

[#31] (3) Parameter estimation: With 10 parameters fitting one-dimensional curves, many parameters (e.g., α and σx) are likely highly correlated and poorly identified. Consider presenting scatter plots of the parameters (e.g., α vs σx) in the Supplement.

We have provided the scatter plots with a correlation matrix in Figure 4 – figure supplement 1 for the 12-month-old group and Figure 5 – figure supplement 1 for the 6-month-old group. As pointed out by the reviewer, there are significant rank correlations between parameters including ⍺ and σ_x² in both the 6 and 12-month-old groups. However, we also noted that there are no obvious linear relationships between the parameters.

The correlation above raises a potential problem of non-identifiability among parameters. First, we computed the variance inflation index (VIF) for all parameters to examine the risk of multicollinearity, though we did not consider a linear regression between parameters and DI in this study. All VIF values were below the conventional threshold 10 (Appendix 2 – table 5), suggesting that severe multicollinearity is unlikely to bias our conclusions. Second, we have conducted the simulation with different combinations of ⍺, σ_x², and K to clarify their contribution to overgeneralization and overdifferentiation observed in the 12-month-old group. 

In Appendix 2 – table 6, the values of ⍺ and σ_x² were either their upper or lower boundary set in parameter estimation, while the value K was selected heuristically to demonstrate its effect. Given the observed positive correlation between alpha and σ_x², and their negative correlation with K (Figure 4 - figure supplement 1), we consider the product of K \= {4, 35}, ⍺ \= {1, 3} and σ_x² \= {0.01, 3}. Among these combinations, the representative condition for the control group is α = 3, σ_x² = 3, and that for the App^NL-G-F group is α = 1, σ_x² = 0.01. In the latter condition, overgeneralization and overdifferentiation, which showed higher test 1 CR, lower number of acquisition latent causes (K_acq), lower test 3 CR, lower DI between test 3 and test 1, and higher number of latent causes after extinction (K_rem), was extremely induced. 

We found conditions that fall outside of empirical correlation, such as ⍺ = 3, σ_x² = 0.01, also reproduced overgeneralization and overdifferentiation. Similarly, the combination, ⍺ = 1, σ_x² = 3, exhibited control-like behavior when K = 4 but shifted toward App^NL-G-F-like behavior when K = 36. The effect of K was also evident when ⍺ = 3 and σ_x² = 3, where K = 36 led to over-differentiation. We note that these conditions were artificially set and likely not representative of biologically plausible. These results underscore the non-identifiability concern raised by the reviewer. Therefore, we acknowledge that merely attributing overgeneralization to lower ⍺ or overdifferentiation to lower σ_x² may be overly reductive. Instead, these patterns likely arise from the joint effect of ⍺, σ_x², and K. We have revised the manuscript accordingly in Results and Discussion (page 11-13, 18-19).

[#32] (4) Data normalization: Normalizing the data between 0 and 1 removes the interpretability of % freezing, making mice with large changes in freezing indistinguishable seem similar to mice with small changes.

As we describe in our reply to comment #26, the conditioned response in the latent cause model was scaled between 0 and 1, and we assume 0 and 1 mean the minimal and maximal CR within each mouse, respectively. Furthermore, although we initially tried to fit simulated CRs to raw CRs, we found that the fitting level was low due to the individual difference in the degree of behavioral expression: some mice exhibited a larger range of CR, while others showed a narrower one. Thus, we decided to normalize the data. We agree that this processing will make the mice with high changes in freezing% indistinguishable from those with low changes. However, the freezing% changes within the mouse were preserved and did not affect the discrimination index.

[#33] (5) Overlooking parameter differences: Differences in parameters, like w₀, that didn't fit the hypothesis may have been ignored.

Our initial hypothesis is that internal states were altered in App^NL-G-F mice, and we did not have a specific hypothesis on which parameter would contribute to such a state. We mainly focus on the parameters (1) that are significantly different between control and App</sup>NL-G</sup>- mice and (2) that are significantly correlated to the empirical behavioral data, DI between test 3 and test 1. 

In the 12-month-old group, besides ⍺ and σ_x², w₀ and K showed marginal p-value in Mann-Whitney U test (Table S7) and moderate correlation with the DI (Table S8). While differences in K were already discussed in the manuscript, we did miss the point that w₀ could contribute to the differences in w between control and App^NL-G-F (Figure 4G) in the previous manuscript. We explain the contribution of w₀ on the reinstatement results here. When other parameters are fixed, higher w₀ would lead to higher CR in test 3, because higher w₀ would allow increasing w_context by the unsignaled shock, leading to reinstatement (Appendix 2 – table 7). It is likely that higher w₀ would be sampled through the parameter estimation in the 12-month-old control but not App^NL-G-F. On the other hand, the number of latent causes is not sensitive to w₀ when other parameters were fixed at the initial guess value (Appendix 2 – table 1), suggesting w₀ has a small contribution to memory modification process. 

Thus, we speculate that although the difference in w₀ between control and App^NL-G-F mice may arise from the sampling process, resulting in a positive correlation with DI between test 3 and test 1, its contribution to diverged internal states would be smaller relative to α or σ_x² as a wide range of w₀ has no effect on the number of latent causes (Appendix 2 – table 7). We have added the discussion of differences in w₀ in the 12-month-old group in manuscript Line 357-359.

In the 6-month-old group, besides ⍺ and σ_x², 𝜃 is significantly higher in the AD mice group (Table S10) but not correlated with the DI (Table S11). We have already discussed this point in the manuscript.  

[#34] (6) Initial response: Higher initial responses in the model at the start of the experiment may reflect poor model fit.

Please refer to our reply to comment #26 for our explanation of what contributes to high initial responses in the latent cause model.

In addition, achieving a good fit for the acquisition CRs was not our primary purpose, as the response measured in the acquisition phase includes not only a conditioned response to the CS and context but also an unconditioned response to the novel stimuli (CS and US). This mixed response presumably increased the variance of the measured freezing rate over individuals, therefore we did not cover the results in the discussion.

Rather, we favor models at least replicating the establishment of conditioning, extinction and reinstatement of fear memory in order to explain the memory modification process. As we mentioned in the reply for comment #4, alternative models, the latent state model and the Rescorla-Wagner model, failed to replicate the observation (cf. Figure 3 – figure supplement 1A-1C). Thus, we chose to stand on the latent cause model as it aligns better with the purpose of this study. 

[#35] In addition, please be transparent if data is excluded, either during the fitting procedure or when performing one-way ANCOVA. Avoid discarding data when possible, but if necessary, provide clarity on the nature of excluded data (e.g., how many, why were they excluded, which group, etc?).

We clarify the information of excluded data as follows. We had 25 mice for the 6-month-old control group, 26 mice for the 6-month-old App^NL-G-F group, 29 mice for the 12-month-old control group, and 26 mice for the 12-month-old App^NL-G-F group (Table S1). 

Our first exclusion procedure was applied to the freezing rate data in the test phase. If the mouse had a freezing rate outside of the 1.5 IQR in any of the test phases, it is regarded as an outlier and removed from the analysis (see Statistical analysis in Materials and Methods). One mouse in the 6-month-old control group, one mouse in the 6-month-old App^NL-G-F group, five mice in the 12-month-old control group, and two mice in the 12-month-old App^NL-G-F group were excluded.

Our second exclusion procedure was applied during the fitting and parameter estimation (see parameter estimation in Materials and Methods). We have provided the number of anomaly samples during parameter estimation in Appendix 1 – figure 2.   

Lastly, we would like to state that all the sample sizes written in the figure legends do not include outliers detected through the exclusion procedure mentioned above.

[#36] Finally, since several statistical tests were used and the differences are small, I suggest noting that multiple comparisons were not controlled for, so p-values should be interpreted cautiously.

We have provided power analyses in Tables S21 and S22 with methods described in the manuscript (Line 897-898) and added a note that not all of the multiple comparisons were corrected for in the manuscript (Line 898-899).

References cited in the response letter only 

Bellio, T. A., Laguna-Torres, J. Y., Campion, M. S., Chou, J., Yee, S., Blusztajn, J. K., & Mellott, T. J. (2024). Perinatal choline supplementation prevents learning and memory deficits and reduces brain amyloid Aβ42 deposition in App^NL-G-F Alzheimer’s disease model mice. PLOS ONE, 19(2), e0297289. https://doi.org/10.1371/journal.pone.0297289

Blei, D. M., & Frazier, P. I. (2011). Distance Dependent Chinese Restaurant Processes. Journal of Machine Learning Research, 12(74), 2461–2488.

Cochran, A. L., & Cisler, J. M. (2019). A flexible and generalizable model of online latent-state learning. PLOS Computational Biology, 15(9), e1007331. https://doi.org/10.1371/journal.pcbi.1007331

Curiel Cid, R. E., Crocco, E. A., Duara, R., Vaillancourt, D., Asken, B., Armstrong, M. J., Adjouadi, M., Georgiou, M., Marsiske, M., Wang, W., Rosselli, M., Barker, W. W., Ortega, A., Hincapie, D., Gallardo, L., Alkharboush, F., DeKosky, S., Smith, G., & Loewenstein, D. A. (2024). Different aspects of failing to recover from proactive semantic interference predicts rate of progression from amnestic mild cognitive impairment to dementia. Frontiers in Aging Neuroscience, 16. https://doi.org/10.3389/fnagi.2024.1336008

Giustino, T. F., Fitzgerald, P. J., Ressler, R. L., & Maren, S. (2019). Locus coeruleus toggles reciprocal prefrontal firing to reinstate fear. Proceedings of the National Academy of Sciences, 116(17), 8570–8575. https://doi.org/10.1073/pnas.1814278116

Gu, X., Wu, Y.-J., Zhang, Z., Zhu, J.-J., Wu, X.-R., Wang, Q., Yi, X., Lin, Z.-J., Jiao, Z.-H., Xu, M., Jiang, Q., Li, Y., Xu, N.-J., Zhu, M. X., Wang, L.-Y., Jiang, F., Xu, T.-L., & Li, W.-G. (2022). Dynamic tripartite construct of interregional engram circuits underlies forgetting of extinction memory. Molecular Psychiatry, 27(10), 4077–4091. https://doi.org/10.1038/s41380-022-01684-7

Lacagnina, A. F., Brockway, E. T., Crovetti, C. R., Shue, F., McCarty, M. J., Sattler, K. P., Lim, S. C., Santos, S. L., Denny, C. A., & Drew, M. R. (2019). Distinct hippocampal engrams control extinction and relapse of fear memory. Nature Neuroscience, 22(5), 753–761. https://doi.org/10.1038/s41593-019-0361-z

Loewenstein, D. A., Curiel, R. E., Greig, M. T., Bauer, R. M., Rosado, M., Bowers, D., Wicklund, M., Crocco, E., Pontecorvo, M., Joshi, A. D., Rodriguez, R., Barker, W. W., Hidalgo, J., & Duara, R. (2016). A Novel Cognitive Stress Test for the Detection of Preclinical Alzheimer’s Disease: Discriminative Properties and Relation to Amyloid Load. The American Journal of Geriatric Psychiatry : Official Journal of the American Association for Geriatric Psychiatry, 24(10), 804–813. https://doi.org/10.1016/j.jagp.2016.02.056

Loewenstein, D. A., Greig, M. T., Curiel, R., Rodriguez, R., Wicklund, M., Barker, W. W., Hidalgo, J., Rosado, M., & Duara, R. (2015). Proactive Semantic Interference Is Associated With Total and Regional Abnormal Amyloid Load in Non-Demented Community-Dwelling Elders: A Preliminary Study. The American Journal of Geriatric Psychiatry : Official Journal of the American Association for Geriatric Psychiatry, 23(12), 1276–1279. https://doi.org/10.1016/j.jagp.2015.07.009

Valles-Salgado, M., Gil-Moreno, M. J., Curiel Cid, R. E., Delgado-Á lvarez, A., Ortega-Madueño, I., Delgado-Alonso, C., Palacios-Sarmiento, M., López-Carbonero, J. I., Cárdenas, M. C., MatíasGuiu, J., Díez-Cirarda, M., Loewenstein, D. A., & Matias-Guiu, J. A. (2024). Detection of cerebrospinal fluid biomarkers changes of Alzheimer’s disease using a cognitive stress test in persons with subjective cognitive decline and mild cognitive impairment. Frontiers in Psychology, 15. https://doi.org/10.3389/fpsyg.2024.1373541

Zaki, Y., Mau, W., Cincotta, C., Monasterio, A., Odom, E., Doucette, E., Grella, S. L., Merfeld, E., Shpokayte, M., & Ramirez, S. (2022). Hippocampus and amygdala fear memory engrams reemerge after contextual fear relapse. Neuropsychopharmacology, 47(11), 1992–2001. https://doi.org/10.1038/s41386-022-01407-0

Author response:

The following is the authors’ response to the original reviews

Public Reviews:

Reviewer #1 (Public review):

Li et al. investigate Ca2+ signaling in T. gondii and argue that Ca2+ tunnels through the ER to other organelles to fuel multiple aspects of T. gondii biology. They focus in particular on TgSERCA as the presumed primary mechanism for ER Ca2+ filling. Although, when TgSERCA was knocked out there was still a Ca2+ release in response to TG present.

Note that we did not generate a complete SERCA knockout, as this gene is essential, and its complete loss would not permit the isolation of viable parasites. Instead, we created conditional mutants that downregulate the expression of SERCA. Importantly, some residual activity is present in the mutant after 24 h of ATc treatment as shown in Fig 4C. This is consistent with our Western blots, which demonstrate the presence of residual SERCA protein at 1, 1.5 and 2 days post ATc treatment (Fig. 3B). We have clarified this point in the revised manuscript (lines 232233). See also lines 97-102.

Overall the Ca2+ signaling data do not support the conclusion of Ca2+ tunneling through the ER to other organelles in fact they argue for direct Ca2+ uptake from the cytosol. The authors show EM membrane contact sites between the ER and other organelles, so Ca2+ released by the ER could presumably be taken up by other organelles but that is not ER Ca2+ tunneling. They clearly show that SERCA is required for T. gondii function.

Overall, the data presented to not fully support the conclusions reached

We agree that the data does not support Ca²⁺ tunneling as defined and characterized in mammalian cells. In response to this comment, we have modified the title and the text accordingly.

However, we respectfully would like to emphasize that the study demonstrates more than just the role of SERCA in T. gondii “function”. Our findings reveal that the ER, through SERCA activity, sequesters calcium following influx through the PM (see reviewer 2 comment). The ER calcium pool is important for replenishing other intracellular compartments.

The experiments support a model in which the ER actively takes up cytosolic Ca²⁺ as it enters the parasite and contributes to intracellular Ca²⁺ redistribution during transitions between distinct extracellular calcium environments. We believe that the role of the ER in modulating intracellular calcium dynamics is demonstrated in Figures 1H–K, 4G-H, and 5H–K. To highlight the relevance of these findings, we have included an expanded discussion in the revised manuscript. See lines 443-449 and 510-522.

Data argue for direct Ca2+ uptake from the cytosol

The ER most likely takes up calcium from the cytosol following its entry through the PM and redistributes it to the other organelles. We deleted any mention of the word “tunneling” and replaced it with transfer and re-distribution as they reflect our experimental findings more accurately.

We interpret the experiments shown in Figure 1 H and I as re-distribution because the amount of calcium released after nigericin or GPN are greatly enhanced after TG addition. We first add calcium to allow intracellular stores to become filled, followed by the addition of TG, which allows calcium leakage from the ER. This leaked calcium can either enter the cytosol and be pumped out or be taken up by other organelles. Our interpretation is that this process leads to an increased calcium content in acidic compartments.

We conducted an additional experiment in which SERCA was inhibited prior to calcium addition, allowing cytosolic calcium to be exported or taken up by acidic stores. We observed a change in the GPN response (Fig. S2A), possibly indicating that the PLVAC can sequester calcium when SERCA is inactive. While this may support the reviewer’s view, TG treatment does not reflect physiological conditions and may enhance calcium transfer to other compartments. Although the result is interesting, interpretation is complicated by the use of parasites in suspension and drug exposure in solution. Single-parasite measurements are not feasible due to weak signals, and adhered parasites are even less physiological than those in suspension.

In support of our view, the experiments shown in Figs 4G and H show that down regulating SERCA reduces significantly the response to GPN indicating diminished acidic store loading. In Fig 5I we observe that mitochondrial calcium uptake is reduced in the iDSERCA (+ATc) mutant in response to GPN. Fig 2B demonstrates that TgSERCA can take up calcium at 55 nM, close to resting cytosolic calcium while in Figures 5E and S5B we show that the mitochondrion is not responsive to an increase of cytosolic calcium. Uptake by the mitochondria requires much higher concentrations (Fig 5B-C), which may be achieved within microdomains at MCS between the ER and mitochondrion. This is also consistent with findings reported by Li et al (Nat Commun. 2021) where similar microdomains mediated transfer of calcium to the apicoplast (Fig. 7 E and F of the mentioned reference) was observed.

Reviewer 2 (Public review):

The role of the endoplasmic reticulum (ER) calcium pump TgSERCA in sequestering and redistributing calcium to other intracellular organelles following influx at the plasma membrane.

T. gondii transitions through life cycle stages within and exterior to the host cells, with very different exposures to calcium, adds significance to the current investigation of the role of the ER in redistributing calcium following exposure to physiological levels of extracellular calcium

They also use a conditional knockout of TgSERCA to investigate its role in ER calcium store-filling and the ability of other subcellular organelles to sequester and release calcium. These knockout experiments provide important evidence that ER calcium uptake plays a significant role in maintaining the filling state of other intracellular compartments.

We thank the reviewer.

While it is clearly demonstrated, and not surprising, that the addition of 1.8 mM extracellular CaCl2 to intact T. gondii parasites preincubated with EGTA leads to an increase in cytosolic calcium and subsequent enhanced loading of the ER and other intracellular compartments, there is a caveat to the quantitation of these increases in calcium loading. The authors rely on the amplitude of cytosolic free calcium increases in response to thapsigargin, GPN, nigericin, and CCCP, all measured with fura2. This likely overestimates the changes in calcium pool sizes because the buffering of free calcium in the cytosol is nonlinear, and fura2 (with a Kd of 100-200 nM) is a substantial, if not predominant, cytosolic calcium buffer. Indeed, the increases in signal noise at higher cytosolic calcium levels (e.g. peak calcium in Figure 1C) are indicative of fura2 ratio calculations approaching saturation of the indicator dye.

We acknowledge the limitations associated with using Fura-2 for cytosolic calcium measurements. However, according to the literature (Grynkiewicz, Get al. (1985). J. Biol. Chem. 260 (6): 3440–3450. PMID 3838314) Fura-2 is suited for measurements between 100 nM and 1 µM calcium. The responses in our experiments were within that range and the experiments with the SERCA mutant and mitochondrial GCaMPfs supports the conclusions of our work.

However, we agree with the reviewer that the experiment shown in Fig 1C (now Fig 1D) presents a response that approaches the limit of the linear range of Fura-2. In response to this, we have replaced this panel with a more representative experiment that remains within the linear range of the indicator (revised Fig 1D). Additionally, we have included new experiments adding GPN along with corresponding quantifications, which further support our conclusions regarding calcium dynamics in the parasite.

Another caveat, not addressed, is that loading of fura2/AM can result in compartmentalized fura2, which might modify free calcium levels and calcium storage capacity in intracellular organelles.

We are aware of the potential issue of Fura-2 compartmentalization, and our protocol was designed to minimize this effect. We load cells with Fura-2 for 26 min at room temperature, then maintain them on ice, and restrict the use of loaded parasites to 2-3 hours. We have observed evidence of compartmentalization as this is reflected in increasing concentrations of resting calcium with time. We carry out experiments within a time frame in which the resting calcium stays within the 100 nM range. We have included a sentence in the Materials and Methods section. Lines 604-606.

Additionally, following this reviewer’s suggestion, we performed further experiments to directly assess compartmentalization. See below the full response to reviewer 2.

The finding that the SERCA inhibitor cyclopiazonic acid (CPA) only mobilizes a fraction of the thapsigargin-sensitive calcium stores in T. gondii coincides with previously published work in another apicomplexan parasite, P. falciparum, showing that thapsigargin mobilizes calcium from both CPA-sensitive and CPA-insensitive calcium pools (Borges-Pereira et al., 2020, DOI: 10.1074/jbc.RA120.014906). It would be valuable to determine whether this reflects the off-target effects of thapsigargin or the differential sensitivity of TgSERCA to the two inhibitors.

This is an interesting observation, and we now include a discussion of this result considering the Plasmodium study and include the citation. Lines 436-442.

Figure S1 suggests differential sensitivity, and it shows that thapsigargin mobilizes calcium from both CPA-sensitive and CPA-insensitive calcium pools in T. gondii. Also important is that we used 1 µM TG as we are aware that TG has shown off-target effects at higher concentrations. TG is a well-characterized, irreversible SERCA inhibitor that ensures complete and sustained inhibition of SERCA activity. In contrast, CPA is a reversible inhibitor whose effectiveness is influenced by ATP levels, and it may only partially inhibit SERCA or dissociate over time, allowing residual Ca²⁺ reuptake into the ER.

Additionally, as suggested by the reviewer we performed experiments using the Mag-Fluo-4 protocol to compare the inhibitory effects of CPA and TG. These results are presented in Fig. S3 (Lines 217-223). Under the conditions of the Mag-Fluo-4 assay with digitonin-permeabilized cells, both TG and CPA showed similar rates of Ca²⁺ leakage following the addition of the inhibitor. This may indicate that under the conditions of the Mag-Fluo-4 experiments the rate of Ca²⁺ leak is mostly determined by the intrinsic leak mechanism and not by the nature of the inhibitor. By contrast, in intact Fura-2–loaded cells, CPA induces a smaller cytosolic Ca²⁺ increase than TG, consistent with less efficient SERCA inhibition likely due to its reversibility and possibly incomplete inhibition under cellular conditions.

The authors interpret the residual calcium mobilization response to Zaprinast observed after ATc knockdown of TgSERCA (Figures 4E, 4F) as indicative of a target calcium pool in addition to the ER. While this may well be correct, it appears from the description of this experiment that it was carried out using the same conditions as Figure 4A where TgSERCA activity was only reduced by about 50%.

We partially agree with the reviewer that 50% knockdown of TgSERCA means that the ER may still be targeted by zaprinast, and that there is no definitive evidence of the involvement of another calcium pool. The Mag-Fluo-4 experiment, while we acknowledge that the fluorescence of MagFluo-4 is not linear to calcium, indicates that SERCA activity is present even after 24 hr of ATc treatment. However, when Zaprinast is added after TG, we observed a significant calcium release in wild type cells. This result suggests the presence of another large calcium pool than the one mobilized by TG (PMID: 2693306).

We recently published work describing the Golgi as a calcium store in Toxoplasma (PMID: 40043955) and we showed in Fig. S4 D-G of that work, that GPN treatment of tachyzoites loaded with Fura-2 diminished the Zaprinast response indicating that they could be impacting a similar store. In the present study we performed additional experiments in which TG was followed by GPN and Zaprinast showing a similar pattern. GPN significantly diminished the Zaprinast response. These results are shown now in Figure S2B. We address these possibilities in the discussion and interpretation of the result. Lines 451-460.

The data in Figures 4A vs 4G and Figures 4B vs 4H indicate that the size of the response to GPN is similar to that with thapsigargin in both the presence and absence of extracellular calcium. This raises the question of whether GPN is only releasing calcium from acidic compartments or whether it acts on the ER calcium stores, as previously suggested by Atakpa et al. 2019 DOI: 10.1242/jcs.223883. Nonetheless, Figure 1H shows that there is a robust calcium response to GPN after the addition of thapsigargin.

The results of the indicated experiments did not exclude the possibility that GPN can also mobilize some calcium from the ER besides acidic organelles. We don’t have any evidence to support that GPN can mobilize calcium from the ER either. Based on our unpublished work, we think GPN mainly release calcium from the PLVAC. We included the mentioned citation and discuss the result considering the possibility that GPN may be acting on more than one store. Lines 451-460.

An important advance in the current work is the use of state-of-the-art approaches with targeted genetically encoded calcium indicators (GECIs) to monitor calcium in important subcellular compartments. The authors have previously done this with the apicoplast, but now add the mitochondria to their repertoire. Despite the absence of a canonical mitochondrial calcium uniporter (MCU) in the Toxoplasma genome, the authors demonstrate the ability of T. gondii mitochondrial to accumulate calcium, albeit at high calcium concentrations. Although the calcium concentrations here are higher than needed for mammalian mitochondrial calcium uptake, there too calcium uptake requires calcium levels higher than those typically attained in the bulk cytosolic compartment. And just like in mammalian mitochondria, the current work shows that ER calcium release can elicit mitochondrial calcium loading even when other sources of elevated cytosolic calcium are ineffective, suggesting a role for ER-mitochondrial membrane contact sites. With these new tools in hand, it will be of great value to elucidate the bioenergetics and transport pathways associated with mitochondrial calcium accumulation in T. gondii.

We thank this reviewer praising our work. Studies of bioenergetics and transport pathways associated with mitochondrial calcium accumulation is part of our future plans mentioned in lines 520-522 and 545.

The current studies of calcium pools and their interactions with the ER and dependence on SERCA activity in T. gondi are complemented by super-resolution microscopy and electron microscopy that do indeed demonstrate the presence of close appositions between the ER and other organelles (see also videos). Thus, the work presented provides good evidence for the ER acting as the orchestrating organelle delivering calcium to other subcellular compartments through contact sites in T. gondi, as has become increasingly clear from work in other organisms.

Thank you

Reviewer #3 (Public review):

This manuscript describes an investigation of how intracellular calcium stores are regulated and provides evidence that is in line with the role of the SERCA-Ca2+ATPase in this important homeostasis pathway. Calcium uptake by mitochondria is further investigated and the authors suggest that ER-mitochondria membrane contact sites may be involved in mediating this, as demonstrated in other organisms.

The significance of the findings is in shedding light on key elements within the mechanism of calcium storage and regulation/homeostasis in the medically important parasite Toxoplasma gondii whose ability to infect and cause disease critically relies on calcium signalling. An important strength is that despite its importance, calcium homeostasis in Toxoplasma is understudied and not well understood.

We agree with the reviewer. Thank you

A difficulty in the field, and a weakness of the work, is that following calcium in the cell is technically challenging and thus requires reliance on artificial conditions. In this context, the main weakness of the manuscript is the extrapolation of data. The language used could be more careful, especially considering that the way to measure the ER calcium is highly artificial - for example utilising permeabilization and over-loading the experiment with calcium. Measures are also indirect - for example, when the response to ionomycin treatment was not fully in line with the suggested model the authors hypothesise that the result is likely affected by other storage, but there is no direct support for that.

The Mag-Fluo-4-based protocol for measuring intraluminal calcium is well established and has been extensively used in mammalian cells, DT40 cells and other cells for measuring intraluminal calcium, activity of SERCA and response to IP3 (Some examples: PMID: 32179239, PMID: 15963563, PMID: 19668195, PMID: 30185837, PMID: 19920131).

Furthermore, we have successfully employed this protocol in previous work, including the characterization of the Trypanosoma brucei IP3R (PMID: 23319604) and the assessment of SERCA activity in Toxoplasma (PMID: 40043955 and 34608145). The citation PMID: 32179239 provides a detailed description of the protocol, including references to its prior use. In addition, the schematic at the top of Figure 2 summarizes the experimental workflow, reinforcing that the protocol follows established methodologies. We included more references and an expanded discussion, lines 425-435.

We respectfully disagree with the concern regarding potential calcium overloading. The cells used in our assays were permeabilized, which is a critical step that allows to precisely control calcium concentrations. All experiments were conducted at 220 nM free calcium, a concentration within the physiological range of cytosolic calcium fluctuations. This concentration was consistently used across all studies described above. Importantly, permeabilization ensures that the dye present in the cytosol becomes diluted, and allows MgATP (which cannot cross intact membranes) to access the ER membrane, in addition to be able to expose the ER to precise calcium concentrations.

The Mag-Fluo-4 loading conditions are designed to allow compartmentalization of the indicator to all intracellular compartments and the calcium uptake stimulated by MgATP exclusively occurs in the compartment occupied by SERCA as only SERCA is responsive to MgATP-dependent transport in this experimental setup

Regarding the use of IO, we would like to clarify that its broad-spectrum activity is welldocumented. As a calcium ionophore, IO facilitates calcium release across multiple membranes, and not just the ER leading to a more substantial calcium release compared to the more selective effect of TG. The results observed with IO were consistent with this expected broader activity and support our interpretation.

Lastly, we emphasize that the experiment in Figure 2 was designed specifically to assess SERCA activity in situ under defined conditions. It was not intended to provide a comprehensive characterization of the role of TgSERCA in the parasite. We now clarify this distinction in the revised Discussion lines 425-435.

Below we provide some suggestions to improve controls, however, even with those included, we would still be in favour of revising the language and trying to avoid making strong and definitive conclusions. For example, in the discussion perhaps replace "showed" with "provide evidence that are consistent with..."; replace or remove words like "efficiently" and "impressive"; revise the definitive language used in the last few lines of the abstract (lines 13-17); etc. Importantly we recommend reconsidering whether the data is sufficiently direct and unambiguous to justify the model proposed in Figure 7 (we are in favour of removing this figure at this early point of our understanding of the calcium dynamic between organelles in Toxoplasma).

We thank the reviewer for the suggestions and we modified the language as suggested. We limited the use of the word "showed" to references to previously published work. We deleted the other words

Figure 7 is intended as a conceptual model to summarize our proposed pathways, and, like all models, it represents a working hypothesis that may not fully capture the complexity of calcium dynamics in the parasite. In light of the reviewer’s comments, we revised the figure and legend to clearly distinguish between pathways for which there is experimental evidence from those that are hypothetical.

Another important weakness is poor referencing of previous work in the field. Lines 248250 read almost as if the authors originally hypothesised the idea that calcium is shuttled between ER and mitochondria via membrane contact sites (MCS) - but there is extensive literature on other eukaryotes which should be first cited and discussed in this context. Likewise, the discussion of MCS in Toxoplasma does not include the body of work already published on this parasite by several groups. It is informative to discuss observations in light of what is already known.

The sentence in which we state the hypothesis about the calcium transfer refers specifically to Toxoplasma. To clarify this, we have now added the phrase “In mammalian cells” (Line 311) and included additional citations, as suggested by the reviewer. While only a few studies have described membrane contact sites (MCSs) in Toxoplasma, we do cite several pertinent articles (e.g., lines 479-486). We believe that we cited all articles mentioning MCS in T. gondii

However, we must clarify to the reviewer that the primary focus of our study is not to characterize or confirm the presence of MCSs in T. gondii, but rather to demonstrate functional calcium transfer between the ER and mitochondria. Our data support the conclusion that this transfer requires close apposition of these organelles, consistent with the presence of MCSs.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Line 45: change influx to release as Ca2+ influx usually referred to Ca2+ entry from the extracellular space. Same for line 71.

Corrected, line 47 and 73

(2) Line 54: consider toning down the strong statement of 'widely' accepted as ER Ca2+ subdomain heterogeneity remains somewhat debated.

Changed the sentence to “it has been proposed”, Line 56

(3) Line 119-21: A lower release in response to TG is typical and does not reflect TG specific for SERCA. It is due to the slow kinetics of Ca2+ leak out of the ER allowing other buffering and transport mechanisms to act. Also, could be a reflection of the duration after TG treatment to allow complete store depletion. Figure S1A-B shows that there is still Ca2+ in the stores following TG but the TG signal does not go back to baseline arguing that the leak is still active. Hence the current data does not address the specificity of TG for TgSERCA. Please revise the statement accordingly.

Thank for the suggestion, we changed the sentence to this: “This result could reflect the slow kinetics of Ca²⁺ leak from the ER, allowing other buffering and transport mechanisms to mitigate the phenomenon. Alternatively, it may indicate the duration after TG treatment allowing time to complete store depletion. As shown in Figure S1A-B, residual Ca²⁺ remains in the stores after TG treatment, and the TG-induced phenomenon does not return to baseline, suggesting that the leak remains active”. Lines 124-128

(4) Figure 1C: the authors interpret the data 'This Ca2+ influx appeared to be immediately taken up by the ER as the response to TG was much greater in parasites previously exposed to extracellular Ca2+'. I don't understand this interpretation, in Ca2+-containing solution it would expected to have a larger signal as TG is likely to activate store-operated Ca2+ entry which would contribute to a larger cytosolic Ca2+ transient. Does T. gondii have SOCE? It cannot be uptake into the ER as SERCA is blocked. Unless the authors are arguing for another ER Ca2+ uptake pathway? But why are Ca2+ uptake in the ER would lower the signal whereas the data show an increased signal?

We pre-incubated the suspension with calcium to allow filling of the stores, while SERCA is still active, and added thapsigargin (TG) at 400 seconds to measure calcium release. The experiment was designed to introduce the concept that the ER may have access to extracellular calcium, a phenomenon not yet clearly demonstrated in Toxoplasma. We did not expect to have less release by TG but if the ER is not efficient in filling after extracellular calcium entry it would be expected to have a similar response to TG. Yes, it is very possible that when we add TG we are also seeing more calcium entry through the PM as we previously proposed that the increased cytosolic Ca²⁺ may regulate Ca²⁺ entry. However, the evidence does not support that this increased entry would be triggered by store depletion. The experiments with the SERCA mutant (Fig. 4D) shows that in the conditional knockout mutant, the ER is partially depleted, yet this does not lead to enhanced calcium entry, suggesting that the depletion alone is not sufficient to trigger increased influx.

There is no experimental evidence supporting the regulation of calcium entry by store depletion in Toxoplasma (PMID: 24867952). We revised the text to clarify this point and expanded the discussion on store-operated calcium entry (SOCE). While it is possible that a channel similar to Orai exists in Toxoplasma, it is highly unlikely to be regulated by store depletion, as there is no gene homologous to STIM. If store-regulated calcium entry does occur in Toxoplasma, it is likely mediated through a different, still unidentified, mechanism. Lines 461-467.

(5) The choice of adding Ca2+ first followed by TG is curious as it is more difficult to interpret. Would be more informative to add TG, allow the leak to complete, and then add Ca2+ which would allow temporal separation between Ca2+ release from stores and Ca2+ influx from the extracellular space. Was this experiment done? If not would be useful to have the data.

Yes, this experiment was already published: PMID: 24867952 and PMID: 38382669.

It mainly highlighted that increased cytosolic calcium may regulate calcium entry most likely through a TRP channel. See our response to point 4 and the description of the new Fig. S2 in the response to point 7.

(6) Line 136-39: these experiments as designed - partly because of the issues discussed above - do not address the ability of organelles to access extracellular Ca2+ or the state of refilling of intracellular Ca2+ stores. They can simply be interpreted as the different agents (TG, Nig, GPN, CCCP) inducing various levels of Ca2+ influx.

Concerning TG, the experiment shown in Fig. 4D shows that depletion of the ER calcium does not result in stimulation of calcium entry, indicating the absence of classical SOCE activation in Toxoplasma.

To our knowledge, neither mitochondria nor lysosomes (or other acidic compartments) are capable of triggering classical SOCE in mammalian cells.

Given that the ER in Toxoplasma lacks the canonical components required to initiate SOCE, it is unclear why the mitochondria or acidic compartments would be able to do so. While it is possible that T. gondii utilizes an alternative mechanism for store-operated calcium entry, investigating such a pathway would require a comprehensive study. In mammalian systems, it took almost 15 years and the efforts of multiple research groups to identify the molecular components of SOCE. Expecting this complex question to be resolved within the scope of a single study is unrealistic.

Our current data show that the mitochondrion is unable to access calcium from the cytosol, as shown in Figure 5E. Performing a similar experiment for the PLVAC would be ideal; however, expression of fluorescent calcium indicators in this organelle has not been successful. This is likely due to the presence of several proteases that degrade expressed proteins, as well as the acidic environment, which quenches fluorescence. These challenges have made studying calcium dynamics in the PLVAC particularly difficult.

To address the reviewer’s comment, we performed an additional experiment presented in Fig. S2A. In this experiment, we first inhibited SERCA with thapsigargin (TG), preventing calcium uptake into the ER, and subsequently added calcium to the suspension. Under these conditions, calcium cannot be sequestered by the ER. We then applied GPN and quantified the response, comparing it to a similar experimental condition without TG. Indeed, under these conditions, we observed a significant but modest increase in the GPN-induced response, suggesting that the PLVAC may be capable of directly taking up calcium from the cytosol. However, this occurs under conditions of SERCA inhibition which creates nonphysiological conditions with elevated cytosolic calcium levels and the presence of TG may promote additional ER leakage, both of which could artificially enhance PLVAC uptake. Under physiological conditions, with functional SERCA activity, the ER would likely sequester cytosolic calcium more efficiently, thereby limiting calcium availability for PLVAC direct uptake. Thus, while the result is intriguing, it may not reflect calcium handling under normal cellular conditions. See lines 172-178.

(7) Figure 1H-I: I disagree with the authors' interpretation of the results (lines 144-153). The data argue that by blocking ER Ca2+ uptake by TG, other organelles take up Ca2+ from the cytosol where it accumulates due to the leak and Ca2+ influx as is evident from the data allowing more release. The data does not argue for ER Ca2+ tunneling to other organelles. Tunneling would be reduced in the presence of TG (see PMID: 30046136, 24867608).

We partially agree with this concern. In our experiments, TG was used to inhibit SERCA and block calcium uptake into the ER, allowing calcium to leak into the cytosol. We propose that this leaked calcium is subsequently taken up by other intracellular compartments. This effect is observed immediately upon TG addition. However, pre-incubation with TG or knockdown of SERCA reduces calcium storage in the ER, thereby diminishing the transfer of calcium to other stores.

To further support our claim, we performed additional experiments in the absence of extracellular calcium, now presented in Figure 1J-K. We observed that calcium release triggered by GPN or nigericin was significantly enhanced when both agents were added after TG. These results suggest that calcium initially released from the ER can be sequestered by other compartments. As mentioned, we deleted any mention of “tunneling,” but we believe the data support the occurrence of calcium transfer. New results described in lines 166-171.

The experiment in Fig S2A described in the response to (6) also addresses this concern. Under physiological conditions with functional SERCA, cytosolic calcium would likely be rapidly sequestered by the ER, limiting its availability to other compartments. See lines 172178.

(8) Line 175: SERCA-dependent Ca2+ uptake is higher at 880 nM as would be expected yet the authors state that it's optimal at 220 nM Ca2+ ?

Yes, it is true that the SERCA-dependent Ca²⁺ uptake rate is higher at elevated Ca²⁺ concentrations. We chose to use 220 nM free calcium because of several reasons: 1) this concentration is close to physiological cytosolic levels fluctuations; 2) it is commonly used in studies of mammalian SERCA; and 3) calcium uptake is readily detectable at this level. While this may not represent the maximal activity conditions for SERCA, we believe it is a reasonable and physiologically relevant choice for assessing calcium transport activity SERCA-dependent. We added one sentence to the results explaining this reasoning (lines 204-207) and we deleted the word optimal.

(9) Figure 3H: the saponin egress data support the conclusion that organelles Ca2+ take up cytosolic Ca2+ directly without the need for ER tunneling.

The saponin concentration used permeabilizes the host cell membrane, allowing the intracellular tachyzoite to be surrounded with the added higher extracellular calcium concentration. The saponin concentration used does not affect the tachyzoite membrane as the parasite is still moving and calcium oscillations were clearly seen under similar conditions (PMID: 26374900 ). The resulting calcium increase in the tachyzoite cytosol is what stimulates parasite motility and egress. Since SERCA activity is reduced in the mutant, cytosolic calcium accumulates more rapidly, reaching the threshold for egress sooner and thereby accelerating parasite exit. The result does not support that the other stores contribute to this because of the Ionomycin response, which shows that egress is diminished in the mutant, likely because the calcium stores are depleted. We added an explanation in the results, lines 262-269 and the discussion, lines 532-539.

(10) Figure S2: the HA and SERCA signals do not match perfectly? Could this reflect issues with HA tagging, potentially off-target effects? Was this tested?

These are not off-target effects, as we did not observe them in the control cells lacking HA tagging. The HA signal also disappeared after treatment with ATc, further confirming that the IFA signal is specific. We agree with the reviewer that the signals do not align perfectly. This discrepancy could be due to differences in antibody accessibility or the fact that the two antibodies recognize different regions of the protein. We added a sentence about this in the result; lines 240-243.

Reviewer #2 (Recommendations for the authors):

The description of the data of Figures 1B and S1A starting on line 108 would be easier to follow if Figure S1A was actually incorporated into Figure 1. It is not clear why these two complementary experiments were separated since they are both equally important in understanding and interpreting the data.

We re-arranged figure 1 and incorporated S1A now as Fig 1C.

As noted in the public comments, loading of fura2/AM can result in compartmentalized fura2, which can contaminate the cytosolic calcium measurements and might modify free calcium levels and calcium storage capacity in intracellular organelles. This can be assessed using the digitonin permeabilization method used in the MagFluo4 measurements, but in this case, detecting the fura2 signal remaining after cell permeabilization.

As suggested by the reviewer, we measured Fura-2 compartmentalization by permeabilizing cells with digitonin as we do for the Mag-Fluo-4 and the fluorescence was reduced almost completely and was unresponsive to any additions (see Author response image 1).

Author response image 1.

T. gondii tachyzoites in suspension exposed to Thapsigargin Calcium and GPN. The dashed lines shows and experiments using the same conditions but parasites were permeabilized with digitonin shows a similar experiment with parasites exposed to MgATP.to release the cytosolic Fura. Part B

Following the public comment regarding the residual calcium mobilization response to Zaprinast observed after 24 h ATc knockdown of SERCA (Figsures 4E, 4F, as explained in the legend to Figure 4), was there still a response to Zaprinast after 48 h knockdown, where the thapsigargin response was apparently fully ablated?

Unfortunately, we were unable to perform this experiment as it is not possible to obtain sufficient cells at 48 h with ATc. Due to the essential role of TgSERCA, parasites are unable to replicate after 24 h.

As noted in the public comments, the data in Figure 4A vs 4G and Figure 4B vs 4H appear to show that the calcium responses to GPN are similar to that with thapsigargin, which seems unexpected if the acidic compartment is loaded from the ER. The results with GPN addition after thapsigargin (Figure 1H) argue against this, but the authors should still cite the work of Atakpa et al.

We think that the reviewer is concerned that GPN may also be acting on the ER. This is a possibility that we considered, and we now included the suggested citation (line 457). However, we believe that it is difficult to directly compare the responses, as the kinetics of calcium release from the ER may differ from those of release from the PLVAC. This could be due to differences in the calcium buffering capacity between the two compartments. Additionally, it is possible that calcium leaked from the ER is more efficiently sequestered by other stores or extruded through the plasma membrane than calcium released from the PLVAC. Besides, GPN is known to have a more disruptive effect on membranes compared to TG, which may also influence their responses. As noted by the reviewer, Figure 1H also supports the idea that the acidic compartment is loaded from the ER.

The abbreviation for the plant-like vacuolar compartment (PLVAC) only appears in a figure legend but should be defined in the main text on first use.

Corrected, lanes 140-143

The authors should cite the previous study of Borges-Pereira et al., 2020 (PMID: 32848018) that also demonstrates the incomplete overlap of the calcium pools mobilized by thapsigargin and CPA in P. falciparum. The ability to measure calcium in intracellular stores using MagFluo4 opens the possibility to further investigate this discrepancy between CPA and thapsigargin, but CPA does not appear to have been used in the permeabilized cell experiments with MagFluo4. I would suggest that this could be added to Figure 2 and/or Figure 4, or at least as a supplementary figure.

In response to this reviewer’s critique we performed additional experiments with Mag-Fluo4 loaded parasites. These are presented in the new Figure S3. We added CPA and TG and combined them to inhibit SERCA and to allow calcium leak from the loaded organelle. Under these conditions, we observed a very similar leak rate after the addition of the inhibitors as measured by the slope of Ca²⁺ leak. We believe that the leak rate is most likely determined by the intrinsic ER mechanism. See the discussion of this result in lines 436442 and the previous response to the same reviewer comment.

Reviewer #3 (Recommendations for the authors):

Suggestions for improved or additional experiments, data, or analyses

(1) Figure 1A is not mentioned in the main text even though it is discussed.

Corrected

(2) Figure 1G: Values do not match, how can GPN be so high?

These figures were replaced by new traces and individual quantification analyses for each experiment.

(3) Figure 1H and I: Is this type of data/results also available for the mitochondrion?

Unfortunately, we were not able to include this experiment because we were unable to accurately quantify the mitochondrial calcium release. Instead, we used mitochondrial GECIs and the results are shown in Figure 5 to study mitochondrial calcium uptake.

(4) Figure 1H: where does the calcium go after GPN addition? Taken up by another calcium store?

Most likely calcium is extruded through the plasma membrane by the activity of the Calcium ATPase TgA1.

However, the reviewer’s suggestion is also possible, and calcium could be taken by another store like the mitochondrion. In this regard, we did observe a large mitochondrial calcium increase (parasites expressing SOD2-GCaMp6) after adding GPN (Fig 5I) suggesting that the mitochondrion may take calcium from the organelle targeted by GPN. However, the calcium affinity of the mitochondrion is very low, so the concentration of calcium needs to be very high to activate it and these concentrations are most likely achieved at the microdomains formed between the mitochondrion and other organelles.

(5) Figure 2B-C: Further explanation of why these particular values were chosen for the follow-up experiments would be helpful for the reader.

We tested a wide range of MgATP and free calcium concentrations to measure ER Ca²⁺ uptake catalyzed by TgSERCA. The concentrations shown fall within the linear range.

We followed the free calcium concentrations used by studies of mammalian SERCA (https://doi.org/10.1016/j.ceca.2020.102188 ). In this protocol they used 220 nM free calcium, which was close to cytosolic Ca²⁺ levels. TgSERCA can take up calcium efficiently at this concentration, as shown in Fig 2. We used less MgATP than the mammalian cell protocols, since we did not observe a significant increase in SERCA activity beyond 0.5 mM MgATP. We added one more sentence explaining in the results, lines 204-207.

(6) Figure 3E: Revise the error bar? (and note that colours do not match the graph legend).

The colors do match; the problem visualizing it is because vacuoles containing a single parasite are virtually absent in the control group without ATc treatment.

(7) Figure 3H: 'Interestingly, when testing egress after the addition of saponin in the presence of extracellular Ca2+, we observed that the tachyzoites egressed sooner (Figure 3H, saponin egress).' This is the only graph showing egress timing, and thus it is not clear what is the comparison. The egressed here is sooner compared to what condition? Egress in the absence of Ca2+? This requires clarification and might require the control data to be added.

In the saponin experiment we compare time to egress of the mutant grown with or without ATc. The measurement is for time to egress after adding saponin. This experiment is in the presence of extracellular calcium. The protocol was previously used to measure time to egress: PMID: 40043955, PMID: 38382669, PMID: 26374900. See also response to question 9 of reviewer 1.

(8) Figure 4C: There is a small peak appearing right after TG addition this should be discussed and explained.

This trace was generated in a different fluorometer, F-4000. This was an artifact due to jumping of the signal when adding TG. Multiple repeats of the same experiment in the newer F7000 did not show the peak. We included in the MM the use of the F-4000 fluorometer for some experiments. We apologize for the omission. Lines 609-610

(9) Figure 5A: An important control that is missing is co-localisation with a mitochondrial marker.

The expression of the SOD2-GCaMP6 has been characterized: PMID: 31758454

(10) Figure 5H: This line was made for this study however the line genetic verification is missing.

In response to this concern we now include a new Figure S5 showing the fluorescence of GCaMP6 in the mitochondrion of the iDTgSERCA mutant (Fig. S5A). We include several parasites. In addition, we show fluorescence measurements after addition of Calcium showing that the cells are unresponsive indicating that the indicator is not in the cytosol. Lines 650-651 and 344-348.

(11) Figure 6D: since the membranes are hard to see, it is not clear whether the arrows show structures that are in line with the definition of membrane contact sites. The authors should provide an in-depth analysis of the length of the interaction between the membranes where the distance is less than 30 nM, and discuss how many structures corresponding to the definition were analysed.

All the requested details are now included in the legend to Figure S3.

Minor corrections to the text and figures

(1) Unify statistical labelling throughout the paper replacing *** with p values.

Corrected. We changed the *** with the actual p value in some figures. For figure 2 and Fig S1, we still use the *** due to the space limitation.

(2) Unify ATC vs ATc throughout the paper.

Corrected

(3) Unify capitalization of line name (iΔTgserca/i ΔTgSERCA) throughout the paper.

Corrected

(4) Unify capitalization of p value (p/P) throughout the paper.

Corrected in figures

(5) Unify Fig X vs Fig. X throughout the text.

Corrected

(6) Add values of scale bars to legends (eg Figure S2).

Corrected

(7) What is the time point for the data in Figures 4E-H, 5H, and S3? 24hrs? include in the legend.

Added 24 h to the legends. Fig S3 is now S4.

(8) Figure 3F: The second graph is NS thus perhaps no need for the p-value?

Corrected

(8) Figure 3G: Worth considering swapping the two around: first attachment and then invasion?

Corrected. Invasion and attachment bars were swapped.

(10) Figure 4A/B: Wrong colour match for Figure 4B.

Corrected

(11) Figure 4F: In the main text, the authors reference to Figure 1F, correct to 4F.

Corrected

(12) Figure 4H: In the main text, authors reference to Figure 1H, correct to 4H.

Corrected

Author response:

The following is the authors’ response to the original reviews.

eLife assessment

This manuscript presents useful findings on several phage from deep sea isolates of Lentisphaerae strains WC36 and zth2 that further our understanding of deep sea microbial life. The manuscript's primary claim is that phage isolates augment polysaccharide use in Pseudomonas bacteria via auxiliary metabolic genes (AMGs). However, the strength of the evidence is incomplete and does not support the primary claims. Namely, there are not data presented to rule out phage contamination in the polysaccharide stock solution, AMGs are potentially misidentified, and there is missing evidence of successful infection.

Thanks for the Editor’s and Reviewers’ positive and constructive comments, which help us improve the quality of our manuscript entitled “Deep-sea bacteriophages facilitate host utilization of polysaccharides” (paper#eLife-RP-RA-2023-92345). The comments are valuable, and we have studied the comments carefully and have made corresponding revisions according to the suggestions. We removed some uncertain results and strengthened other parts of the manuscript, which evidently improved the accuracy and impact of the revised version. Revised portions are marked in blue in the modified manuscript. Please find the detailed responses as following.

Public Reviews:

Reviewer #1 (Public Review):

Summary: This manuscript describes the identification and isolation of several phage from deep sea isolates of Lentisphaerae strains WC36 and zth2. The authors observe induction of several putative chronic phages with the introduction of additional polysaccharides to the media. The authors suggest that two of the recovered phage genomes encode AMGs associated with polysaccharide use. The authors also suggest that adding the purified phage to cultures of Pseudomonas stutzeri 273 increased the growth of this bacterium due to augmented polysaccharide use genes from the phage. While the findings were of interest and relevance to the field, it is my opinion that several of the analysis fall short of supporting the key assertions presented.

Thanks for your comments. We removed some uncertain results and strengthened other parts of the manuscript, which evidently improved the accuracy and impact of the revised version. Please find the detailed responses as following.

Strengths: Interesting isolate of deep sea Lentisphaerae strains which will undoubtedly further our understanding of deep sea microbial life.

Thanks for your positive comments.  

Weaknesses:

(1) Many of the findings are consistent with a phage contamination in the polysaccharide stock solution. 

Thanks for your comments. We are very sure that the phages are specifically derived from the Lentisphaerae strain WC36 but not the polysaccharide stock solution. The reasons are as following: (1) the polysaccharide stock solution was strictly sterilized to remove any phage contamination; (2) we have performed multiple TEM checks of the rich medium supplemented with 10 g/L laminarin alone (Supplementary Fig. 1A) or in 10 g/L starch alone (Supplementary Fig. 1B), and there were not any phage-like structures, which confirmed that the polysaccharides (laminarin/starch) we used were not contaminated with any phage-like structures; in addition, we also observed the polysaccharides (laminarin/starch) directly by TEM and did not find any phage-like structures (Supplementary Fig. 2); (3) the polysaccharide (starch) alone could not promote the growth of Pseudomonas stutzeri 273, however, the supplement of starch together with the extracted Phages-WC36 could effectively facilitate the growth of Pseudomonas stutzeri 273 (Author response image 1). The above results clearly indicated the phages were derived from the Lentisphaerae strain WC36 but not the polysaccharide stock solution. 

Author response image 1.

Growth curve and status of Pseudomonas stutzeri 273 cultivated in basal medium, basal medium supplemented with 20 μl/mL Phages-WC36, basal medium supplemented with 5 g/L starch, basal medium supplemented with 5 g/L starch and 20 μl/mL Phages-WC36. 

(2) The genes presented as AMGs are largely well known and studied phage genes which play a role in infection cycles.

Thanks for your comments. Indeed, these AMGs may be only common in virulent phages, while have never been reported in chronic phages. In virulent phages, these genes typically act as lysozymes, facilitating the release of virions from the host cell upon lysis, or injection of viral DNA upon infection. However, the chronic phages do not lyse the host. Therefore, the persistence of these genes in chronic phages may be due to their ability to assist the host in metabolizing polysaccharides. Finally, according to your suggestions, we have weakened the role of AMGs and added “potential” in front of it. The detailed information is shown below.

(3) The evidence that the isolated phage can infect Pseudomonas stutzeri 273 is lacking, putting into question the dependent results.

Thanks for your comments. Actually, we selected many marine strains (Pseudomonadota, Planctomycetes, Verrucomicrobia, Fusobacteria, and Tenericutes isolates) to investigate whether Phages-WC36 could assist them in degradation and utilization of polysaccharides, and found that Phages-WC36 could only promote the growth of strain 273. It is reported that filamentous phages could recognize and bind to the host pili, which causes the pili to shrink and brings the filamentous phages closer to and possibly through the outer membrane of host cells. The possible mechanism of other chronic phages release without breaking the host might be that it was enclosed in lipid membrane and released from the host cells by a nonlytic manner. Thus, these chronic phages may have a wider host range. However, we were unable to further reveal the infection mechanism due to some techniques absence. Therefore, according to your suggestions, we have deleted this section in the revised manuscript.

Reviewer #1 (Recommendations For The Authors):

I have previously reviewed this manuscript as a submission to another journal in 2022. My recommendations here mirror those of my prior suggestions, now with further added details.

Thanks for your great efforts for reviewing our manuscript and valuable suggestions for last and this versions.

Specific comments:

Comment 1: Line 32. Rephrase to "polysaccharides cause the induction of multiple temperate phages infecting two strains of Lentisphaerae (WC36 and zth2) from the deep sea."

Thanks for your positive suggestion. We have modified this description as “Here, we found for the first time that polysaccharides induced the production of multiple temperate phages infecting two deep-sea Lentisphaerae strains (WC36 and zth2).” in the revised manuscript (Lines 31-33). 

Comment 2: Line 66. "Chronic" infections are not "lysogenic" as described here, suggesting the former is a subcategory of the latter. If you are going to introduce lifecycles you need a brief sentence distinguishing "chronic" from "lysogenic"

Thanks for your positive suggestion. We added this sentence as “Currently, more and more attention has been paid to chronic life cycles where bacterial growth continues despite phage reproduction (Hoffmann Berling and Maze, 1964), which was different from the lysogenic life cycle that could possibly lyse the host under some specific conditions.” in the revised manuscript (Lines 66-69).

Comment 3: Line 72. Please avoid generalized statements like "a hand-full" (or "plenty" line 85). Try to be at least somewhat quantitative regarding how many chronic phages are known. This is a fairly common strategy among archaeal viruses. 

Thanks for your suggestion. Given that some filamentous phages also have a chronic life cycle that is not explicitly reported, we cannot accurately estimate their numbers. According to your suggestions, we have modified these descriptions as “however, to our best knowledge, only few phages have been described for prokaryotes in the pure isolates up to date (Roux et al., 2019; Alarcón-Schumacher et al., 2022; Liu et al., 2022).” in the revised manuscript (Lines 73-75). In addition, the number of chronic phages in the biosphere cannot be accurately estimated, according to the latest report (Chevallereau et al., 2022), which showed that “a large fraction of phages in the biosphere are produced through chronic life cycles”. Therefore, we have modified this description as “Therefore, a large percentage of phages in nature are proposed to replicate through chronic life cycles” in the revised manuscript (Lines 87-88). 

Comment 4: Line 93. While Breitbart 2012 is a good paper to cite here, there have been several, much more advanced analysis of the oceans virome. https://doi.org/10.1016/j.cell.2019.03.040 is one example, but there are several others. A deeper literature review is required in this section.  

Thanks for your valuable suggestions. We have added some literatures and modified this description as “A majority of these viruses are bacteriophages, which exist widely in oceans and affect the life activities of microbes (Breitbart, 2012; Roux et al., 2016; Gregory et al., 2019; Dominguez-Huerta et al., 2022).” in the revised manuscript (Lines 94-97). 

References related to this response:

Roux, S., Brum, J.R., Dutilh, B.E., Sunagawa, S., Duhaime, M.B., Loy, A., Poulos, B.T., Solonenko, N., Lara, E., Poulain, J., et al. (2016) Ecogenomics and potential biogeochemical impacts of globally abundant ocean viruses. Nature 537:689-693. 

Gregory, A.C., Zayed, A.A., Conceição-Neto, N., Temperton, B., Bolduc, B., Alberti, A., Ardyna, M., Arkhipova, K., Carmichael, M., Cruaud, C., et al. (2019) Marine DNA Viral Macro- and Microdiversity from Pole to Pole. Cell 177:1109-1123.e1114. 

Dominguez-Huerta, G., Zayed, A.A., Wainaina, J.M., Guo, J., Tian, F., Pratama, A.A., Bolduc, B., Mohssen, M., Zablocki, O., Pelletier, E., et al. (2022) Diversity and ecological footprint of Global Ocean RNA viruses. Science 376:1202-1208.

Comment 5: Line 137. I see the phage upregulation in Figure 1, however in the text and figure it would be good to also elaborate on what the background expression generally looks like. Perhaps a transcriptomic read normalization and recruitment to the genome with a display of the coverage map, highlighting the prophage would be helpful. Are the polysacharides directly influencing phage induction or is there some potential for another cascading effect?  

Thanks for your comments. We have elaborated all expressions of phage-associated genes under different conditions in the Supplementary Table 1, which showed that the background expressions were very low. The numbers in Fig. 1C were the gene expressions (by taking log2 values) of strain WC36 cultured in rich medium supplemented with 10 g/L laminarin compared with the rich medium alone.

In addition, our RT-qPCR results (Fig. 1D) also confirmed that these genes encoding phage-associated proteins were significantly upregulated when 10 g/L laminarin was added in the rich medium. According to your suggestions, we have modified this description as “In addition to the up-regulation of genes related to glycan transport and degradation, when 10 g/L laminarin was added in the rich medium, the most upregulated genes were phage-associated (e. g. phage integrase, phage portal protein) (Fig. 1C and Supplementary Table 1), which were expressed at the background level in the rich medium alone.” in the revised manuscript (Lines 136-140). Based on the present results, we speculate that polysaccharides might directly induce phage production, which needs to be verified by a large number of experiments in the future.

Comment 6: Line 179. We need some assurance that phage was not introduced by your laminarin or starch supplement. Perhaps a check on the TEM/sequencing check of supplement itself would be helpful? This may be what is meant on Line 188 "without culturing bacterial cells" however this is not clearly worded if that is the case. Additional note, further reading reinforces this as a key concern. Many of the subsequent results are consistent with a contaminated starch stock. 

Thanks for your comments. We are very sure that the phages are specifically derived from the Lentisphaerae strain WC36 but not the polysaccharide stock solution. The reasons are as following: (1) we have performed multiple TEM checks of the rich medium supplemented with 10 g/L laminarin alone (Supplementary Fig. 1A) or in 10 g/L starch alone (Supplementary Fig. 1B), and there were not any phage-like structures, which confirmed that the polysaccharides (laminarin/starch) we used are not contaminated with any phage-like structures. In addition, we also observed the polysaccharides (laminarin/starch) directly by TEM and did not find any phage-like structures (Supplementary Fig. 2). According to your suggestions, we have modified this description as “We also tested and confirmed that there were not any phage-like structures in rich medium supplemented with 10 g/L laminarin alone (Supplementary Fig. 1A) or in 10 g/L starch alone (Supplementary Fig. 1B), ruling out the possibility of phage contamination from the polysaccharides (laminarin/ starch).” in the revised manuscript (Lines 158-162) and “Meanwhile, we also checked the polysaccharides (laminarin/ starch) in rich medium directly by TEM and did not find any phage-like structures (Supplementary Fig. 2).” in the revised manuscript (Lines 178-180). (2) the polysaccharide stock solution was strictly sterilized to remove any phage contamination. (3) the polysaccharide (starch) alone could not promote the growth of Pseudomonas stutzeri 273, however, the supplement of starch together with the extracted Phages-WC36 could effectively facilitate the growth of Pseudomonas stutzeri 273 (Response Figure 1). The above results clearly indicated the phage was derived from the Lentisphaerae strain WC36 but not the polysaccharide stock solution. 

In addition, given that polysaccharide was a kind of critical energy source for most microorganisms, we sought to ask whether polysaccharide also induces the production of bacteriophages in other deep-sea bacteria. To this end, we cultured deep-sea representatives from other four other phyla (including Chloroflexi, Tenericutes, Proteobacteria, and Actinobacteria) in the medium supplemented with laminarin/starch, and checked the supernatant of cells suspension through TEM as described above. We could not find any phage-like structures in these cells suspension (Author reaponse image 2), which also confirmed that there was no phage contamination in the polysaccharides.

Author response image 2.

Growth curve and status of Pseudomonas stutzeri 273 cultivated in basal medium, basal medium supplemented with 20 μl/mL Phages-WC36, basal medium supplemented with 5 g/L starch, basal medium supplemented with 5 g/L starch and 20 μl/mL Phages-WC36.   

Author response image 3.

TEM observation of the supernatant of cells suspension of a Chloroflexi strain, a Tenericutes strain, a Proteobacteria strain and an Actinobacteria strain that cultivated in the rich medium supplemented with 10 g/L laminarin and 10 g/L starch. No phage-like particles could be observed.  

Comment 7: Line 223. Correct generalized wording "long time". 

Thanks for your comments. We have changed “after for a long time” to “after 30 days” in the revised manuscript (Line 197).

Comment 8: Line 229. Please more explicitly describe what these numbers are (counts of virion like structures - filamentous and hexagonal respectively?), the units (per µL?), and how these were derived. The word "around" should be replaced with mean and standard deviation values for each count from replicates, without which these are not meaningful.

Thanks for your comments. The average numbers per microliter (µL) of filamentous and hexagonal phages in each condition were respectively calculated by randomly choosing ten TEM images. According to your suggestions, we have modified this description as “Specifically, the average number per microliter of filamentous phages (9.7, 29 or 65.3) extracted from the supernatant of strain WC36 cultured in rich medium supplemented with 10 g/L laminarin for 5, 10 or 30 days was higher than that cultured in rich medium supplemented with 5 g/L laminarin (4.3, 13.7 or 35.3) (Fig. 3B). The average number per microliter of hexagonal phages (9, 30, 46.7) extracted from the supernatant of strain WC36 cultured in rich medium supplemented with 10 g/L laminarin for 5, 10 or 30 days was higher than that cultured in rich medium supplemented with 5 g/L laminarin (4, 11.3 or 17.7) (Fig. 3C).” in the revised manuscript (Lines 203-210).

Comment 9: Line 242. This section should be included in the discussion of Figure 2 - around line 194.

Thanks. According to your suggestion, we have moved this section to the discussion corresponding to Figure 2 (Lines 183-191).

Comment 10: Figure 3. Stay consistent in the types of figures generated per strain. Figure 3A should be a growth curve.

Thanks for your comments. Actually, figure 3A was a growth curve, the corresponding description “(A) Growth curve of strain WC36 cultivated in either rich medium alone or rich medium supplemented with 5 g/L or 10 g/L laminarin for 30 days.” was shown in the Figure 3A legend in this manuscript.

Comment 11: Line 312. Move the discussion of AMGs to after the discussion of the phage genome identification.

Thanks for your valuable comments. According to your suggestions, we have moved the discussion of AMGs to after the discussion of the phage genome identification.

Comment 12: Line 312. It would be informative to sequence in-bulk each of your treatments as opposed to just sequencing the viral isolates (starch and no host included) to see what viruses can be identified in each. ABySS is also not a common assembler for viral analysis. Is there literature to support it as a sufficient tool in assembling viral genomes? What sequencing depths were obtained in your samples?

Thanks for your comments. In previous studies, we did sequence the starch or laminarin alone (no host included) and did not detect any phage-related sequences. The introduction of ABySS software was shown in these literatures (Jackman SD, Vandervalk BP, Mohamadi H, Chu J, Yeo S, Hammond SA, Jahesh G, Khan H, Coombe L, Warren RL, Birol I. ABySS 2.0: resource-efficient assembly of large genomes using a Bloom filter. Genome Res. 2017 May;27(5):768-777; Simpson JT, Wong K, Jackman SD, Schein JE, Jones SJ, Birol I. ABySS: a parallel assembler for short read sequence data. Genome Res. 2009 Jun;19(6):1117-23.), which were also used to assemble viral genomes in these literatures (Guo Y, Jiang T. First Report of Sugarcane Mosaic Virus Infecting Goose Grass in Shandong Province, China. Plant Dis. 2024 Mar 21. doi: 10.1094/PDIS-11-23-2514-PDN; Tang M, Chen Z, Grover CE, Wang Y, Li S, Liu G, Ma Z, Wendel JF, Hua J. Rapid evolutionary divergence of Gossypium barbadense and G. hirsutum mitochondrial genomes. BMC Genomics. 2015 Oct 12;16:770.). The sequencing depth of the phages of strain WC36 and zth2 were 350x and 365x, respectively.

Comment 13: Line 323. Replace "eventually" with more detail about what was done to derive the genomes. Were these the only four sequences identified as viral?

Thanks for your comments. We have used the ABySS software (http://www.bcgsc.ca/platform/bioinfo/software/abyss) to perform genome assembly with multiple-Kmer parameters. VIBRANT v1.2.1 (Kieft et al., 2020), DRAM-v (Shaffer et al., 2020), VirSorter v1.0.5 (with categories 1 (“pretty sure”) and 2 (“quite sure”)) (Roux et al., 2015) and VirFinder v1.1 (with statistically significant viral prediction: score > 0.9 and P-value < 0.05) (Ren et al., 2017) with default parameters were used to identify viral genomes from these assembly sequences by searching against the both cultured and non-cultured viral NCBI-RefSeq database (http://blast.ncbi.nlm.nih.gov/) and IMG/VR database (Camargo et al., 2023). The GapCloser software (https://sourceforge.net/projects/soapdenovo2/files/GapCloser/) was subsequently applied to fill up the remaining local inner gaps and correct the single base polymorphism for the final assembly results. All the detailed processes were described in the supplementary information. The virus sequences with higher scores are only these four, but they are not complete genomes. Some virus sequences with shorter sequences and lower scores were excluded.

Comment 14: Line 328. We need some details about the host genomes here. How were these derived? What is their completeness/contamination? What is their size? If the bins are poor, these would not serve as a reliable comparison to identify integrated phage.

Thanks for your comments. For genomic sequencing, strains WC36 and zth2 were grown in the liquid rich medium supplemented with 5 g/L laminarin and starch and harvested after one week of incubation at 28 °C. Genomic DNA was isolated by using the PowerSoil DNA isolation kit (Mo Bio Laboratories Inc., Carlsbad, CA). Thereafter, the genome sequencing was carried out with both the Illumina NovaSeq PE150 (San Diego, USA) and Nanopore PromethION platform (Oxford, UK) at the Beijing Novogene Bioinformatics Technology Co., Ltd. A complete description of the library construction, sequencing, and assembly was performed as previously described (Zheng et al., 2021). We used seven databases to predict gene functions, including Pfam (Protein Families Database, http://pfam.xfam.org/), GO (Gene Ontology, http://geneontology.org/) (Ashburner et al., 2000), KEGG (Kyoto Encyclopedia of Genes and Genomes, http://www.genome.jp/kegg/) (Kanehisa et al., 2004), COG (Clusters of Orthologous Groups, http://www.ncbi.nlm.nih.gov/COG/) (Galperin et al., 2015), NR (Non-Redundant Protein Database databases), TCDB (Transporter Classification Database), and Swiss-Prot (http://www.ebi.ac.uk/uniprot/) (Bairoch and Apweiler, 2000). A whole genome Blast search (E-value less than 1e-5, minimal alignment length percentage larger than 40%) was performed against above seven databases.

The completeness of the genomes of strains WC36 and zth2 were 100%, which were checked by the CheckM v1.2.2. The size of the genome of strains WC36 and zth2 were 3,660,783 bp and 3,198,720bp, respectively. The complete genome sequences of strains WC36 and zth2 presented in this study have been deposited in the GenBank database with accession numbers CP085689 and CP071032, respectively. 

Moreover, to verify whether the absence of microbial contamination in phage sequencing results, we used the new alignment algorithm BWA-MEM (version 0.7.15) to perform reads mapping of host WGS to these phages. We found that all the raw reads of host strains (WC36 and zth2) were not mapping to these phages sequences (Author response image 3, shown as below). In addition, we also performed the evaluation of the assembly graph underlying the host consensus assemblies. Clean reads were mapped to the bacterial complete genome sequences by the Bowtie 2 (version 2.5.0), BWA (version 0.7.8) and SAMTOOLS (version 0.1.18). The results showed that the total mismatch rate of strains WC36 and zth2 were almost 0% and 0.03%, respectively (Author response table 1, shown as below). In addition, we also collected the cells of strains WC36 and zth2, and then sent them to another company for whole genome sequencing (named WC36G and ZTH, GenBank accession numbers CP151801 and CP119760, respectively). The completeness of the genomes of strains WC36G and ZTH were also 100%. The size of the genome of strains WC36G and ZTH were 3,660,783bp and 3,198,714bp, respectively. The raw reads of strains WC36G and zth2 were also not mapping to the phages sequences. Therefore, we can confirm that these bacteriophage genomes were completely outside of the host chromosomes. 

Author response image 4.

The read mapping from WGS to phage sequences.

Author response table 1.

Sequencing depth and coverage statistics.

References related to this response:

Zheng, R., Liu, R., Shan, Y., Cai, R., Liu, G., and Sun, C. (2021b) Characterization of the first cultured free-living representative of Candidatus Izemoplasma uncovers its unique biology ISME J 15:2676-2691. 

Ashburner, M., Ball, C.A., Blake, J.A., Botstein, D., Butler, H., Cherry, J.M., Davis, A.P., Dolinski, K., Dwight, S.S., Eppig, J.T., et al. (2000) Gene ontology: tool for the unification of biology. The Gene Ontology Consortium Nat Genet 25:25-29. 

Kanehisa, M., Goto, S., Kawashima, S., Okuno, Y., and Hattori, M. (2004) The KEGG resource for deciphering the genome Nucleic Acids Res 32:D277-280. 

Galperin, M.Y., Makarova, K.S., Wolf, Y.I., and Koonin, E.V. (2015) Expanded microbial genome coverage and improved protein family annotation in the COG database Nucleic Acids Res 43:D261-269. 

Bairoch, A., and Apweiler, R. (2000) The SWISS-PROT protein sequence database and its supplement TrEMBL in 2000 Nucleic Acids Res 28:45-48.

Comment 15: Line 333. This also needs some details. What evidence do you have that these are not chromosomal? If not chromosomal where can they be found? Sequencing efforts should also be able to yield extrachromosomal elements such as plasmids etc... If you were to sequence your purified isolate cultures from the rich media alone and include all assemblies (not just those binned for example) as a reference, would you be able to recruit viral reads? The way this reads suggests that Chevallereau et al., worked specifically with these phage, which is not the case - please rephrase.

Thanks for your comments. We carefully compared the bacteriophage genomes with those of the corresponding hosts (strains WC36 and zth2) using Galaxy Version 2.6.0 (https://galaxy.pasteur.fr/) (Afgan et al., 2018) with the NCBI BLASTN method and used BWA-mem software for read mapping from host whole genome sequencing (WGS) to these bacteriophages. These analyses both showed that the bacteriophage genomes are completely outside of the host chromosomes. Therefore, we hypothesized that the phage genomes might exist in the host in the form similar to that of plasmid.

Comment 16: Line 335. More to the point here that we need confirmation that these phages were not introduced in the polysaccharide treatment

Thanks for your comments. Please find our answers for this concern in the responses for comment 1 of “weakness” part and comment 6 of “Recommendations For The Authors” part.

Comment 17: Line 342. Lacking significant detail here. Phylogeny based on what gene(s), how were the alignments computed/refined, what model used etc..?

Thanks for your comments. According to your suggestions, all the related information was shown in this section “Materials and methods” of this manuscript. The maximum likelihood phylogenetic tree of Phage-WC36-2 and Phage-zth2-2 was constructed based on the terminase large subunit protein (terL). These proteins used to construct the phylogenetic trees were all obtained from the NCBI databases. All the sequences were aligned by MAFFT version 7 (Katoh et al., 2019) and manually corrected. The phylogenetic trees were constructed using the W-IQ-TREE web server (http://iqtree.cibiv.univie.ac.at) with the “GTR+F+I+G4” model (Trifinopoulos et al., 2016). Finally, we used the online tool Interactive Tree of Life (iTOL v5) (Letunic and Bork, 2021) to edit the tree. 

Comment 18: Line 346. How are you specifically defining AMGs in this study? Most of these are well-known and studied phage genes with specific life cycle functions and could not be considered as polysaccharide processing AMGs even though in host cells many do play a role in polysaccharide processing systems. A substantially deeper literature review is needed in this section, which would ultimately eliminate most of these from the potential AMG pools. Further, the simple HMM/BLASTp evalues are not sufficient to support the functional annotation of these genes. At a minimum, catalytic/conserved regions should be identified, secondary structures compared, and phylogenetic analysis (where possible) developed etc... My recommendation is to eliminate this section entirely from the manuscript. 

Categorically:

- Glycoside hydrolase (various families), glucosaminidases, and transglycosylase are all very common to phage and operate generally as a lysins, facilitating the release of virions from the host cell upon lysis, or injection of viral DNA upon infection https://doi.org/10.3389/fmicb.2016.00745 (and citations therein) https://doi.org/10.1016/j.cmi.2023.10.018 etc... In order to confirm these as distinct AMGs we would need a very detailed analysis indicating that these are not phage infection cycle/host recognition related, however I strongly suspect that under such interrogation, these would prove to be as such.

-TonB related systems including ExbB are well studied among phages as part of the trans-location step in infection. These could not be considered as AMGs. https://doi.org/10.1128/JB.00428-19. Other TonB dependent receptors play a role in host recognition.

-Several phage acetyltransferases play a role in suppressing host RNA polymerase in order to reserve host cell resources for virion production, including polysaccharide production. https://doi.org/10.3390/v12090976. Further it has been shown that the E. coli gene neuO (O-acetyltransferase) is a homologue of lambdoid phage tail fiber genes https://doi.org/10.1073/pnas.0407428102. I suspect the latter is also the case here and this is a tail fiber gene.

Thanks for your valuable comments. According to your suggestions, we have reanalyzed these AMGs and made some modifications (the new version Fig. 5A, shown as below). These genes encoding proteins associated with polysaccharide transport and degradation may be only common in virulent phages, and have never been reported in chronic phages. Unlike virulent phages, these genes typically act as lysozymes, facilitating the release of virions from the host cell upon lysis, or injection of viral DNA upon infection, chronic phages do not lyse the host. It is reported that, filamentous phages could recognize and bind to the host pili, which causes the pili to shrink and brings the filamentous phages closer to and possibly through the outer membrane of host cells (Riechmann et al., 1997; Sun et al., 1987). The possible mechanism of other chronic phage release without breaking the host might be that it was enclosed in lipid membrane and released from the host cells by a nonlytic manner. It has recently been reported that the tailless Caudoviricetes phage particles are enclosed in lipid membrane and are released from the host cells by a nonlytic manner (Liu et al., 2022), and the prophage induction contributes to the production of membrane vesicles by Lacticaseibacillus casei BL23 during cell growth (da Silva Barreira et al., 2022). Therefore, the persistence of these genes in chronic phages may be due to their ability to assist the host in metabolizing polysaccharides. 

Finally, according to your suggestions, we have weakened the role of AMGs and added “potential” in front of it.

References related to this response:

Riechmann L, Holliger P. (1997) The C-terminal domain of TolA is the coreceptor for filamentous phage infection of E. coli Cell 90:351-60.

Sun TP, Webster RE. (1987) Nucleotide sequence of a gene cluster involved in entry of E colicins and single-stranded DNA of infecting filamentous bacteriophages into Escherichia coli J Bacteriol 169:2667-74. 

Liu Y, Alexeeva S, Bachmann H, Guerra Martníez J.A, Yeremenko N, Abee T et al. (2022) Chronic release of tailless phage particles from Lactococcus lactis Appl Environ Microbiol 88: e0148321. da Silva Barreira, D., Lapaquette, P., Novion Ducassou, J., Couté, Y., Guzzo, J., and Rieu, A. Spontaneous prophage induction contributes to the production of membrane vesicles by the gram-positive bacterium Lacticaseibacillus casei BL23. mBio_._ 2022;13:e0237522.

Comment 19: Line 354. To make this statement that these genes are missing from the host, we would need to know that these genomes are complete.

Thanks for your comments. The completeness of the genomes of strains WC36 and zth2 were 100%, which were checked by the CheckM v1.2.2. The size of the genome of strains WC36 and zth2 were 3,660,783 bp and 3,198,720bp, respectively. The complete genome sequences of strains WC36 and zth2 presented in this study have been deposited in the GenBank database with accession numbers CP085689 and CP071032, respectively. In addition, we also collected the cells of strains WC36 and zth2, and then sent it to another company for whole genome sequencing (named WC36G and ZTH, GenBank accession numbers CP151801 and CP119760, respectively). The completeness of the genomes of strains WC36G and ZTH were also 100%. The size of the genome of strains WC36G and ZTH were 3,660,783bp and 3,198,714bp, respectively. Therefore, these genomes of strains WC36 and zth2 were complete and circular.    

Comment 20: Figure 5. Please see https://peerj.com/articles/11447/ and https://doi.org/10.1093/nar/gkaa621 for a detailed discussion on vetting AMGs. Several of these should be eliminated according to the standards set in the field. More specifically, and by anecdotal comparison with other inoviridae genomes, for Phage-WC36-1 and Phage-zth2-1, I am not convinced that the transactional regulator and glycoside hydrolase are a part of the phage genome. The phage genome probably ends at the strand switch.

Thanks for your comments. According to your suggestions, we have analyzed these two articles carefully and modified the genome of Phage-WC36-1 and Phage-zth2-1 by anecdotal comparison with other inoviridae genomes. As you said, the transactional regulator and glycoside hydrolase are not a part of the phage genome.

The new version Fig. 5A was shown.

References related to this response:

Shaffer, M., Borton, M.A., McGivern, B.B., Zayed, A.A., La Rosa, S.L., Solden, L.M., Liu, P., Narrowe, A.B., Rodrgíuez-Ramos, J., Bolduc, B., et al. (2020) DRAM for distilling microbial metabolism to automate the curation of microbiome function Nucleic Acids Res 48:8883-8900 

Pratama, A.A., Bolduc, B., Zayed, A.A., Zhong, Z.P., Guo, J., Vik, D.R., Gazitúa, M.C., Wainaina, J.M., Roux, S., and Sullivan, M.B. (2021) Expanding standards in viromics: in silico evaluation of dsDNA viral genome identification, classification, and auxiliary metabolic gene curation PeerJ 9:e11447

Comment 21: Line 380. This section needs to start with detailed evidence that this phage can even infect this particular strain. Added note, upon further reading the serial dilution cultures are not sufficient to prove these phage infect this Pseudomonas. We need at a minimum a one-step growth curve and wet mount microscopy. It is much more likely that some carry over contaminant is invading the culture and influencing OD600. With the given evidence, I am not at all convinced that these phages have anything to do with Pseudomonas polysaccharide use and I recommend either drastically revising this section or eliminating it entirely.

Line 386-389. Could this be because you are observing your added phage in the starch enriched media while no phage were introduced with the "other types of media" so none would be observed? This could have nothing to do with infection dynamics. Further, this would also be consistent with your starch solution being contaminated by phage.

Line 399. Again consistent with the starch media being contaminated.

Line 401-408. This is more likely to do with the augmentation of the media with an additional carbon source and not involving the phage. 

Line 410. I am not convinced that these viruses infect the Pseudomonas strain. Extensive further evidence of infection is needed to make these assertions.  Figure 6A. We need confirmation that the isolate culture remains pure and there are no other contaminants introduced with the phage.

Thanks for your comments. We have proved that the polysaccharides (laminarin/ starch) didn't contaminate any phages above. Actually, we selected many marine strains (Pseudomonadota, Planctomycetes, Verrucomicrobia, Fusobacteria, and Tenericutes isolates) to investigate whether Phages-WC36 could assist them in degradation and utilization of polysaccharides, and found that Phages-WC36 could only promote the growth of strain 273. The presence of filamentous phages and hexagonal phages was detected in the supernatant of strain 273 cultured in basal medium supplemented with 5 g/L starch and 20 μl/mL Phages-WC36. After 3 passages of serial cultivation in basal medium supplemented with 5 g/L starch, we found that filamentous phages and hexagonal phages were also present in basal medium supplemented with starch, but not in the basal medium, which may mean that Phages-WC36 could infect strain 273 and starch is an important inducer. In addition, the Phages-WC36 used in the growth assay of strain 273 were multiple purified and eventually suspended in SM buffer (0.01% gelatin, 50 mM Tris-HCl, 100 mM NaCl and 10 mM MgSO4). Thus, these phages are provided do not contain some extracellular enzymes and/or nutrients. In addition, we set up three control groups in the growth assay of strain 273: basal medium, basal medium supplemented with Phages-WC36 and basal medium supplemented with starch. If the Phages-WC36 contains some extracellular enzymes and/or nutrients, strain 273 could also grow well in the basal medium supplemented only with Phages-WC36. However, the poor growth results of strain 273 cultivated in the basal medium supplemented with Phages-WC36 further confirmed that there were not some extracellular enzymes and/or nutrients in these phages.

Finally, the possible mechanism of the chronic phage release without breaking the host might be that it was enclosed in lipid membrane and released from the host cells by a nonlytic manner. Thus, these chronic phages may have a wider host range. However, we were unable to further disclose the infection mechanism in this paper. Therefore, according to your suggestions, we have deleted this section entirely.

Comment 27: Line 460. Details about how these genomes were reconstructed is needed here.  

Thanks for your comments. According to your suggestions, we have added the detailed information about the genome sequencing, annotation, and analysis as “Genome sequencing, annotation, and analysis of strains WC36 and zth2 For genomic sequencing, strains WC36 and zth2 were grown in the liquid rich medium supplemented with 5 g/L laminarin and starch and harvested after one week of incubation at 28 °C. Genomic DNA was isolated by using the PowerSoil DNA isolation kit (Mo Bio Laboratories Inc., Carlsbad, CA). Thereafter, the genome sequencing was carried out with both the Illumina NovaSeq PE150 (San Diego, USA) and Nanopore PromethION platform (Oxford, UK) at the Beijing Novogene Bioinformatics Technology Co., Ltd. A complete description of the library construction, sequencing, and assembly was performed as previously described (Zheng et al., 2021b). We used seven databases to predict gene functions, including Pfam (Protein Families Database, http://pfam.xfam.org/), GO (Gene Ontology, http://geneontology.org/) (Ashburner et al., 2000), KEGG (Kyoto Encyclopedia of Genes and Genomes, http://www.genome.jp/kegg/) (Kanehisa et al., 2004), COG (Clusters of Orthologous Groups, http://www.ncbi.nlm.nih.gov/COG/) (Galperin et al., 2015), NR (Non-Redundant Protein Database databases), TCDB (Transporter Classification Database), and Swiss-Prot (http://www.ebi.ac.uk/uniprot/) (Bairoch and Apweiler, 2000). A whole genome Blast search (E-value less than 1e-5, minimal alignment length percentage larger than 40%) was performed against above seven databases.” in the revised manuscript (Lines 333-351).

Comment 28: Line 462. Accession list of other taxa in the supplement would help here.  

Thanks for your comments. The accession numbers of these strains were displayed behind these strains in Figure 1A. According to your suggestions, we have added an accession list of these taxa (Supplementary Table 6) in the revised manuscript.

Comment 29: Line 463. Is there any literature to support that these are phylogenetically informative genes for Inoviridae?  

Thanks for your comments. There are some literatures (Zeng et al, 2021; Evseev et al, 2023) to support that these are phylogenetically informative genes for Inoviridae. We have added these literatures in the revised manuscript. 

References related to this response:

Zeng, J., Wang, Y., Zhang, J., Yang, S., and Zhang, W. (2021) Multiple novel filamentous phages detected in the cloacal swab samples of birds using viral metagenomics approach Virol J 18:240

Evseev, P., Bocharova, J., Shagin, D., and Chebotar, I. (2023) Analysis of Pseudomonas aeruginosa isolates from patients with cystic fibrosis revealed novel groups of filamentous bacteriophages. Viruses 15: 2215

Reviewer #2 (Public Review):

Summary: This paper investigates virus-host interactions in deep-sea bacteriophage systems which employ a seemingly mutualistic approach to viral replication in which the virus aids host cell polysaccharide import and utilization via metabolic reprogramming. The hypothesis being tested is supported with solid and convincing evidence and the findings are potentially generalizable with implications for our understanding of polysaccharide-mediated virus-host interactions and carbon cycles in marine ecosystems more broadly.

Thanks for your positive comments.

Strengths: This paper synthesizes sequencing and phylogenic analyses of two Lentisphaerae bacteria and three phage genomes; electron microscopy imaging of bacterial/phage particles; differential gene expression analyses; differential growth curve analyses, and differential phage proliferation assays to extract insights into whether laminarin and starch can induce both host growth and phage proliferation. The data presented convincingly demonstrate that both host culture density and phage proliferation increase as a result having host, phage, and polysaccharide carbon source together in culture.

Thanks for your positive comments.  

Weaknesses (suggestions for improvement): 

(1) The article would be strengthened by the following additional experiment: providing the phage proteins hypothesized to be aiding host cell growth (red genes from Figure 5...TonB system energizer ExbB, glycosidases, etc) individually or in combination on plasmids rather than within the context of the actual phage itself to see if such additional genes are necessary and sufficient to realize the boosts in host cell growth/saturation levels observed in the presence of the phages tested.

Thanks for your valuable comments. It is a really good idea to express individually or in combination on plasmids to see the effects of those polysaccharide-degradation proteins in the host cell. However, at present, we failed to construct the genetic and expression system for the strictly anaerobic strain WC36, which hindering our further detailed investigation of the functions of those polysaccharide-degradation proteins. In our lab, we are trying our best to build the genetic and expression system for strain WC36. We will definitely test your idea in the future. 

(2) The paper would also benefit from additional experiments focused on determining how the polysaccharide processing, transport, and metabolism genes are being used by the phages to either directly increase viral infection/replication or else to indirectly do so by supporting the growth of the host in a more mutualistic manner (i.e. by improving their ability to import, degrade, and metabolize polysaccharides).  

Thanks for your valuable comments. Indeed, due to the chronic phage genome is not within the chromosome of the host, it is very hard to disclose the exact auxiliary process and mechanism of chronic phages. At present, we are trying to construct a genetic manipulation system for the strictly anaerobic host WC36, and we will gradually reveal this auxiliary mechanism in the future. In addition, combined with the reviewer 1’s suggestions, the focus of revised manuscript is to emphasize that polysaccharides induce deep-sea bacteria to release chronic phages, and most of the content of phage assisting host metabolism of polysaccharides has been deleted.

(3) The introduction would benefit from a discussion of what is known regarding phage and/or viral entry pathways that utilize carbohydrate anchors during host entry. The discussion could also be improved by linking the work presented to the concept of "selfishness" in bacterial systems (see for instance Giljan, G., Brown, S., Lloyd, C.C. et al. Selfish bacteria are active throughout the water column of the ocean. ISME COMMUN. 3, 11 (2023) https://doi.org/10.1038/s43705-023-00219-7). The bacteria under study are gram negative and it was recently demonstrated (https://www.nature.com/articles/ismej201726) that "selfish" bacteria sequester metabolizable polysaccharides in their periplasm to advantage. It is plausible that the phages may be hijacking this "selfishness" mechanism to improve infectivity and ENTRY rather than helping their hosts to grow and profilerate so they can reap the benefits of simply having more hosts to infect. The current work does not clearly distinguish between these two distinct mechanistic possibilities. The paper would be strengthened by at least a more detailed discussion of this possibility as well as the author's rationale for interpreting their data as they do to favor the "mutualistic" interpretation. In the same light, the paper would benefit from a more careful choice of words which can also help to make such a distinction more clear/evident/intentional. As currently written the authors seem to be actively avoiding giving insights wrt this question.  

Thanks for your valuable comments. According to your suggestions, we have added the related discussion as “Moreover, it was recently demonstrated that selfish bacteria, which were common throughout the water column of the ocean, could bind, partially hydrolyze, and transport polysaccharides into the periplasmic space without loss of hydrolysis products (Reintjes et al., 2017; Giljan et al., 2023). Based on our results, we hypothesized that these chronic phages might also enter the host through this “selfishness” mechanism while assisting the host in metabolizing polysaccharides, thus not lysing the host. On the other hand, these chronic phages might hijack this “selfishness” mechanism to improve their infectivity and entry, rather than helping their hosts to grow and proliferate, so they could reap the benefits of simply having more hosts to infect. In the future, we need to construct a genetic operating system of the strictly anaerobic host strain WC36 to detailedly reveal the relationship between chronic phage and host.” in the revised manuscript (Lines 305-316). 

References related to this response:

Reintjes, G., Arnosti, C., Fuchs, B.M., and Amann, R. (2017) An alternative polysaccharide uptake mechanism of marine bacteria ISME J 11:1640-1650

Giljan, G., Brown, S., Lloyd, C.C., Ghobrial, S., Amann, R., and Arnosti, C. (2023) Selfish bacteria are active throughout the water column of the ocean ISME Commun 3:11

(4) Finally, I would be interested to know if the author’s sequencing datasets might be used to inform the question raised above by using bacterial immunity systems such as CRISPR/Cas9. For example, if the phage systems studied are truly beneficial/mutualistic for the bacteria then it’s less likely that there would be evidence of targeted immunity against that particular phage that has the beneficial genes that support polysaccharide metabolism.

Thanks for your comments. According to your suggestions, we have carefully analyzed the genome of strain WC36, and found that there were no CRISPR/Cas9-related genes. Considering our results that the number of chronic phages was increased with the prolongation of culture time, we speculated that host might have no targeted immunity against these chronic phages.

Reviewer #2 (Recommendations For The Authors):

There are some minor grammatical errors and unclear statements (lines 99-100, 107-109, 163, 222, 223, 249-250, 254) which should also be fixed before final publication. 

Thanks for your valuable comments. We have fixed these minor grammatical errors and unclear statements in the revised manuscript.

Lines 99-100: we have modified this description as “For instance, AMGs of marine bacteriophages have been predicted to be involved in photosynthesis (Mann et al., 2003), nitrogen cycling (Ahlgren et al., 2019; Gazitúa et al., 2021), sulfur cycling (Anantharaman et al., 2014; Roux et al., 2016), phosphorus cycling (Zeng and Chisholm, 2012), nucleotide metabolism (Sullivan et al., 2005; Dwivedi et al., 2013; Enav et al., 2014), and almost all central carbon metabolisms in host cells (Hurwitz et al., 2013).” in the revised manuscript (Lines 100-105).

Lines 107-109: we have modified this description as “However, due to the vast majority of deep-sea microbes cannot be cultivated in the laboratory, most bacteriophages could not be isolated.” in the revised manuscript (Lines 110-111).

Line 163: we have modified this description as “Based on the growth curve of strain WC36, we found that the growth rate of strictly anaerobic strain WC36 was relatively slow.” in the revised manuscript (Lines 149-151).

Lines 222-223: we have modified this description as “Regardless of whether the laminarin was present, the bacterial cells kept their cell shape intact, indicating they were still healthy after 30 days” in the revised manuscript (Lines 195-197).

Lines 249-250: we have modified this description as “However, the entry and exit of the hexagonal phages into the WC36 cells were not observed.” in the revised manuscript (Lines 190-191).

Line 254: we have modified this description as “To explore whether the production of bacteriophages induced by polysaccharide is an individual case, we further checked the effect of polysaccharides on another cultured deep-sea Lentisphaerae strain zth2.” in the revised manuscript (Lines 213-215).

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

We thank the reviewers for the detailed assessment of our work as well as their praise and constructive feedback which helped us to significantly improve our manuscript.

Reviewer #1 (Public Review):

The inferior colliculus (IC) is the central auditory system's major hub. It integrates ascending brainstem signals to provide acoustic information to the auditory thalamus. The superficial layers of the IC ("shell" IC regions as defined in the current manuscript) also receive a massive descending projection from the auditory cortex. This auditory cortico-collicular pathway has long fascinated the hearing field, as it may provide a route to funnel "high-level" cortical signals and impart behavioral salience upon an otherwise behaviorally agnostic midbrain circuit.

Accordingly, IC neurons can respond differently to the same sound depending on whether animals engage in a behavioral task (Ryan and Miller 1977; Ryan et al., 1984; Slee & David, 2015; Saderi et al., 2021; De Franceschi & Barkat, 2021). Many studies also report a rich variety of non-auditory responses in the IC, far beyond the simple acoustic responses one expects to find in a "low-level" region (Sakurai, 1990; Metzger et al., 2006; Porter et al., 2007). A tacit assumption is that the behaviorally relevant activity of IC neurons is inherited from the auditory cortico-collicular pathway. However, this assumption has never been tested, owing to two main limitations of past studies:

(1) Prior studies could not confirm if data were obtained from IC neurons that receive monosynaptic input from the auditory cortex.

(2) Many studies have tested how auditory cortical inactivation impacts IC neuron activity; the consequence of cortical silencing is sometimes quite modest. However, all prior inactivation studies were conducted in anesthetized or passively listening animals. These conditions may not fully engage the auditory cortico-collicular pathway. Moreover, the extent of cortical inactivation in prior studies was sometimes ambiguous, which complicates interpreting modest or negative results.

Here, the authors' goal is to directly test if auditory cortex is necessary for behaviorally relevant activity in IC neurons. They conclude that surprisingly, task relevant activity in cortico-recipient IC neuron persists in absence of auditory cortico-collicular transmission. To this end, a major strength of the paper is that the authors combine a sound-detection behavior with clever approaches that unambiguously overcome the limitations of past studies.

First, the authors inject a transsynaptic virus into the auditory cortex, thereby expressing a genetically encoded calcium indicator in the auditory cortex's postsynaptic targets in the IC. This powerful approach enables 2-photon Ca2+ imaging from IC neurons that unambiguously receive monosynaptic input from auditory cortex. Thus, any effect of cortical silencing should be maximally observable in this neuronal population. Second, they abrogate auditory cortico-collicular transmission using lesions of auditory cortex. This "sledgehammer" approach is arguably the most direct test of whether cortico-recipient IC neurons will continue to encode task-relevant information in absence of descending feedback. Indeed, their method circumvents the known limitations of more modern optogenetic or chemogenetic silencing, e.g. variable efficacy.

I also see three weaknesses which limit what we can learn from the authors' hard work, at least in the current form. I want to emphasize that these issues do not reflect any fatal flaw of the approach. Rather, I believe that their datasets likely contain the treasure-trove of knowledge required to completely support their claims.

(1) The conclusion of this paper requires the following assumption to be true: That the difference in neural activity between Hit and Miss trials reflects "information beyond the physical attributes of sound." The data presentation complicates asserting this assumption. Specifically, they average fluorescence transients of all Hit and all Miss trials in their detection task. Yet, Figure 3B shows that mice's d' depends on sound level, and since this is a detection task the smaller d' at low SPLs presumably reflects lower Hit rates (and thus higher Miss rates). As currently written, it is not clear if fluorescence traces for Hits arise from trials where the sound cue was played at a higher sound level than on Miss trials. Thus, the difference in neural activity on Hit and Miss trials could indeed reflect mice's behavior (licking or not licking). But in principle could also be explained by higher sound-evoked spike rates on Hit compared to Miss trials, simply due to louder click sounds. Indeed, the amplitude and decay tau of their indicator GCaMP6f is non-linearly dependent on the number and rate of spikes (Chen et al., 2013), so this isn't an unreasonable concern.

(2) The authors' central claim effectively rests upon two analyses in Figures 5 and 6. The spectral clustering algorithm of Figure 5 identifies 10 separate activity patterns in IC neurons of control and lesioned mice; most of these clusters show distinct activity on averaged Hit and Miss trials. They conclude that although the proportions of neurons from control and lesioned mice in certain clusters deviates from an expected 50/50 split, neurons from lesioned mice are still represented in all clusters. A significant issue here is that in addition to averaging all Hits and Miss trials together, the data from control and lesioned mice are lumped for the clustering. There is no direct comparison of neural activity between the two groups, so the reader must rely on interpreting a row of pie charts to assess the conclusion. It's unclear how similar task relevant activity is between control and lesioned mice; we don't even have a ballpark estimate of how auditory cortex does or does not contribute to task relevant activity. Although ideally the authors would have approached this by repeatedly imaging the same IC neurons before and after lesioning auditory cortex, this within-subjects design may be unfeasible if lesions interfere with task retention. Nevertheless, they have recordings from hundreds to thousands of neurons across two groups, so even a small effect should be observable in a between-groups comparison.

(3) In Figure 6, the authors show that logistic regression models predict whether the trial is a Hit or Miss from their fluorescence data. Classification accuracy peaks rapidly following sound presentation, implying substantial information regarding mice's actions. The authors further show that classification accuracy is reduced, but still above chance in mice with auditory cortical lesions. The authors conclude from this analysis task relevant activity persists in absence of auditory cortex. In principle I do not disagree with their conclusion.

The weakness here is in the details. First, the reduction in classification accuracy of lesioned mice suggests that auditory cortex does nevertheless transmit some task relevant information, however minor it may be. I feel that as written, their narrative does not adequately highlight this finding. Rather one could argue that their results suggest redundant sources of task-relevant activity converging in the IC. Secondly, the authors conclude that decoding accuracy is impaired more in partially compared to fully lesioned mice. They admit that this conclusion is at face value counterintuitive, and provide compelling mechanistic arguments in the Discussion. However, aside from shaded 95% CIs, we have no estimate of variance in decoding accuracy across sessions or subjects for either control or lesioned mice. Thus we don't know if the small sample sizes of partial (n = 3) and full lesion (n = 4) groups adequately sample from the underlying population. Their result of Figure 6B may reflect spurious sampling from tail ends of the distributions, rather than a true non-monotonic effect of lesion size on task relevant activity in IC.

Our responses to the ‘recommendations for the authors’ below lay out in detail how we addressed each comment and concern. Besides filling in key information about how our original analysis aimed at minimizing any potential impact of differences in sound level distributions - namely that trials used for decoding were limited to a subset of sound levels - and which was accidentally omitted in the original manuscript, we have now carried out several additional analyses.

We would like to highlight one of these because it supplements both the clustering and decoding analysis that we conducted to compare hit and miss trial activity, and directly addresses what the reviewer identified as our work’s main weakness (a possible confound between animal behavior and sound level distributions) and the request for an analysis that operates at the level of single units rather than the population level. Specifically, we assessed, separately for each recorded neuron, whether there was a statistically significant difference in the magnitude of neural activity between hit and miss trials. This approach allowed us to fully balance the numbers of hit and miss trials at each sound level that were entered into the analysis. The results revealed that a large proportion (close to 50%) of units were task modulated, i.e. had significantly different response magnitudes between hit and miss trials, and that this proportion was not significantly different between lesioned and non-lesioned mice. We hope that this, together with the rest of our responses, convincingly demonstrates that the shell of the IC encodes mouse sound detection behavior even when top-down input from the auditory cortex is absent.

Reviewer #2 (Public Review):

Summary:

This study takes a new approach to studying the role of corticofugal projections from auditory cortex to inferior colliculus. The authors performed two-photon imaging of cortico-recipient IC neurons during a click detection task in mice with and without lesions of auditory cortex. In both groups of animals, they observed similar task performance and relatively small differences in the encoding of task-response variables in the IC population. They conclude that non-cortical inputs to the IC provide can substantial task-related modulation, at least when AC is absent. Strengths:

This study provides valuable new insight into big and challenging questions around top-down modulation of activity in the IC. The approach here is novel and appears to have been executed thoughtfully. Thus, it should be of interest to the community.

Weaknesses: There are, however, substantial concerns about the interpretation of the findings and limitations to the current analysis. In particular, Analysis of single unit activity is absent, making interpretation of population clusters and decoding less interpretable. These concerns should be addressed to make sure that the results can be interpreted clearly in an active field that already contains a number of confusing and possibly contradictory findings.

Our responses to the ‘recommendations for the authors’ below lay out in detail how we addressed each comment and concern. Several additional analyses have now been carried out including ones that operate at the level of single units rather than the population level, as requested by the reviewer. We would like to briefly highlight one here because it supplements both the clustering and decoding analysis that we conducted to compare hit and miss trial activity and directly addresses what the other reviewers identified as our work’s main weakness (a possible confound between animal behavior and sound level distributions). Specifically, we assessed, separately for each recorded neuron, whether there was a statistically significant difference in the magnitude of neural activity between hit and miss trials. This approach allowed us to fully balance the numbers of hit and miss trials at each sound level that were entered into the analysis. The results revealed that a large proportion (close to 50%) of units were task modulated, i.e. had significantly different response magnitudes between hit and miss trials, and that this proportion was not significantly different between lesioned and non-lesioned mice. We hope that this, together with the rest of our responses, convincingly demonstrates that the shell of the IC encodes mouse sound detection behavior even when top-down input from the auditory cortex is absent.

Reviewer #3 (Public Review):

Summary:

This study aims to demonstrate that cortical feedback is not necessary to signal behavioral outcome to shell neurons of the inferior colliculus during a sound detection task. The demonstration is achieved by the observation of the activity of cortico-recipient neurons in animals which have received lesions of the auditory cortex. The experiment shows that neither behavior performance nor neuronal responses are significantly impacted by cortical lesions except for the case of partial lesions which seem to have a disruptive effect on behavioral outcome signaling. Strengths:

The experimental procedure is based on state of the art methods. There is an in depth discussion of the different effects of auditory cortical lesions on sound detection behavior. Weaknesses:

The analysis is not documented enough to be correctly evaluated. Have the authors pooled together trials with different sound levels for the key hit vs miss decoding/clustering analysis? If so, the conclusions are not well supported, as there are more misses for low sound levels, which would completely bias the outcome of the analysis. It would possible that the classification of hit versus misses actually only reflects a decoding of sound level based on sensory responses in the colliculus, and it would not be surprising then that in the presence or absence of cortical feedback, some neurons responds more to higher sound levels (hits) and less to lower sound levels (misses). It is important that the authors clarify and in any case perform an analysis in which the classification of hits vs misses is done only for the same sound levels. The description of feedback signals could be more detailed although it is difficult to achieve good temporal resolution with the calcium imaging technique necessary for targeting cortico-recipient neurons.

Our responses to the ‘recommendations for the authors’ below lay out in detail how we addressed each comment and concern. Besides filling in key information about how our original analysis aimed at minimizing any potential impact of differences in sound level distributions - namely that trials used for decoding were limited to a subset of sound levels - and which was accidentally omitted in the original manuscript, we have now carried out several additional analyses to directly address what the reviewer identified as our work’s main weakness (a possible confound between animal behavior and sound level distributions). This includes an analysis in which we were able to demonstrate for one imaging session with a sufficiently large number of trials that limiting the trials entered into the decoding analysis to those from a single sound level did not meaningfully impact decoding accuracy. We would like to highlight another new analysis here because it supplements both the clustering and decoding analyses that we conducted to compare hit and miss trial activity and addresses the other reviewers’ request for an analysis that operates at the level of single units rather than the population level. Specifically, we assessed, separately for each recorded neuron, whether there was a statistically significant difference in the magnitude of neural activity between hit and miss trials. This approach allowed us to fully balance the numbers of hit and miss trials at each sound level that were entered into the analysis. The results revealed that a large proportion (close to 50%) of units were task modulated, i.e. had significantly different response magnitudes between hit and miss trials, and that this proportion was not significantly different between lesioned and non-lesioned mice. We hope that this, together with the rest of our responses, convincingly demonstrates that the shell of the IC encodes mouse sound detection behavior even when top-down input from the auditory cortex is absent.

Reviewer #1 (Recommendations For The Authors):

Thank you for the opportunity to read your paper. I think the conclusion is exciting. Indeed, you indicate that perhaps contrary to many of our (untested) assumptions, task-relevant activity in the IC may persist in absence of auditory cortex.

As mentioned in my public review: Despite my interest in the work, I also think that there are several opportunities to significantly strengthen your conclusions. I feel this point is important because your work will likely guide the efforts of future students and post-docs working on this topic. The data can serve as a beacon to move the field away from the (somewhat naïve) idea that the evolved forebrain imparts behavioral relevance upon an otherwise uncivilized midbrain. This knowledge will inspire a search for alternative explanations. Indeed, although you don't highlight it in your narrative, your results dovetail nicely with several studies showing task-relevant activity in more ventral midbrain areas that project to the IC (e.g., pedunculopontine nuclei; see work from Hikosaka in monkeys, and more recently in mice from Karel Svoboda's lab).

Thanks for the kind words.

These studies, in particular the work by Inagaki et al. (2022) outlining how the transformation of an auditory go signal into movement could be mediated via a circuit involving the PPN/MRN (which might rely on the NLL for auditory input) and the motor thalamus, are indeed highly relevant.

We made the following changes to the manuscript text.

Line 472:”...or that the auditory midbrain, thalamus and cortex are bypassed entirely if simple acousticomotor transformations, such as licking a spout in response to a sound, are handled by circuits linking the auditory brainstem and motor thalamus via pedunculopontine and midbrain reticular nuclei (Inagaki et al., 2022).”

The beauty of the eLife experiment is that you are free to incorporate or ignore these suggestions. After all, it's your paper, not mine. Nevertheless, I hope you find my comments useful.<br /> First, a few suggestions to address my three comments in the public review.

Suggestion for public comment #1: An easy way to address this issue is to average the neural activity separately for each trial outcome at each sound level. That way you can measure if fluorescence amplitude (or integral) varies as a function of mice's action rather than sound level. This approach to data organization would also open the door to the additional analyses for addressing comment #2, such as directly comparing auditory and putatively non-auditory activity in neurons recorded from control and lesioned mice.

We have carried out additional analyses for distinguishing between the two alternative explanations of the data put forward by the reviewer: That the difference in neural activity between hit and miss trials reflects a) behavior or b) sound level (more precisely: differences in response magnitude arising from a higher proportion of high-sound-level trials in the hit trial group than in the miss trial group). If the data favored b), we would expect no difference in activity between hit and miss trials when plotted separately for each sound level. The new Figure 4 - figure supplement 1 indicates that this is not the case. Hit and miss trial activity are clearly distinct even when plotted separately for different sound levels, confirming that this difference in activity reflects the animals’ behavior rather than sensory information.

Changes to manuscript.

Line 214: “While averaging across all neurons cannot capture the diversity of responses, the averaged response profiles suggest that it is mostly trial outcome rather than the acoustic stimulus and neuronal sensitivity to sound level that shapes those responses (Figure 4 – figure supplement 1).”

Additionally, we assessed for each neuron separately whether there was a significant difference between hit and miss trial activity and therefore whether the activity of the neuron could be considered “task-modulated”. To achieve this, we used equal numbers of hit and miss trials at each sound level to ensure balanced sound level distributions and thus rule out any potential confound between sound level distributions and trial outcome. This analysis revealed that the proportion of task-modulated neurons was very high (close to 50%) and not significantly different between lesioned and non-lesioned mice (Figure 6 - figure supplement 3).

Changes to the manuscript.

Line 217: “Indeed, close to half (1272 / 2649) of all neurons showed a statistically significant difference in response magnitude between hit and miss trials…”

Line 307: “Although the proportion of individual neurons with distinct response magnitudes in hit and miss trials in lesioned mice did not differ from that in non-lesioned mice, it was significantly lower when separating out mice with partial lesions (Figure 6 – figure supplement 3).”

Differences in the distributions of sound levels in the different trial types could also potentially confound the decoding into hit and miss trials. Our original analysis was actually designed to take this into account but, unfortunately, we failed to include sufficient details in the methods section.

Changes to the manuscript.

Line 710: “Rather than including all the trials in a given session, only trials of intermediate difficulty were used for the decoding analysis. More specifically, we only included trials across five sound levels, comprising the lowest sound level that exceeded a d’ of 1.5 plus the two sound levels below and above that level. That ensured that differences in sound level distributions would be small, while still giving us a sufficient number of trials to perform the decoding analysis.“

In this context, it is worth bearing in mind that a) the decoding analysis was done on a frame-byframe basis, meaning that the decoding score achieved early in the trial has no impact on the decoding score at later time points in the trial, b) sound-driven activity predominantly occurs immediately after stimulus onset and is largely over about 1 s into the trial (see cluster 3, for instance, or average miss trial activity in Figure 4 – figure supplement 1), c) decoding performance of the behavioral outcome starts to plateau 500-1000 ms into the trial and remains high until it very gradually begins to decline after about 2 s into the trial. In other words, decoding performance remains high far longer than the stimulus would be expected to have an impact on the neurons’ activity. Therefore, we would expect any residual bias due to differences in the sound level distribution that our approach did not control for to be restricted to the very beginning of the trial and not to meaningfully impact the conclusions derived from the decoding analysis.

Finally, we carried out an additional decoding analysis for one imaging session in which we had a sufficient number of trials to perform the analysis not only over the five (59, 62, 65, 68, 71 dB SPL) original sound levels, but also over a reduced range of three (62, 65, 68 dB SPL) sound levels, as well as a single (65 dB SPL) sound level (Figure 6 - figure supplement 1). The mean sound level differences between the hit trial distributions and miss trial distributions for these three conditions were 3.08, 1.01 and 0 dB, respectively. This analysis suggests that decoding performance is not meaningfully impacted by changing the range of sound levels (and sound level distributions), other than that including fewer sound levels means fewer trials and thus noisier decoding.

Changes to manuscript.

Line 287: ”...and was not meaningfully affected by differences in sound level distributions between hit and miss trials (Figure 6 – figure supplement 1).”

Suggestion for public comment #2: Perhaps a solution would be to display example neuron activity in each cluster, recorded in control and lesioned mice. The reader could then visually compare example data from the two groups, and immediately grasp the conclusion that task relevant activity remains in absence of auditory cortex. Additionally, one possibility might be to calculate the difference in neural activity between Hit and Miss trials for each task-modulated neuron. Then, you could compare these values for neurons recorded in control and lesion mice. I feel like this information would greatly add to our understanding of cortico-collicular processing.

I would also argue that it's perhaps more informative to show one (or a few) example recordings rather than averaging across all cells in a cluster. Example cells would give the reader a better handle on the quality of the imaging, and this approach is more standard in the field. Finally, it would be useful to show the y axis calibration for each example trace (e.g. Figure 5 supp 1). That is also pretty standard so we can immediately grasp the magnitude of the recorded signal.

We agree that while the information we provided shows that neurons from lesioned and nonlesioned groups are roughly equally represented across the clusters, it does not allow the reader to appreciate how similar the activity profiles of neurons are from each of the two groups. However, picking examples can be highly subjective and thus potentially open to bias. We therefore opted instead to display, separately for lesioned and non-lesioned mice, the peristimulus time histograms of all neurons in each cluster, as well as the cluster averages of the response profiles (Figure 5 - figure supplement 3). This, we believe, convincingly illustrates the close correspondence between neural activity in lesioned and non-lesioned mice across different clusters. All our existing and new figures indicate the response magnitude either on the figures’ y-axis or via scale/color bars.

Changes to manuscript.

Line 254: “Furthermore, there was a close correspondence between the cluster averages of lesioned and non-lesioned mice (Figure 5 – figure supplement 3).”

Furthermore, we’ve now included a video of the imaging data which, we believe, gives the reader a much better handle on the data quality than further example response profiles would.

Changes to manuscript.

Line 197: ”...using two-photon microscopy (Figure 4B, Video 1).”

Suggestion for public comment #3: In absence of laborious and costly follow-up experiments to boost the sample size of partial and complete lesion groups, it may be more prudent to simply tone down the claims that lesion size differentially impacts decoding accuracy. The results of this analysis are not necessary for your main claims.

Our new results on the proportions of ‘task-modulated’ neurons (Figure 6 - figure supplement 3) across different experimental groups show that there is no difference between non-lesioned and lesioned mice as a whole, but mice with partial lesions have a smaller proportion of taskmodulated neurons than the other two groups. While this corroborates the results of the decoding analysis, we certainly agree that the small sample size is a caveat that needs to be acknowledged.

Changes to manuscript.

Line 477: ”Some differences were observed for mice with only partial lesions of the auditory cortex.

Those mice had a lower proportion of neurons with distinct response magnitudes in hit and miss trials than mice with (near-)complete lesions. Furthermore, trial outcomes could be read out with lower accuracy from these mice. While this finding is somewhat counterintuitive and is based on only three mice with partial lesions, it has been observed before that smaller lesions…”

A few more suggestions unrelated to public review:

Figure 1: This is somewhat of an oddball in this manuscript, and its inclusion is not necessary for the main point. Indeed, the major conclusion of Fig 1 is that acute silencing of auditory cortex impairs task performance, and thus optogenetic methods are not suitable to test your hypothesis. However, this conclusion is also easily supported from decades of prior work, and thus citations might suffice.

We do not agree that these data can easily be substituted with citations of prior published work. While previous studies (Talwar et al., 2001, Li et al., 2017) have demonstrated the impact of acute pharmacological silencing on sound detection in rodents, pharmacological and optogenetic silencing are not equivalent. Furthermore, we are aware of only one published study (Kato et al., 2015) that investigated the impact of optogenetically perturbing auditory cortex on sound detection (others have investigated its impact on discrimination tasks). Kato et al. (2015) examined the effect of acute optogenetic silencing of auditory cortex on the ability of mice to detect the offsets of very long (5-9 seconds) sounds, which is not easily comparable to the click detection task employed by us. Furthermore, when presenting our work at a recent meeting and leaving out the optogenetics results due to time constraints, audience members immediately enquired whether we had tried an optogenetic manipulation instead of lesions. Therefore, we believe that these data represent a valuable piece of information that will be appreciated by many readers and have decided not to remove them from the manuscript.

A worst case scenario is that Figure 1 will detract from the reader's assessment of experimental rigor. The data of 1C are pooled from multiple sessions in three mice. It is not clear if the signed-rank test compares performance across n = 3 mice or n = 13 sessions. If the latter, a stats nitpicker could argue that the significance might not hold up with a nested analysis considering that some datapoints are not independent of one another. Finally, the experiment does not include a control group, gad2-cre mice injected with a EYFP virus. So as presented, the data are equally compatible with the pessimistic conclusion that shining light into the brain impairs mice's licking. My suggestion is to simply remove Figure 1 from the paper. Starting off with Figure 3 would be stronger, as the rest of the study hinges upon the knowledge that control and lesion mice's behavior is similar.

Instead of reporting the results session-wise and doing stats on the d’ values, we now report results per mouse and perform stats on the proportions of hits and false alarms separately for each mouse. The results are statistically significant for each mouse and suggest that the differences in d’ are primarily caused by higher false alarm rates during the optogenetic perturbation than in the control condition.

Changes to manuscript.

New Figure 1.

We agree that including control mice not expressing ChR2 would be important for fully characterizing the optogenetic manipulation and that the lack of this control group should be acknowledged. However, in the context of this study, the outcome of performing this additional experiment would be inconsequential. We originally considered using an optogenetic approach to explore the contribution of cortical activity to IC responses, but found that this altered the animals’ sound detection behavior. Whether that change in behavior is due to activation of the opsin or simply due to light being shone on the brain has no bearing on the conclusion that this type of manipulation is unsuitable for determining whether auditory cortex is required for the choice-related activity that we recorded in the IC.

Changes to manuscript.

Line 106: ”Although a control group in which the auditory cortex was injected with an EYFP virus lacking ChR2 would be required to confirm that the altered behavior results from an opsindependent perturbation of cortical activity, this result shows that this manipulation is also unsuitable… ”

Figure 2, comment #1: The micrograph of panel B shows the densest fluorescence in the central IC. You interpret this as evidence of retrograde labeling of central IC neurons that project to the shell IC. This is a nice finding, but perhaps a more relevant micrograph would be to show the actual injection site in the shell layers. The rest of Figure 2 documents the non-auditory cortical sources of forebrain feedback. Since non-auditory cortical neurons may or may not target distinct shell IC sub-circuits, it's important to know where the retrograde virus was injected. Stylistic comment: The flow of the panels is somewhat unorthodox. Panel A and B follow horizontally, then C and D follow vertically, followed by E-H in a separate column. Consider sequencing either horizontally or vertically to maximize the reader's experience.

Figure 2, comment # 2: It would also be useful to show more rostral sections from these mice, perhaps as a figure supplement, if you have the data. I think there is a lot of value here given a recent paper (Olthof et al., 2019 Jneuro) arguing that the IC receives corticofugal input from areas more rostral to the auditory cortex. So it would be beneficial for the field to know if these other cortical sources do or do not represent likely candidates for behavioral modulation in absence of auditory cortex.

Figure 2, comment #3: You have a striking cluster of retrogradely labeled PPC neurons, and I'm not sure PPC has been consistently reported as targeting the IC. It would be good to confirm that this is a "true" IC projection as opposed to viral leakage into the SC. Indeed, Figure 2, supplement 2 also shows some visual cortex neurons that are retrogradely labeled. This has bearing on the interpretations, because choice-related activity is rampant in PPC, and thus could be a potential source of the task relevant activity that persists in your recordings. This could be addressed as the point above, by showing the SC sections from these same mice.

All IC injections were made under visual guidance with the surface of the IC and adjacent brain areas fully exposed after removal of the imaging window. Targeting the IC and steering clear of surrounding structures, including the SC, was therefore relatively straightforward.

We typically observed strong retrograde labeling in the central nucleus after viral injections into the dorsal IC and, given the moderate injection volume (~50 nL at each of up to three sites), it was also typical to see spatially fairly confined labeling at the injection sites. For the mouse shown in Figure 2, we do not have further images of the IC. This was one of the earliest mice to be included in the study and we did not have access to an automatic slide scanner at the time. We had to acquire confocal images in a ‘manual’ and very time-consuming manner and therefore did not take further IC images for this mouse. We have now included, however, a set of images spanning the whole IC and the adjacent SC sections for the mouse for which we already show sections in Figure 2 - figure supplement 2. These were added as Figure 2 - figure supplement 3A to the manuscript. These images show that the injections were located in the caudal half of the IC and that there was no spillover into the SC - close inspection of those sections did not reveal any labeled cell bodies in the SC. Furthermore, we include as Figure 2 - figure supplement 3B a dozen additional rostral cortical sections of the same mouse illustrating corticocollicular neurons in regions spanning visual, parietal, somatosensory and motor cortex. Given the inclusion of the IC micrographs in the new supplementary figure, we removed panel B from Figure 2. This should also make it easier for the reader to follow the sequencing of the remaining panels.

Changes to manuscript.

New Figure 2 - figure supplement 3.

Line 159: “After the experiments, we injected a retrogradely-transported viral tracer (rAAV2-retrotdTomato) into the right IC to determine whether any corticocollicular neurons remained after the auditory cortex lesions (Figure 2, Figure 2 – figure supplement 2, Figure 2 – figure supplement 3). The presence of retrogradely-labeled corticocollicular neurons in non-temporal cortical areas (Figure 2) was not the result of viral leakage from the dorsal IC injection sites into the superior colliculus (Figure 2 – figure supplement 3).”

Line 495: “...projections to the IC, such as those originating from somatosensory cortical areas (Lohse et al., 2021; Lesicko et al., 2016) and parietal cortex may have contributed to the response profiles that we observed.

Figure 5 (see also public review point #2): I am not convinced that this unsupervised method yields particularly meaningful clusters; a grain of salt should be provided to the reader. For example, Clusters 2, 5, 6, and 7 contain neurons that pretty clearly respond with either short latency excitation or inhibition following the click sound on Hits. I would argue that neurons with such diametrically opposite responses should not be "classified" together. You can see the same issue in some of Namboodiri/Stuber's clustering (their Figure 1). It might be useful to make it clear to the reader that these clusters can reflect idiosyncrasies of the algorithm, the behavior task structure, or both.

We agree.

Changes to manuscript.

Line 666: “While clustering is a useful approach for organizing and visualizing the activity of large and heterogeneous populations of neurons, we need to be mindful that, given continuous distributions of response properties, the locations of cluster boundaries can be somewhat arbitrary and/or reflect idiosyncrasies of the chosen method and thus vary from one algorithm to another. We employed an approach very similar to that described in Namboodiri et al. (2019) because it is thought to produce stable results in high-dimensional neural data (Hirokawa et al. 2019).”

Methods:

How was a "false alarm" defined? Is it any lick happening during the entire catch trial, or only during the time period corresponding to the response window on stimulus trials?

The response window was identical for catch and stimulus trials and a false alarm was defined as licking during the response window of a catch trial.

Changes to manuscript.

Line 598: “During catch trials, neither licking (‘false alarm’) during the 1.5-second response window …”

L597 and so forth: What's the denominator in the conversion from the raw fluorescence traces into DF/F? Did you take the median or mode fluorescence across a chunk of time? Baseline subtract average fluorescence prior to click onset? Similarly, please provide some more clarification as to how neuropil subtraction was achieved. This information will help us understand how the classifier can decode trial outcome from data prior to sound onset.

Signal processing did not involve the subtraction of a pre-stimulus period.

Changes to manuscript.

Line 629: ”Neuropil extraction was performed using default suite2p parameters (https://suite2p.readthedocs.io/en/latest/settings.html), neuropil correction was done using a coefficient of 0.7, and calcium ΔF/F signals were obtained by using the median over the entire fluorescence trace as F0. To remove slow fluctuations in the signal, a baseline of each neuron’s entire trace was calculated by Gaussian filtering in addition to minimum and maximum filtering using default suite2p parameters. This baseline was then subtracted from the signal.”

Was the experimenter blinded to the treatment group during the behavior experiments? If not, were there issues that precluded blinding (limited staffing owing to lab capacity restrictions during the pandemic)? This is important to clarify for the sake of rigor and reproducibility.

Changes to manuscript.

Line 574: “The experimenters were not blinded to the treatment group, i.e. lesioned or non-lesioned, but they were blind to the lesion size both during the behavior experiments and most of the data processing.”

Minor:

L127-128: "In order to test...lesioned the auditory cortex bilaterally in 7 out of 16 animals". I would clarify this by changing the word animals to "mice" and 7 out of 16 by stating n = 9 and n = 7 are control and lesion groups, respectively.

Agreed.

Changes to manuscript.

Line 129: “...compared the performance of mice with bilateral lesions of the auditory cortex (n = 7) with non-lesioned controls (n = 9)”

L225-226: You rule out self-generated sounds as a likely source of behavioral modulation by citing Nate Sawtell's paper in the DCN. However, Stephen David's lab suggested that in marmosets, post sound activity in central IC may in fact reflect self-generated sounds during licking. I suggest addressing this with a nod to SVD's work (Singla et al., 2017; but see Shaheen et al., 2021).

Agreed.

Changes to manuscript.

Line 243: “(Singla et al., 2017; but see Shaheen et al., 2021)”

Line 238 - 239: You state that proportions only deviate greater than 10% for one of the four statistically significant clusters. Something must be unclear here because I don't understand: The delta between the groups in the significant clusters of Fig 5C is (from left to right) 20%, 20%, 38%, and 12%. Please clarify.

Our wording was meant to convey that a deviation “from a 50/50 split” of 10% means that each side deviates from 50 by 10% resulting in a 40/60 (or 60/40) split. We agree that that has the potential to confuse readers and is not as clear as it could be and have therefore dropped the ambiguous wording.

Changes to manuscript.

Line 253: ”,..the difference between the groups was greater than 20% for only one of them.”

L445: I looked at the cited Allen experiment; I'd be cautious with the interpretation here. A monosynaptic IC->striatum projection is news to me. I think Allen Institute used an AAV1-EGFP virus for these experiments, no? As you know, AAV1 is quite transsynaptic. The labeled fibers in striatum of that experiment may reflect disynaptic labeling of MGB neurons (which do project to striatum).

Agreed. We deleted the reference to this Allen experiment.

L650: Please define "network activity". Is this the fluorescence value for each ROI on each frame of each trial? Averaged fluorescence of each ROI per frame? Total frame fluorescence including neuropil? Depending on who you ask, each of these measures provides some meaningful readout of network activity, so clarification would be useful.

Changes to manuscript.

Line 707: “Logistic regression models were trained on the network activity of each session, i.e., the ΔF/F values of all ROIs in each session, to classify hit vs miss trials. This was done on a frame-by-frame basis, meaning that each time point (frame) of each session was trained separately.

Figure 3 narrative or legend: Listing the F values for the anova would be useful. There is pretty clearly a main effect of training session for hits, but what about for the false alarms? That information is important to solidify the result, and would help more specialized readers interpret the d-prime plot in this figure.

Agreed. There were significant main effects of training day for both hit rates and false alarm rates (as well as d’).

Changes to manuscript.

Line 165: “The ability of the mice to learn and perform the click detection task was evident in increasing hit rates and decreasing false alarm rates across training days (Figure 3A, p < 0.01, mixed-design ANOVAs).”

In summary, thank you for undertaking this work. Your conclusions are provocative, and thus will likely influence the field's direction for years to come.

Thank you for those kind words and valuable and constructive feedback, which has certainly improved the manuscript.

Reviewer #2 (Recommendations For The Authors):

MAJOR CONCERNS

(1) (Fig. 5) What fraction of individual neurons actually encode task-related information in each animal group? How many neurons respond to sound? The clustering and decoding analyses are interesting, but they obscure these simple questions, which get more directly at the main questions of the study. Suggested approach: For a direct comparison of AC-lesioned and -non-lesioned animals, why not simply compare the mean difference between PSTH response for each neuron individually? To test for trial outcome effects, compare Hit and Miss trials (same stimulus, different behavior) and for sound response effects, compare Hit and False alarm trials (same behavior, different response). How do you align for time in the latter case when there's no stimulus? Align to the first lick event. The authors should include this analysis or explain why their approach of jumping right to analysis of clusters is justified.

We have now calculated the fraction of neurons that encode trial outcome by comparing hit and miss trial activity. That fraction does not differ between non-lesioned animals and lesioned animals as a whole, but is significantly smaller in mice with partial lesions. The author’s suggestion of comparing hit and false alarm trial activity to assess sound responsiveness is problematic because hit trials involve reward delivery and consumption. Consequently, they are behaviorally very different from false alarm trials (not least because hit trials tend to contain much more licking). Therefore, we calculated the fraction of neurons that respond to the acoustic stimulus by comparing activity before and after stimulus onset in miss trials. We found no significant difference between the non-lesioned and lesioned mice or between subgroups.

We have addressed these points with the following changes to the manuscript:

Line 217: “Indeed, close to half (1272 / 2649) of all neurons showed a statistically significant difference in response magnitude between hit and miss trials, while only a small fraction (97 / 2649) exhibited a significant response to the sound.”

Line 307: “Although the proportion of individual neurons with distinct response magnitudes in hit and miss trials in lesioned mice did not differ from that in non-lesioned mice, it was significantly lower when separating out mice with partial lesions (Figure 6 – figure supplement 3).”

Line 648: “Analysis of task-modulated and sound-driven neurons. To identify individual neurons that produced significantly different response magnitudes in hit and miss trials, we calculated the mean activity for each stimulus trial by taking the mean activity over the 5 seconds following stimulus presentation and subtracting the mean activity over the 2 seconds preceding the stimulus during that same trial. A Mann-Whitney U test was then performed to assess whether a neuron showed a statistically significant difference (Benjamini-Hochberg adjusted p-value of 0.05) in response magnitude between hit and miss trials. The analysis was performed using equal numbers of hit and miss trials at each sound level to ensure balanced sound level distributions. If, for a given sound level, there were more hit than miss trials, we randomly selected a sample of hit trials (without substitution) to match the sample size for the miss trials and vice versa. Sounddriven neurons were identified by comparing the mean miss trial activity before and after stimulus presentation. Specifically, we performed a Mann-Whitney U test to assess whether there was a statistically significant difference (Benjamini-Hochberg adjusted p-value of 0.05) between the mean activity over the 2 seconds preceding the stimulus and the mean activity over the 1 second period following stimulus presentation.”

Some more specific concerns about focusing only on cluster-level and population decoding analysis are included below.

(2) (L 234) "larger field of view". Do task-related or lesion-dependent effects depend on the subregion of IC imaged? Some anatomists would argue that the IC shell is not a uniform structure, and concomitantly, task-related effects may differ between fields. Did coverage of IC subregions differ between experimental groups? Is there any difference in task related effects between subregions of IC? Or maybe all this work was carried out only in the dorsal area? The differences between lesioned and non-lesioned animals are relatively small, so this may not have a huge impact, but a more nuanced discussion that accounts for observed or potential (if not tested) differences between regions of the IC.

The specific subregion coverage could also impact the decoding analysis (Fig 6), and if possible it might be worth considering an interaction between field of view and lesion size on decoding.

Each day we chose a new imaging location to avoid recording the same neurons more than once and aimed to sample widely across the optically accessible surface of the IC. We typically stopped the experiment only when there were no more new areas to record from. In terms of the depth of the imaged neurons, we were limited by the fact that corticorecipient neurons become sparser with depth and that the signal available from the GCaMP6f labeling of the Ai95 mice becomes rapidly weaker with increasing distance from the surface. This meant that we recorded no deeper than 150 µm from the surface of the IC. Consequently, while there may have been some variability in the average rostrocaudal and mediolateral positioning of imaging locations from animal to animal due to differences between mice in how much of the IC surface was visible, cranial window positioning, and in neuronal labeling etc, our dataset is anatomically uniform in that all recorded neurons receive input from the auditory cortex and are located within 150 µm of the surface of the IC. Therefore, we think it highly unlikely that small sampling differences across animals could have a meaningful impact on the results.

Given that there is no consensus as to where the border between the dorsal and external/lateral cortices of the IC is located and that it is typically difficult to find reliable anatomical reference points (the location of the borders between the IC and surrounding structures is not always obvious during imaging, i.e. a transition from a labeled area to a dark area near the edge of the cranial window could indicate a border with another structure, but also the IC surface sloping away from the window or simply an unlabeled area within the IC), we made no attempt to assign our recordings from corticorecipient neurons to specific subdivisions of the IC.

Changes to manuscript.

Line 195: “We then proceeded to record the activity of corticorecipient neurons within about 150 µm of the dorsal surface of the IC using two-photon microscopy (Figure 4B, Video 1).”

Line 375: “We imaged across the optically accessible dorsal surface of the IC down to a depth of about 150 µm below the surface. Consequently, the neurons we recorded were located predominantly in the dorsal cortex. However, identifying the borders between different subdivisions of the IC is not straightforward and we cannot rule out the possibility that some were located in the lateral cortex.”

(3) (L 482-483) "auditory cortex is not required for the task-related activity recording in IC neurons of mice performing a sound detection task". Most places in the text are clearer, but this statement is confusing. Yes, animals with lesions can have a "normal"-looking IC, but does that mean that AC does not strongly modulate IC during this behavior in normal animals? The authors have shown convincingly that subcortical areas can both shape behavior and modulate IC normally, but AC may still be required for IC modulation in non-lesioned animals. Given the complexity of this system, the authors should make sure they summarize their results consistently and clearly throughout the manuscript.

The reviewer raises an important point. What we have shown is that corticorecipient dorsal IC neurons in mice without auditory cortex show neural activity during a sound detection task that is largely indistinguishable from the activity of mice with an intact auditory cortex. In lesioned mice, the auditory cortex is thus not required. Whether the IC activity of the non-lesioned group can be shaped by input from the auditory cortex in a meaningful way in other contexts, such as during learning, is a question that our data cannot answer.

Changes to manuscript.

Line 508: "While modulation of IC activity by this descending projection has been implicated in various functions, most notably in the plasticity of auditory processing, we have shown in mice performing a sound detection task that IC neurons show task-related activity in the absence of auditory cortical input."

LESSER CONCERNS

(L. 106-107) "Optogenetic suppression of cortical activity is thus also unsuitable..." It appears that behavior is not completely abolished by the suppression. One could also imagine using a lower dose of muscimol for partial inactivation of AC feedback. When some behavior persists, it does seem possible to measure task-related changes in the IC. This may not be necessary for the current study, but the authors should consider how these transient methods could be applied usefully in the Discussion. What about inactivation of cortical terminals in the IC? Is that feasible?

Our argument is not that acute manipulations are unsuitable because they completely abolish the behavior, but because they significantly alter the behavior. Although it would not be trivial to precisely measure the extent of pharmacological cortical silencing in behaving mice that have been fitted with a midbrain window, it should be possible to titrate the size of a muscimol injection to achieve partial silencing of the auditory cortex that does not fully abolish the ability to detect sounds. However, such an outcome would likely render the data uninterpretable. If no effect on IC activity was observed, it would not be possible to conclude whether this was due to the fact that the auditory cortex was only partially silenced or that projections from the auditory cortex have no influence on the recorded IC activity. Similarly, if IC activity was altered, it would not be possible to say whether this was due to altered descending modulation resulting from the (partially) silenced auditory cortex or to the change in behavior, which would likely be reflected in the choice-related activity measured in the IC.

Silencing of corticocollicular axons in the IC is potentially a more promising approach and we did devote a considerable amount of time and effort to establishing a method that would allow us to simultaneously image IC neurons while silencing corticocollicular axons, trying both eNpHR3.0 and Jaws with different viral labeling approaches and mouse lines. However, we ultimately abandoned those attempts because we were not convinced that we had achieved sufficient silencing or that we would be able to convincingly verify this. Furthermore, axonal silencing comes with its own pitfalls and the interpretation of its consequences is not straightforward. Given that our discussion already contains a section (line 421) on axonal silencing, we do not feel there would be any benefit in adding to that.

(Figure 1). Can the authors break down the performance for FA and HR, as they do in Fig. 3? It would be helpful to know what aspect of behavior is impaired by the transient inactivation.

Good point. Figure 1 has been updated to show the results separately for hit rates, false alarms and d’. The new figure indicates that the change in d’ is primarily a consequence of altered false alarm rates. Please also see our response to a related comment by reviewer #1.

Changes to manuscript.

New figure 1.

(Figure 4 legend). Minor: Please clarify, what is time 0 in panel C? Time of click presentation?

Yes, that is correct.

Changes to manuscript.

Line 209: ”Vertical line at time 0 s indicates time of click presentation.”

(L. 228-229). There has been a report of lick and other motor related activity in the IC - e.g., see Shaheen, Slee et al. (J Neurosci 2021), the timing of which suggests that some of it may be acoustically driven.

Thanks for pointing this out. Shaheen et al., 2021 should certainly have been cited by us in this context as well as in other parts of the manuscript.

Changes to manuscript.

Line 243: “(Singla et al., 2017; but see Shaheen et al., 2021)”

Also, have the authors considered measuring a peri-lick response? The difference between hit and miss trials could be perceptual or it could reflect differences in motor activity. This may be hard to tease apart, but, for example, one can test whether activity is stronger on trials with many licks vs. few licks?

(L. 261) "Behavior can be decoded..." similar or alternative to the previous question of evoked activity, can you decode lick events from the population activity?

The difference between hit and miss trial activity almost certainly partially reflects motor activity associated with licking. This was stated in the Discussion, but to make that point more explicitly, we now include a plot of average false alarm trial activity, i.e. trials without sound (catch trials) in which animals licked (but did not receive a reward).

Given a sufficient number of catch trials, it should be possible to decode false alarm and correct rejection trials. However, our experiment was not designed with that in mind and contains a much smaller number of catch trials than stimulus trials (approximately one tenth the number of stimulus trials), so we have not attempted this.

Changes to manuscript.

New Figure 4 - figure supplement 1.

(L. 315) "Pre-stimulus activity..." Given reports of changes in activity related to pupil-indexed arousal in the auditory system, do the authors by any chance have information about pupil size in these datasets?

Given that all recordings were performed in the dark, fluctuations in pupil diameter were relatively small. Therefore, we have not made any attempt to relate pupil diameter to any of the variables assessed in this manuscript.

(L. 412) "abolishes sound detection". While not exactly the same task, the authors might comment on Gimenez et al (J Neurophys 2015) which argued that temporary or permanent lesioning of AC did not impair tone discrimination. More generally, there seems to be some disagreement about what effects AC lesions have on auditory behavior.

Thank you for this suggestion. Gimenez et al. (2015) investigated the ability of freely moving rats to discriminate sounds (and, in addition, how they adapt to changes in the discrimination boundary). Broadly consistent with later reports by Ceballo et al. (2019) (mild impairment) and O’Sullivan et al. (2019) (no impairment), Gimenez et al. (2015) reported that discrimination performance is mildly impaired after lesioning auditory cortex. Where the results of Gimenez et al. (2015) stand out is in the comparatively mild impairments that were seen in their task when they used muscimol injections, which contrast with the (much) larger impairments reported by others (e.g. Talwar et al., 2001; Li et al., 2017; Jaramillo and Zador, 2014).

Changes to manuscript.

Line 433: ”However, transient pharmacological silencing of the auditory cortex in freely moving rats (Talwar et al., 2001), as well as head-fixed mice (Li et al., 2017), completely abolishes sound detection (but see Gimenez et al., 2015).”

(L. 649) "... were generally separable" Is the claim here that the clusters are really distinct from each other? This is unexpected, and it might be helpful if the authors could show this result in a figure.

The half-sentence that this comment refers to has been removed from the methods section. Please also see a related comment by reviewer #1 which prompted us to add the following to the methods section.

Changes to manuscript.

Line 666: “While clustering is a useful approach for organizing and visualizing the activity of large and heterogeneous populations of neurons we need to be mindful that, given continuous distributions of response properties, the locations of cluster boundaries can be somewhat arbitrary and/or reflect idiosyncrasies of the chosen method and thus vary from one algorithm to another. We employed an approach very similar to that described in Namboodiri et al. (2019) because it is thought to produce stable results in high-dimensional neural data (Hirokawa et al. 2019).”

Reviewer #3 (Recommendations For The Authors):

(1) The authors must absolutely clarify if the hit versus misses decoding and clustering analysis is done for a single sound level or for multiple sound levels (what is the fraction of trials for each sound leve?). If the authors did it for multiple sound levels they should redo all analyses sound-level by sound-level, or for a single sound level if there is one that dominates. No doubt that there is information about the trial outcome in IC, but it should not be over-estimated by a confound with stimulus information.

This is an important point. The original clustering analysis was carried out across different sound levels. We have now carried out additional analysis for distinguishing between two alternative explanations of the data, which were also raised by reviewer #1. – that the difference in neural activity between hit and miss trials could reflect a) the animals’ behavior or b) relatively more hit trials at higher sound levels, which would be expected to produce stronger responses. If the data favored b), we would expect no difference in activity between hit and miss trials when plotted separately for different sound levels. The new figure 4 - figure supplement 1 indicates that that is not the case. Hit and miss trial activity are clearly distinct even when plotted separately for different sound levels, confirming that this difference in activity reflects the animals’ behavior rather than sensory information.

We made the following changes to manuscript.

Line 214: “While averaging across all neurons cannot capture the diversity of responses, the averaged response profiles suggest that it is mostly trial outcome rather than the acoustic stimulus and neuronal sensitivity to sound level that shapes those responses (Figure 4 – figure supplement 1).”

Differences in the distributions of sound levels in the different trial types could also potentially confound the decoding into hit and miss trials. Our analysis actually aimed to take this into account but, unfortunately, we failed to include sufficient details in the methods section.

Changes to manuscript.

Line 710: “Rather than including all the trials in a given session, only trials of intermediate difficulty were used for the decoding analysis. More specifically, we only included trials across five sound levels, comprising the lowest sound level that exceeded a d’ of 1.5 plus the two sound levels below and above that level. That ensured that differences in sound level distributions would be small, while still giving us a sufficient number of trials to perform the decoding analysis.“

In this context, it is worth bearing in mind that a) the decoding analysis was done on a frame-byframe basis, meaning that the decoding score achieved early in the trial has no impact on the decoding score at later time points in the trial, b) sound-driven activity predominantly occurs immediately after stimulus onset and is largely over about 1 s into the trial (see cluster 3, for instance, or average miss trial activity in figure 4 - figure supplement 1), c) decoding performance of the behavioral outcome starts to plateau 500-1000 ms into the trial and remains high until it very gradually begins to decline after about 2 s into the trial. In other words, decoding performance remains high far longer than the stimulus would be expected to have an impact on the neurons’ activity. Therefore, we would expect any residual bias due to differences in the sound level distribution that our approach did not control for to be restricted to the very beginning of the trial and not to meaningfully impact the conclusions derived from the decoding analysis.

Furthermore, we carried out an additional decoding analysis for one imaging session in which we had a sufficient number of trials to perform the analysis not only over the five (59, 62, 65, 68, 71 dB SPL) original sound levels, but also over a reduced range of three (62, 65, 68 dB SPL) sound levels, as well as a single (65 dB SPL) sound level (Figure 6 - figure supplement 1). The mean sound level difference between the hit trial distributions and miss trial distributions for these three conditions were 3.08, 1.01 and 0 dB, respectively. This analysis suggests that decoding performance is not meaningfully impacted by changing the range of sound levels (and sound level distributions) other than that including fewer sound levels means fewer trials and thus noisier decoding.

Changes to manuscript.

Line 287: ”...and was not meaningfully affected by differences in sound level distributions between hit and miss trials (Figure 6 – figure supplement 1).”

Finally, in order to supplement the decoding analysis, we determined for each individual neuron whether there was a significant difference between the average hit and average miss trial activity. Note that this was done using equal numbers of hit and miss trials at each sound level to ensure balanced sound level distributions and to rule out any potential confound of sound level. This revealed that the proportion of neurons containing “information about trial outcome” was generally very high, close to 50% on average, and not significantly different between lesioned and non-lesioned mice.

Changes to manuscript.

Line 307: “Although the proportion of individual neurons with distinct response magnitudes in hit and miss trials in lesioned mice did not differ from that in non-lesioned mice, it was significantly lower when separating out mice with partial lesions (Figure 6 – figure supplement 3).”

Line 648: “Analysis of task-modulated and sound-driven neurons. To identify individual neurons that produced significantly different response magnitudes in hit and miss trials, we calculated the mean activity for each stimulus trial by taking the mean activity over the 5 seconds following stimulus presentation and subtracting the mean activity over the 2 seconds preceding the stimulus during that same trial. A Mann-Whitney U test was then performed to assess whether a neuron showed a statistically significant difference (Benjamini-Hochberg adjusted p-value of 0.05) in response magnitude between hit and miss trials. The analysis was performed using equal numbers of hit and miss trials at each sound level to ensure balanced sound level distributions. If, for a given sound level, there were more hit than miss trials we randomly selected a sample of hit trials (without substitution) to match the sample size for the miss trials and vice versa. ”

(2) I have the feeling that the authors do not exploit fully the functional data recorded with two-imaging. They identify several cluster but do not describe their functional differences. For example, cluster 3 is obviously mainly sensory driven as it is not modulated by outcome. This could be mentioned. This could also be used to rule out that trial outcome is the results of insufficient sensory inputs. Could this cluster be used to predict trial outcome at the onset response? Could it be used to predict the presence of the sound, and with which accuracy. The authors discuss a bit the different cluster type, but in a very elusive manner. I recognize that one should be careful with the use of signal analysis methods in calcium imaging but a simple linear deconvolution of the calcium dynamic who help to illustrate the conclusions that the authors propose based on peak responses. It would also be very interesting to align the clusters responses (deconvolved) to the timing of licking and rewards event to check if some clusters do not fire when mice perform licks before the sound comes. It would help clarify if the behavioral signals described here require both the presence of the sound and the behavioral action or are just the reflection of the motor command. As noted by the authors, some clusters have late peak responses (2 and 5). However, 2 and 5 are not equivalent and a deconvolution would evidence that much better. 2 has late onset firing. 5 has early onset but prolonged firing.

We agree with the reviewer’s statement that “cluster 3 is obviously mainly sensory driven”. In the Discussion we refer to cluster 3 as having a “largely behaviorally invariant response profile to the auditory stimulus” (line X), which is consistent with the statement of the reviewer. With regard to the reviewer’s suggestion to describe the “functional differences” between the clusters, we would like to refer to the subsequent three sentences of the same paragraph in which we speculate on the cognitive and behavioral variables that may underlie the response profiles of different clusters. Given the limitations imposed by the task structure, we do not think it is justified to expand on this.

We have added an additional analysis in order to explicitly address the question of which neurons are sound responsive (please also see response to point 3 below and to point 1 of reviewer #2). That trial outcome could be predicted on the basis of only the sound-responsive neurons’ activity during the initial period of the trial (“predict trial outcome at the onset response”) is unlikely given their small number (only 97 of 2649 neurons show a statistically significant sound-evoked response) and given that only a minority (42/98) of those sound-driven neurons are also modulated by trial outcome within that initial trial period (i.e. 0-1s after stimulus onset; data not shown).

Changes to manuscript.

Line 219: “..., while only a small fraction (97 / 2649) exhibited a significant response to the sound.”

Line 658: “Sound-driven neurons were identified by comparing the mean miss trial activity before and after stimulus presentation. Specifically, we performed a Mann-Whitney U test to assess whether there was a statistically significant difference (Benjamini-Hochberg adjusted p-value of 0.05) between the mean activity over the 2 seconds preceding the stimulus and the mean activity over the 1 second period following stimulus presentation. This analysis was performed using miss trials with click intensities from 53 dB SPL to 65 dB SPL (many sessions contained very few or no miss trials at higher sound levels).”

While calcium traces represent an indirect measure of neural activity, deconvolution does not necessarily provide an accurate picture of the spiking underlying those traces and has the potential to introduce additional problems. For instance, deconvolution algorithms tend to perform poorly at inferring the spiking of inhibited neurons (Vanwalleghem et al., 2021). Given that suppression is such a prominent feature of IC activity and is evident both in our calcium data as well as in the electrophysiology data of others (Franceschi and Barkat, 2021), we decided against using deconvolved spikes in our analyses. See also the side-by-side comparison below of the hit and miss trial activity of one example neuron based on either the calcium trace (left) or deconvolved spikes (right) (extracted using the OASIS algorithm (Friedrich et al., 2017) incorporated into suite2p (Pachitariu et al., 2016).

Author response image 1.

(3) Along the same line, the very small proportion of really sensory driven neurons (cluster 3) is not discussed. Is it what on would expect in typical shell or core IC neurons?

As requested by reviewer #2 and mentioned in response to the previous point, we have now quantified the number of neurons in the dataset that produced significant responses to sound (97 / 2649). For a given imaging area, the fraction of neurons that show a statistically significant change in neural activity following presentation of a click of between 53 dB SPL and 65 dB SPL rarely exceeded ten percent. While that number is low, it is not necessarily surprising given the moderate intensity and very short duration of the stimuli. For comparison: Using the same transgenics, labeling approach and imaging setup and presenting 200-ms long pure tones at 60 dB SPL with frequencies between 2 kHz and 64 kHz, we typically find that between a quarter and a third of neurons in a given imaging area exhibit a statistically significant response (data not shown).

Changes to manuscript.

Line 219: “..., while only a small fraction (97 / 2649) exhibited a significant response to the sound.”

Line 658: “Sound-driven neurons were identified by comparing the mean miss trial activity before and after stimulus presentation. Specifically, we performed a Mann-Whitney U test to assess whether there was a statistically significant difference (Benjamini-Hochberg adjusted p-value of 0.05) between the mean activity over the 2 seconds preceding the stimulus and the mean activity over the 1 second period following stimulus presentation. This analysis was performed using miss trials with click intensities from 53 dB SPL to 65 dB SPL (many sessions contained very few or no miss trials at higher sound levels).”

Line 220: “While the number of sound-responsive neurons is low, it is not necessarily surprising given the moderate intensity and very short duration of the stimuli. For comparison: Using the same transgenics, labeling approach and imaging setup and presenting 200-ms long pure tones at 60 dB SPL with frequencies between 2 kHz and 64 kHz, we typically find that between a quarter and a third of neurons in a given imaging area exhibit a statistically significant response (data not shown).”

(4) In the discussion, the interpretation of different transient and permanent cortical inactivation experiment is very interesting and well balanced given the complexity of the issue. There is nevertheless a comment that is difficult to follow. The authors state:

If cortical lesioning results in a greater weight being placed on the activity in spared subcortical circuits for perceptual judgements, we would expect the accuracy with which trial-by-trial outcomes could be read out from IC neurons to be greater in mice without auditory cortex. However, that was not the case.

However, there is no indication that the activity they observe in shell IC is causal to the behavioral decision and likely it is not. There is also no indication that the behavioral signals seen by the authors reflect the weight put on the subcortical pathway for behavior. I find this argument handwavy and would remove it.

While we are happy to amend this section, we would not wish to remove it because a) we believe that the point we are trying to make here is an important and reasonable one and b) because it is consistent with the reviewer’s comment. Hopefully, the following will make this clearer: In order for the mouse to make a perceptual judgment and act upon it - in the context of our task, hearing a sound and then licking a spout - auditory information needs to be read out and converted into a motor command. If the auditory cortex normally plays a key role in such perceptual judgments, cortical lesions would require the animal to base its decisions on the information available from the remaining auditory structures, potentially including the auditory midbrain. This might result in a greater correspondence between the mouse’s behavior and the neural activity in those structures. That we did not observe this outcome for the IC could mean that the auditory cortex did not contribute to the relevant perceptual judgments (sound detection) in the first place. Therefore, no reweighting of signals from the other structures is necessary. Alternatively, greater weight might be placed exclusively on structures other than the auditory midbrain, e.g. the thalamus. The latter would imply that the contribution of the IC remains the same. This includes the possibility that the IC shell does not play a causal role in the behavioral decision – in either control mice or mice with cortical lesions – as suggested by the reviewer.

Changes to manuscript.

Line 471: “This could imply that, following cortical lesions, greater weight is placed on structures other than the IC, with the thalamus being the most likely candidate, ..”

(5) In Fig. 5 the two colors used in B and C are the same although they describe different categories.

The dark green and ‘deep orange’ we used to distinguish between non-lesioned and lesioned in Figure 5C are slightly lighter than the colors used to distinguish between these two categories in other figures and therefore might be more easily confused with the blue and red in Figure 5B. This has been changed.

Author response:

The following is the authors’ response to the current reviews.

We thank the Reviewers and Editors for the constructive comments, which we believe have significantly improved the quality of our manuscript.

The following is the authors’ response to the original reviews.

Reviewer #1 (Public Review):

(1) With respect to the predictions, the authors propose that the subjects, depending on their linguistic background and the length of the tone in a trial, can put forward one or two predictions. The first is a short-term prediction based on the statistics of the previous stimuli and identical for both groups (i.e. short tones are expected after long tones and vice versa). The second is a long-term prediction based on their linguistic background. According to the authors, after a short tone, Basque speakers will predict the beginning of a new phrasal chunk, and Spanish speakers will predict it after a long tone.

In this way, when a short tone is omitted, Basque speakers would experience the violation of only one prediction (i.e. the short-term prediction), but Spanish speakers will experience the violation of two predictions (i.e. the short-term and long-term predictions), resulting in a higher amplitude MMN. The opposite would occur when a long tone is omitted. So, to recap, the authors propose that subjects will predict the alternation of tone durations (short-term predictions) and the beginning of new phrasal chunks (long-term predictions).

The problem with this is that subjects are also likely to predict the completion of the current phrasal chunk. In speech, phrases are seldom left incomplete. In Spanish is very unlikely to hear a function-word that is not followed by a content-word (and the opposite happens in Basque). On the contrary, after the completion of a phrasal chunk, a speaker might stop talking and a silence might follow, instead of the beginning of a new phrasal chunk.

Considering that the completion of a phrasal chunk is more likely than the beginning of a new one, the prior endowed to the participants by their linguistic background should make us expect a pattern of results actually opposite to the one reported here.

We thank the Reviewer #1 for this pertinent comment and the opportunity to address this issue. A very similar concern was also raised by Reviewer #2. Below we try to clarify the motivations that led us to predict that the hypothesized long-term predictions should manifest at the onset (and not within or the end) of a perceptual chunk. 

Reviewers #1 and #2 contest a critical assumption of our study i.e., the fact that longterm predictions should occur at the beginning of a rhythmic chunk as opposed to its completion. They also contest the prediction deriving from this view i.e., omitting the first sound in a perceptual chunk (short for Spanish, long for Basque) would lead to larger error responses than omitting a later element. They suggest an alternative view: the omission of tones at the end of a perceptual rhythmic chunk would evoke larger error responses than omissions at its onset, as subjects are more likely to predict the completion of the chunk than its beginning. This view predicts an interaction effect in the opposite direction of our findings. 

While we acknowledge this as a plausible hypothesis, we believe that the current literature provides strong support for our view. Indeed, many studies in the rhythm and music perception literature have investigated the ERP responses to deviant sounds and omissions placed at different positions within rhythmic patterns (e.g., Ladinig et al., 2009; Bouwer et al., 2016; Brochard et al., 2003; Potter et al., 2009; Yabe et al., 2001). For instance, Lading et al., 2009 presented participants with metrical rhythmical sound sequences composed of eight tones. In some deviant sequences, the first or a later tone was omitted. They found that earlier omissions elicited earlier and higher-amplitude MMN responses than later omissions (irrespective of attention). Overall, this and other studies showed that the amplitude of ERP responses are larger when deviants occur at positions that are expected to be the “start” of a perceptual group - “on the beat” in musical terms - and decline toward the end of the chunk. According to some of these studies, the first element of a chunk is particularly important to track the boundaries of temporal sequences, which is why more predictive resources are invested at that position. We believe that this body of evidence provides robust bases for our hypotheses and the directionality of our predictions.

An additional point that should be considered concerns the amplitude of the prediction error response elicited by the omission. From a predictive coding perspective, the omission of the onset of a chunk should elicit larger error responses because the system is expecting the whole chunk (i.e., two tones/more acoustic information). On the other hand, the omission of the second tone - in the transition between two tones within the chunk - should elicit a smaller error response because the system is expecting only the missing tone (i.e. less acoustic information). 

Given the importance of these points, we have now included them in the updated version of the paper, in which we try to better clarify the rationale behind our hypothesis (see Introduction section, around the 10th paragraph).

(2) The authors report an interaction effect that modulates the amplitude of the omission response, but caveats make the interpretation of this effect somewhat uncertain. The authors report a widespread omission response, which resembles the classical mismatch response (in MEG) with strong activations in sensors over temporal regions. Instead, the interaction found is circumscribed to four sensors that do not overlap with the peaks of activation of the omission response.

We thank the Reviewer for this comment. As mentioned in the provisional response, the approach employed to identify the presence of an interaction effect was conservative: We utilized a non-parametric test on combined gradiometers data, without making a priori assumptions about the location of the effect, and employed small cluster thresholds (cfg.clusteralpha = 0.05) to increase the chances of detecting highly localized clusters with large effect sizes. The fact that the interaction effect arises in a relatively small cluster of sensors does not alter its statistical robustness. It should be also considered that in the present analyses we focused on planar gradiometer data that, compared to magnetometers and axial gradiometers, present more fine-grained spatial resolution and are more suited for picking up relatively small effects. 

The partial overlap of the cluster with the activation peaks may simply reflect the fact that different sources contribute to the generation of the omission-MMN, which has been reported in several studies (e.g., Zhang et al., 2018; Ross & Hamm, 2020).  We value the Reviewer’s input and are grateful for the opportunity to address these considerations.

Furthermore, the boxplot in Figure 2E suggests that part of the interaction effect might be due to the presence of two outliers (if removed, the effect is no longer significant). Overall, it is possible that the reported interaction is driven by a main effect of omission type which the authors report, and find consistently only in the Basque group (showing a higher amplitude omission response for long tones than for short tones). Because of these points, it is difficult to interpret this interaction as a modulation of the omission response.

We thank the Reviewer for the comment and appreciate the opportunity to address these concerns. We have re-evaluated the boxplot in Figure 2E and want to clarify that the two participants mentioned by Reviewer #1, despite being somewhat distant from the rest of the group, are not outliers according to the standard Tukey’s rule. As shown in the figure below, no participant fell outside the upper (Q3+1.5xIQR) and lower whiskers (Q1-1.5xIQR) of the boxplot. 

Moreover, we believe that the presence of a main effect of omission type does not impact the interpretation of the interaction, especially considering that these effects emerge over distinct clusters of channels (see Fig. 1 C; Supplementary Fig. 2 A). 

Based on these considerations - and along with the evidence collected in the control study and the source reconstruction data reported in the new version of the manuscript - we find it unlikely that the interaction effect is driven by outliers or by a main effect of omission type. We appreciate the opportunity provided by the Reviewer to address these concerns, as we believe they strengthen the claim that the observed effect is driven by the hypothesized long-term linguistic priors rather than uncontrolled group differences.

Author response image 1.

It should also be noted that in the source analysis, the interaction only showed a trend in the left auditory cortex, but in its current version the manuscript does not report the statistics of such a trend.

We  appreciate  the  Reviewer’s  suggestion  to  incorporate  more comprehensive source analyses. In the new version of the paper, we perform new analyses on the source data using a new Atlas with more fine-grained parcellations of the regions of interests (ROIs) (Brainnetome atlas; Fan et al., 2016) and focusing on peak activity to increase response’s sensitivity in space and time. We therefore invite the Reviewer to read the updated part on source reconstruction included in the Results and Methods sections of the paper.  

Reviewer #1 (Recommendations For The Authors):

While I have described my biggest concerns with respect to this work in the public review, here I list more specific points that I hope will help to improve the manuscript. Some of these are very minor, but I hope you will still find them constructive. 

(1) I understand the difficulties implied in recruiting subjects from two different linguistic groups, but with 20 subjects per group and a between-groups design, the current study is somewhat underpowered. A post-hoc power analysis shows an achieved power of 46% for medium effect sizes (d = 0.5, and alpha = 0.05, one-sided test). A sensitivity analysis shows that the experiment only has 80% power for effect sizes of d = 0.8 and above. It would be important to acknowledge this limitation in the manuscript. 

We thank the Reviewer for reporting these analyses. It must be noted that our effect of interest was based on Molnar et al.’s (2016) behavioral experiment, in which a sample size of 16 subjects per group was sufficient to detect the perceptual grouping effect. In Yoshida et al., (2010), the perceptual grouping effect emerged with two groups of 20 7–8-month-old Japanese and English-learning infants. Based on these previous findings, we believe that a sample size of 20 participants per group can be considered appropriate for the current MEG study. We clarified these aspects in the Participants section of the manuscript, in which we specified that previous behavioral studies detected the perceptual grouping with similar sample sizes. Moreover, to acknowledge the limitation highlighted by the Reviewer, we also include the power and sensitivity analysis in a note in the same section (see note 2 in the Participants section).

(2) All the line plots in the manuscript could be made much more informative by adding 95% CI bars. For example, in Figure 4A, the omission response for the long tone departs from the one for the short tone very early. Adding CIs would help to assess the magnitude of that early difference. Error bars are present in Figure 3, but it is not specified what these bars represent. 

Thanks for the comments. We added the explanation of the error bars in the new version of Figure 3. For the remaining figures, we prefer maintaining the current version of the ERF, as the box-plots accompanying them provide information about the distribution of the effect across participants.

(3) In the source analysis, there is only mention of an interaction trend in the left auditory cortex, but no statistics are presented. If the authors prefer to mention such a trend, I think it would be important to provide its stats to allow the reader to assess its relevance. 

We performed new analysis on the source data, all reported in the updated version of the manuscript.

(4) In the discussion section, the authors refer to the source analysis and state that "the interaction is evident in the left". But if only a statistical trend was observed, this statement would be misleading. 

We agree with this comment. We invite the Reviewer to check the new part on source reconstruction, in which contrasts going in the same direction of the sensor level data are performed.

(5) In the discussion the authors argue that "This result highlights the presence of two distinct systems for the generation of auditory" that operate at different temporal scales, but the current work doesn't offer evidence for the existence of two different systems. The effects of long-term priors and short-term priors presented here are not dissociated and instead sum up. It remains possible that a single system is in place, collecting statistics of stimuli over a lifetime, including the statistics experienced during the experiment. 

Thanks for pointing that out. We changed the sentence above as follows: “This result highlights the presence of an active predictive system that relies on natural sound statistics learned over a lifetime to process incoming auditory input”.

(6) In the discussion, the authors acknowledge that the omission response has been interpreted both as pure prediction and as pure prediction error. Then they declare that "Overall, these findings are consistent with the idea that omission responses reflect, at least in part, prediction error signals.". However an argument for this statement is not provided. 

Thanks for pointing out this lack of argument. In the new version of the manuscript, we explained our rationale as follows: “Since sensory predictive signals primarily arise in the same regions as the actual input, the activation of a broader network of regions in omission responses compared to tones suggests that omission responses reflect, at least in part, prediction error signals”.

(7) In the discussion the authors present an alternative explanation in which both groups might devote more resources to the processing of long events, because these are relevant content words. Following this, they argue that "Independently on the interpretation, the lack of a main effect of omission type in the control condition suggests that the long omission effect is driven by experience with the native language." However as there was no manipulation of duration in the control experiment, a lack of the main effect of omission type there does not rule out the alternative explanation that the authors put forward. 

This is correct; thanks for noticing it. We removed the sentence above to avoid ambiguities.

Minor points: 

(8) The scale of the y-axis in Figure 2C might be wrong, as it goes from 9 to 11 and then to 12. If the scale is linear, the top value should be 13, or the bottom value should be 10. 

Figure 2C has been modified accordingly, thanks for noticing the error.

(9) There is a very long paragraph starting on page 7 and ending on page 8. Toward the end of the paragraph, the analysis of the control condition is presented. That could start a new paragraph.

Thanks for the suggestion. We modified the manuscript as suggested.

Reviewer #2 (Public Review):

(1) Despite the evidence provided on neural responses, the main conclusion of the study reflects a known behavioral effect on rhythmic sequence perceptual organization driven by linguistic background (Molnar et al. 2016, particularly). Also, the authors themselves provide a good review of the literature that evidences the influence of longterm priors in neural responses related to predictive activity. Thus, in my opinion, the strength of the statements the authors make on the novelty of the findings may be a bit far-fetched in some instances.

Thanks for the suggestion. A similar point was also advanced by Reviewer 1. In general, we believe our work speaks about the predictive nature of such experiencedependent  effects, and show that these linguistic priors shape sensory processes at very early stages. This is discussed in the sixth and seventh paragraphs of the Discussion section. In the new version of the article, we modified some statements and tried to make them more coherent with the scope of the present work. For instance, we changed "This result highlights the presence of two distinct systems for the generation of auditory predictive models, one relying on the transition probabilities governing the recent past, and another relying on natural sound statistics learned over a lifetime“ with “This result highlights the presence of an active predictive system that relies on natural sound statistics learned over a lifetime to process incoming auditory input”.

(2) Albeit the paradigm is well designed, I fail to see the grounding of the hypotheses laid by the authors as framed under the predictive coding perspective. The study assumes that responses to an omission at the beginning of a perceptual rhythmic pattern will be stronger than at the end. I feel this is unjustified. If anything, omission responses should be larger when the gap occurs at the end of the pattern, as that would be where stronger expectations are placed: if in my language a short sound occurs after a long one, and I perceptually group tone sequences of alternating tone duration accordingly, when I hear a short sound I will expect a long one following; but after a long one, I don't necessarily need to expect a short one, as something else might occur.

A similar point was advanced by Reviewer #1. We tried to clarify the rationale behind our hypothesis. Please refer to the response provided to the first comment of Reviewer #1 above.

(3) In this regard, it is my opinion that what is reflected in the data may be better accounted for (or at least, additionally) by a different neural response to an omission depending on the phase of an underlying attentional rhythm (in terms of Large and Jones rhythmic attention theory, for instance) and putative underlying entrained oscillatory neural activity (in terms of Lakatos' studies, for instance). Certainly, the fact that the aligned phase may differ depending on linguistic background is very interesting and would reflect the known behavioral effect.

We thank the Reviewer for this comment. We explored in more detail the possibility that the aligned phase may differ depending on linguistic background, which is indeed a very interesting hypothesis. In the phase analyses reported below we focused on the instantaneous phase angle time locked to the onset of short and long tones presented in the experiment.

In short, we extracted time intervals of two seconds centered on the onset of the tones for each participant (~200 trials per condition) and using a wavelet transform (implemented in Fieldtrip ft_freqanalysis) we targeted the 0.92 Hz frequency that corresponds to the rhythm of presentation of our pairs of tones. We extracted the phase angle for each time point and using the circular statistics toolbox implemented in Matlab we computed the Raleigh z scores across all the sensor space for each tone (long and short tone) and group (Spanish (Spa) dominants and Basque (Eus) dominants). This method evaluates the instantaneous phase clustering at a specific time point, thus evaluating the presence of a specific oscillatory pattern at the onset of the specific tone. 

Author response image 2.

Here we observe that the phase clustering was stronger in the right sensors for both groups. The critical point is to evaluate the phase angle (estimated in phase radians) for the two groups and the two tones and see if there are statistical differences. We focused first on the sensor with higher clustering (right temporal MEG1323) and observed very similar phase angles for the two groups both for long and short tones (see image below). We then focused on the four left fronto-temporal sensor pairs who showed the significant interaction: here we observed one sensor (MEG0412) with different effects for the two groups (interaction group by tone was significant, p=0.02): for short tones the “Watson (1961) approximation U2 test” showed a p-value of 0.11, while for long tones the p-value was 0.03 (after correction for multiple comparisons). 

Overall, the present findings suggest the tendency to phase aligning differently in the two groups to long and short tones in the left fronto-temporal hemisphere. However, the effect could be detected only in one gradiometer sensor and it was not statistically robust. The effect in the right hemisphere was statistically more robust, but it was not sensitive to group language dominance. 

Due to the inconclusive nature of these analyses regarding the role of language experience in shaping the phase alignment to rhythmic sound sequences, we prefer to keep these results in the public review rather than incorporating them in the article.  Nonetheless, we believe that this decision does not undermine the main finding that the group differences in the MMN amplitude are driven by long-term predictions – especially in light of the many studies indicating the MMN as a putative index of prediction error (e.g., Bendixen et al., 2012; Heilbron and Chait, 2018). Moreover, as suggested in the preliminary reply, despite evoked responses and oscillations are often considered distinct electrophysiological phenomena, current evidence suggests that these phenomena are interconnected (e.g., Studenova et al., 2023). In our view, the hypotheses that the MMN reflects differences in phase alignment and long-term prediction errors are not mutually exclusive.

Author response image 3.

(4) Source localization is performed on sensor-level significant data. The lack of  sourcelevel statistics weakens the conclusions that can be extracted. Furthermore, only the source reflecting the interaction pattern is taken into account in detail as supporting their hypotheses, overlooking other sources. Also, the right IFG source activity is not depicted, but looking at whole brain maps seems even stronger than the left. To sum up, source localization data, as informative as it could be, does not strongly support the author's claims in its current state. 

A similar comment was also advanced by Reviewer #1 (comment 2). We appreciate the suggestion to incorporate more comprehensive source analyses. In the new version of the paper, we perform new analyses on the source data using a new Atlas with more fine-grained parcellations of the ROIs, and focusing on peak activity to increase response’s sensitivity in space and time. We therefore invite the Reviewer to read the updated part on source reconstruction included in the Results and Methods sections of the paper. 

In the article, we report only the source reconstruction data from ROIs in the left hemisphere, because it is there that the interaction effect arises at the sensor level. However, we also explored the homologous regions in the right hemisphere, as requested by the Reviewer. A cluster-based permutation test focusing on the interaction between language group and omission type was performed on both the right STG and IFG data. No significant interaction emerged in any of these regions. Below a plot of the source activity time series over ROIs in the right STG and IFG. 

Author response image 4.

Reviewer #2 (Recommendations For The Authors):

In this set of private recommendations for the authors, I will outline a couple of minor comments and try to encourage additional data analyses that, in my opinion, would strengthen the evidence provided by the study. 

(1) As I noted in the public review, I believe an oscillatory analysis of the data would, on one hand, provide stronger support for the behavioral effect of rhythmic perceptual organization given the lack of behavioral direct evidence; and, on the other hand, provide evidence (to be discussed if so) for a role of entrained oscillation phase in explaining the different pattern of omission responses. One analysis the authors could try is to measure the phase angle of an oscillation, the frequency of which relates to the length of the binary pattern, at the onset of short and long tones, separately, and compare it across groups. Also, single trials of omission responses could be sorted according to that phase. 

Thanks for the suggestion. Please see phase analyses reported above.

(2) I wonder why source activity for the right IFG was not shown. I urge the authors to provide and discuss a more complete picture of the source activity found. Given the lack of source statistics (which could be performed), I find it a must to give an overall view. I find it so because I believe the distinction between perceptual grouping effects due to inherent acoustic differences across languages or semantic differences is so interesting. 

Thanks again for the invitation to provide a more complete picture of the source activity data. As mentioned in the response above, we invite the Reviewer to read the new related part included in the Results and Methods sections of the paper. In our updated source reconstruction analysis, we find that some regions around the left STG show a pattern that resembles the one found at the sensor-level, providing further support for the “acoustic” (rather than syntactic/semantic) nature of the effect. 

We did not report ROI analysis on the right hemisphere because the interaction effect at sensor level emerged on the left hemisphere. Yet, we included a summary of this analysis in the public response above. 

(3) Related to this, I have to acknowledge I had to read the whole Molnar et al. (2016) study to find the only evidence so far that, acoustically, in terms of sound duration, Basque and Spanish differ. This was hypothesized before but only at Molnar, an acoustic analysis is performed. I think this is key, and the authors should give it a deeper account in their manuscript. I spend my review of this study thinking, well, but when we speak we actually bind together different words and the syllabic structure does not need to reflect the written one, so maybe the effect is due to a high-level statistical prior related to the content of the words... but Molnar showed me that actually, acoustically, there's a difference in accent and duration: "Taken together, Experiments 1a and 1b show that Basque and Spanish exhibit the predicted differences in terms of the position of prosodic prominence in their phonological phrases (Basque: trochaic, Spanish: iambic), even though the acoustic realization of this prominence involves not only intensity in Basque but duration, as well. Spanish, as predicted, only uses duration as a cue to mark phrasal prosody." 

Thanks for the suggestion, the distinction in terms of sound duration in Spanish and Basque reported by Molnar is indeed very relevant for the current study. 

We add a few sentences to highlight the acoustic analysis by Molnar and the consequent acoustic nature of the reported effect.

In the introduction: “Specifically, the effect has been proposed to depend on the quasiperiodic alternation of short and long auditory events in the speech signal – reported in previous acoustic analyses (Molnar et al., 2016) – which reflect the linearization of function words (e.g., articles, prepositions) and content words (e.g., nouns, adjectives, verbs).”

In the discussion, paragraph 3, we changed “We hypothesized that this effect is linked to a long-term “duration prior” originating from the syntactic function-content word order of language, and specifically, from its acoustic consequences on the prosodic structure” with “We hypothesized that this effect is linked to a long-term “duration prior” originating from the acoustic properties of the two languages, specifically from the alternation of short and long auditory events in their prosody”.

In the discussion, end of paragraph eight: “The reconstruction of cortical sources associated with the omission of short and long tones in the two groups showed that an interaction effect mirroring the one at the sensor level was present in the left STG, but not in the left IFG (fig. 3, B, C, D). Pairwise comparisons within different ROIs of the left STG indicated that the interaction effect was stronger over primary (BA 41/42) rather than associative (BAs 22) portions of the auditory cortex. Overall, these results suggest that the “duration prior” is linked to the acoustic properties of a given language rather than its syntactic configurations”.

Now, some minor comments: 

(1) Where did the experiments take place? Were they in accordance with the Declaration of Helsinki? Did participants give informed consent? 

All the requested information has been added to the updated version of the manuscript. Thanks for pointing out this.

(2) The fixed interval should be called inter-stimulus interval. 

Thanks for pointing this out. We changed the wording as suggested.

(3) The authors state that "Omission responses allow to examine the presence of putative error signals decoupled from bottom-up sensory input, offering a critical test for predictive coding (Walsh et al 2020, Heilbron and Chait, 2018).". However the way omission responses are computed in their study is by subtracting the activity from the previous tone. This necessarily means that in the omission activity analyzed, there's bottom-up sensory input activity. As performing another experiment with a control condition in which a sequence of randomly presented tones with different durations to compare directly the omission activity in both sequences (experimental and control) is possibly too demanding, I at least urge the authors to incorporate the fact that their omission responses do reflect also tone activity. And consider, for future experiments, the inclusion of further control conditions. 

Thanks for the opportunity to clarify this aspect. Actually, the way we computed the omission MMN is not by subtracting the activity of the previous tone from the omission, but by subtracting the activity of randomly selected tones across the whole experiment. That is, we randomly selected around 120 long and short tones (i.e., about the same number as the omissions); we computed the ERF for the long and short tones; we subtracted these ERF from the ERF of the corresponding short and long omissions. We clarified these aspects in both the Materials and Methods (ERF analysis paragraph) and Results section.

Moreover, the subtraction strategy - which is the standard approach to calculate the MMN - allows to handle possible neural carryover effects arising from the perception of the tone preceding the omission.

The sentence "Omission responses allow to examine the presence of putative error signals decoupled from bottom-up sensory input, offering a critical test for predictive coding (Walsh et al 2020, Heilbron and Chait, 2018)." simply refer to the fact that the error responses resulting from an omission are purely endogenous, as omissions are just absence of an expected input (i.e., silence). On the other hand, when a predicted sequence of tones is disrupted by an auditory deviants (e.g., a tone with a different pitch or duration than the expected one), the resulting error response is not purely endogenous, but it partially includes the response to the acoustic properties of the deviant.

(4) When multiple clusters emerged from a comparison, only the most significant cluster was reported. Why? 

We found more than one significant cluster only in the comparison between pure omissions vs tones (figure 2 A, B). The additional significant cluster from this comparison is associated with a P-value of 0.04, emerges slightly earlier in time, and goes in the same direction as the cluster reported in the paper i.e., larger ERF responses for omission vs tones. We added a note specifying the presence of this second cluster, along with a figure on the supplementary material (Supplementary Fig. 1 A, B).

(5) Fig 2, if ERFs are baseline corrected -50 to 0ms, why do the plots show pre-stimulus amplitudes not centered at 0? 

This is because we combined the latitudinal and longitudinal gradiometers on the ERF obtained after baseline correction, by computing the root mean square of the signals at each sensor position (see also  https://www.fieldtriptoolbox.org/example/combineplanar_pipelineorder/). This information is reported in the methods part of the article.

(6) Fig 2, add units to color bars. 

Sure.

(7) Fig 2 F and G, put colorbar scale the same for all topographies. 

Sure, thanks for pointing this out.

(8) The interaction effect language (Spanish; Basque) X omission type (short; long) appears only in a small cluster of 4 sensors not located at the locations with larger amplitudes to omissions. Authors report it as left frontotemporal, but it seems to me frontocentral with a slight left lateralization.

(1) the fact that the cluster reflecting the interaction effect does not overlap with the peaks of activity is not surprising in our view. Many sources contribute to the generation of the MMN. The goal of our work was to establish whether there is also evidence for a long-term system (among the many) contributing to this. That is why we perform a first analysis on the whole omission response network (likely including many sources and predictive/attentional systems), and then we zoom in and focus on our hypothesized interaction. We never claim that the main source underlying the omissionMMM is the long-term predictive system. 

(2) The exact location of those sensors is at the periphery of the left-hemisphere omission response, which mainly reflects activity from the left temporal regions. The sensor location of this cluster could be influenced by multiple factors, including (i) the direction of the source dipoles determining an effect; (ii) the combination of multiple sources contributing to the activity measured at a specific sensor location, whose unmixing could be solved only with a beamforming source approach. Based on the whole evidence we collected also in the source analyzes we concluded that the major contributors to the sensor-level interaction are emerging from both frontal and temporal regions.

Reviewer #3 (Public Review):

(1) The main weaknesses are the strength of the effects and generalisability. The sample size is also relatively small by today's standards, with N=20 in each group. Furthermore, the crucial effects are all mostly in the .01>P<.05 range, such as the crucial interaction P=.03. It would be nice to see it replicated in the future, with more participants and other languages. It would also have been nice to see behavioural data that could be correlated with neural data to better understand the real-world consequences of the effect.

We appreciate the positive feedback from Reviewer #3. We agree that it would be nice to see this study replicated in the future with larger sample sizes and a behavioral counterpart. Below are a few comments concerning the weakness highlighted: 

(i) Concerning the sample size: a similar point was raised by Reviewer #1. We report our reply as presented above: “Despite a sample size of 20 participants per group can be considered relatively small for detecting an effect in a between-group design, it must be noted that our effect of interest was based on Molnar et al.’s (2016) experiment, where a sample size of 16 subjects per group was sufficient to detect the perceptual grouping effect. In Yoshida et al., 2010, the perceptual grouping effect arose with two groups of 20 7–8-month-old Japanese and English-learning infants. Based on these findings, we believe that a sample size of 20 participants per group can be considered appropriate for the current study”. We clarified these aspects in the new version of the manuscript.

(ii) We believe that the lack of behavioral data does not undermine the main findings of this study, given the careful selection of the participants and the well-known robustness of the perceptual grouping effect (e.g., Iversen 2008; Yoshida et al., 2010; Molnar et al. 2014; Molnar et al. 2016). As highlighted by Reviewer #2, having Spanish and Basque dominant “speakers as a sample equates that in Molnar et al. (2016), and thus overcomes the lack of direct behavioral evidence for a difference in rhythmic grouping across linguistic groups. Molnar et al. (2016)'s evidence on the behavioral effect is compelling, and the evidence on neural signatures provided by the present study aligns with it”. (iii) Regarding the fact that the “crucial effects are all mostly in the .01>P<.05 range”: we want to stress that the approach we used to detect the interaction effect was conservative, using a cluster-based permutation approach with no a priori assumptions about the location of the effect. The robustness of our approach has also been highlighted by Reviewer 2: “Data analyses. Sound, state-of-the-art methodology in the event-related field analyses at the sensor level.” In sum, despite some crucial effects being in the .01>P<.05 range, we believe that the statistical soundness of our analysis, combined with the lack of effect in the control condition, provides compelling evidence for our H1.

Reviewer #3 (Recommendations For The Authors):

Figures - Recommend converting all diagrams and plots to vector images to ensure they remain clear when zoomed in the PDF format. 

Sure, thanks. 

Figure 1: To improve clarity, the representation of sound durations in panels C and D should be revisited. The use of quavers/eighth notes can be confusing for those familiar with musical notation, as they imply isochrony. If printed in black and white, colour distinctions may be lost, making it difficult to discern the different durations. A more universal representation, such as spectrograms, might be more effective. 

Thanks for the suggestion. It’s true that the quavers/eighth notes might be confusing in that respect. However, we find this notation as a relatively standard approach to define paradigms in auditory neuroscience, see for instance the two papers below. In the new version of the manuscript, we specified in the captions under the figure that the notes refer to individual tones, in order to avoid ambiguities.

- Wacongne, C., Labyt, E., Van Wassenhove, V., Bekinschtein, T., Naccache, L., & Dehaene, S. (2011). Evidence for a hierarchy of predictions and prediction errors in human cortex. Proceedings of the National Academy of Sciences, 108(51), 20754-20759.

- Dehaene, S., Meyniel, F., Wacongne, C., Wang, L., & Pallier, C. (2015). The neural representation of sequences: from transition probabilities to algebraic patterns and linguistic trees. Neuron, 88(1), 2-19.

Figure 2 : In panel C of Figure 2, please include the exact p-value for the interaction observed. Refrain from using asterisks or "n.s." and opt for exact p-values throughout for the sake of clarity. 

Thank you for your suggestion. We have included the exact p-value for the interaction in panel C of Figure 2. However, for the remaining figures, we have chosen to maintain the use of asterisks and "n.s.". We would like our pictures to convey the key findings concisely, while the numerical details can be found in the article text. The caption below the image also provides guidance on the interpretation of the p-values: (statistical significance: **p < 0.01, *p < 0.05, and ns p > 0.05).  

Figure 3 Note typo "Omission reponse"

Fixed. Thanks for noticing the typo. 

A note: we moved the figure reflecting the main effect of long tone omission and the lack of main effect of language background (Figure 4 in the previous manuscript) in the supplementary material (Supplementary Figure 2).

References

Bendixen, A., SanMiguel, I., & Schröger, E. (2012). Early electrophysiological indicators for predictive processing in audition: a review. International Journal of Psychophysiology, 83(2), 120-131.

Heilbron, M., & Chait, M. (2018). Great expectations: is there evidence for predictive coding in auditory cortex?. Neuroscience, 389, 54-73.

Iversen, J. R., Patel, A. D., & Ohgushi, K. (2008). Perception of rhythmic grouping depends on auditory experience. The Journal of the Acoustical Society of America, 124(4), 22632271.

Molnar, M., Lallier, M., & Carreiras, M. (2014). The amount of language exposure determines nonlinguistic tone grouping biases in infants from a bilingual environment. Language Learning, 64(s2), 45-64.

Molnar, M., Carreiras, M., & Gervain, J. (2016). Language dominance shapes non-linguistic rhythmic grouping in bilinguals. Cognition, 152, 150-159.

Ross, J. M., & Hamm, J. P. (2020). Cortical microcircuit mechanisms of mismatch negativity and its underlying subcomponents. Frontiers in Neural Circuits, 14, 13.

Simon, J., Balla, V., & Winkler, I. (2019). Temporal boundary of auditory event formation: An electrophysiological marker. International Journal of Psychophysiology, 140, 53-61.

Studenova, A. A., Forster, C., Engemann, D. A., Hensch, T., Sander, C., Mauche, N., ... & Nikulin, V. V. (2023). Event-related modulation of alpha rhythm explains the auditory P300 evoked response in EEG. bioRxiv, 2023-02.

Yoshida, K. A., Iversen, J. R., Patel, A. D., Mazuka, R., Nito, H., Gervain, J., & Werker, J. F. (2010). The development of perceptual grouping biases in infancy: A Japanese-English cross-linguistic study. Cognition, 115(2), 356-361.

Zhang, Y., Yan, F., Wang, L., Wang, Y., Wang, C., Wang, Q., & Huang, L. (2018). Cortical areas associated with mismatch negativity: A connectivity study using propofol anesthesia. Frontiers in Human Neuroscience, 12, 392.

Ladinig, O., Honing, H., Háden, G., & Winkler, I. (2009). Probing attentive and preattentive emergent meter in adult listeners without extensive music training. Music Perception, 26(4), 377-386. 

Brochard, R., Abecasis, D., Potter, D., Ragot, R., & Drake, C. (2003). The “ticktock” of our internal clock: Direct brain evidence of subjective accents in isochronous sequences. Psychological Science, 14(4), 362-366.

Potter, D. D., Fenwick, M., Abecasis, D., & Brochard, R. (2009). Perceiving rhythm where none exists: Event-related potential (ERP) correlates of subjective accenting. Cortex, 45(1), 103-109.

Bouwer, F. L., Werner, C. M., Knetemann, M., & Honing, H. (2016). Disentangling beat perception from sequential learning and examining the influence of attention and musical abilities on ERP responses to rhythm. Neuropsychologia, 85, 80-90.

Author response:

The following is the authors’ response to the original reviews

We thank the three reviewers for their insightful feedback. We look forward to addressing the raised concerns in a revised version of the manuscript. There were a few common themes among the reviews that we will briefly touch upon now, and we will provide more details in the revised manuscript. 

First, the reviewers asked for the reasoning behind the task ratios we implemented for the different attentional width conditions. The different ratios were selected to be as similar as possible given the size and spacing of our stimuli (aside from the narrowest cue width of one bin, the ratios for the others were 0.66, .6 and .66). As Figure 1b shows, while the ratios were similar, task difficulty is not constant across cue widths: spreading attention makes the task more difficult generally. But, while the modeled width of the spatial distribution of attention changes monotonically with cue width, task difficulty does not. Furthermore, prior work has indicated that there is a relationship between task difficulty and the overall magnitude of the BOLD response, however we don’t suspect that this will influence the width of the modulation. How task difficulty influences the BOLD response is an important topic, and we hope that future work will investigate this relationship more directly.   

Second, reviewers raised interest in the distribution of spatial attention in higher visual areas. In our study we focus only on early visual regions (V1-V3). This was primarily driven by pragmatic considerations, in that we only have retinotopic estimates for our participants in these early visual areas. Our modeling approach is dependent on having access to the population receptive field estimates for all voxels, and while the main experiment was scanned using whole brain coverage, retinotopy was measured in a separate session using a field of view only covering the occipital cortex.  

Lastly, we appreciate the opportunity to clarify the purpose of the temporal interval analysis. The reviewer is correct in assuming we set out to test how much data is needed to recover the cortical modulation and how dynamic a signal the method can capture. This analysis does show that more data provides more reliable estimates, though the model was still able to recover the location and width of the attentional cue at shorter timescales of as few as two TRs. This has implications for future studies that may involve more dynamic tracking of the attentional field.

Public Reviews

Reviewer #1 (Public review): 

The authors conducted an fMRI study to investigate the neural effects of sustaining attention to areas of different sizes. Participants were instructed to attend to alphanumeric characters arranged in a circular array. The size of attention field was manipulated in four levels, ranging from small (18 deg) to large (162 deg). They used a model-based method to visualize attentional modulation in early visual cortex V1 to V3, and found spatially congruent modulations of the BOLD response, i.e., as the attended area increased in size, the neural modulation also increased in size in the visual cortex. They suggest that this result is a neural manifestation of the zoomlens model of attention and that the model-based method can effectively reconstruct the neural modulation in the cortical space. 

The study is well-designed with sophisticated and comprehensive data analysis. The results are robust and show strong support for a well-known model of spatial attention, the zoom-lens model. Overall, I find the results interesting and useful for the field of visual attention research. I have questions about some aspects of the results and analysis as well as the bigger picture. 

(1) It appears that the modulation in V1 is weaker than V2 and V3 (Fig 2). In particular, the width modulation in V1 is not statistically significant (Fig 5). This result seems a bit unexpected. Given the known RF properties of neurons in these areas, in particular, smaller RF in V1, one might expect more spatially sensitive modulation in V1 than V2/V3. Some explanations and discussions would be helpful. Relatedly, one would also naturally wonder if this method can be applied to other extrastriate visual areas such as V4 and what the results look like. 

We agree with the reviewer. It’s very interesting how the spatial resolution within different visual regions contributes to the overall modulation of the attentional field, and how this in turn would influence perception. Our data showed that fits in V1 appeared to be less precise than in V2 and V3. This can be seen in the goodness of fit of the model as well as the gain and absolute angular error estimates. The goodness of fit and gain were lowest in V1 and the absolute angular error was largest in V1 (see Figure 5). We speculate that the finer spatial granularity of V1 RFs was countered by a lower amplitude and SNR of attention-related modulation in V1, resulting in overall lower sensitivity to variation in attentional field width. Prior findings concur that the magnitude of covert spatial attention increases when moving from striate to extrastriate cortex (Bressler & Silver (2010); Buracas & Boynton (2007)). Notably, in our perception condition, V1 showed more spatially sensitive modulation (see Figure 7), consistent with the known RF properties of V1 neurons.

Regarding the second point: unfortunately, our dataset did not allow us to explore higherorder cortical regions with the model-based approach. While the main experiment was scanned using a sequence with whole brain coverage, the pRF estimates came from a separate scanning session which only had limited occipital coverage. Our modeling approach is dependent on the polar angle estimates from this pRF session. We now explicitly state this limitation in the methods (lines 87-89):

“In this session, the field of view was restricted to the occipital cortex to maximize SNR, thereby limiting the brain regions for which we had pRF estimates to V1, V2, and V3.”

(2) I'm a bit confused about the angular error result. Fig 4 shows that the mean angular error is close to zero, but Fig 5 reports these values to be about 30-40 deg. Why the big discrepancy? Is it due to the latter reporting absolute errors? It seems reporting the overall bias is more useful than absolute value. 

The reviewer’s inference here is exactly right: Figure 4 shows signed error, whereas Figure 5 shows absolute error. We show the signed error for the example participant because, (1) by presenting the full distribution of model estimates for one participant, readers have access to a more direct representation of the data, and (2) at the individual level it is possible to examine potential directional biases in the location estimates (which do not appear to be present). As we don’t suspect a consistent directional bias across the group, we believe the absolute error in location estimates is more informative in depicting the precision in location estimates using the model-based approach. In the revised manuscript, we modified Figure 5 to make the example participant’s data visually distinct for easy comparison. We have clarified this reasoning in the text (results lines 59-64):

“The angular error distribution across blocks, separated by width condition, is shown in Figure 4 for one example participant to display block-to-block variation. The model reliably captured the location of the attentional field with low angular error and with no systematic directional bias. This result was observed across participants. We next examined the absolute angular error to assess the overall accuracy of our estimates.”

(3) A significant effect is reported for amplitude in V3 (line 78), but the graph in Fig 5 shows hardly any difference. Please confirm the finding and also explain the directionality of the effect if there is indeed one. 

We realize that the y-axis scale of Figure 5 was making it difficult to see that gain decreases with cue width in area V3. Instead of keeping the y-axis limits the same across visual regions, we now adapt the y-axis scale of each subplot to the range of data values:  

We now also add the direction of the effect in the text (results lines 83-86):

“We observed no significant relationship between gain and cue width in V1 and V2 (V1 t(7)=.54, p=.605; V2 t(7)=-2.19, p=.065), though we did find a significant effect in V3 illustrating that gain decreases with cue width (t(7)=-3.12, p=.017).”

(4) The purpose of the temporal interval analysis is rather unclear. I assume it has to do with how much data is needed to recover the cortical modulation and hence how dynamic a signal the method can capture. While the results make sense (i.e., more data is better), there is no obvious conclusion and/or interpretation of its meaning. 

We apologize for not making our reasoning clear. We now emphasize our reasoning in the revised manuscript (results lines 110-112). Our objective was to quantify how much data was needed to recover the dynamic signal. As expected, we found that including more data reduces noise (averaging helps), but importantly, we found that we still obtained meaningful model fits even with limited data. We believe this has important implications for future paradigms that explore more dynamic deployment of spatial attention, where one would not want to average over multiple repetitions of a condition.

The first paragraph of the Temporal Interval Analysis section in the results now reads: 

“In the previous analyses, we leveraged the fact that the attentional cue remained constant for 5-trial blocks (spatial profiles were computed by averaging BOLD measurements across a block of 10 TRs). We next examined the degree to which we were able to recover the attentional field on a moment-by-moment (TR-by-TR) basis. To do this, we systematically adjusted the number of TRs that contributed to the averaged spatial response profile. To maintain a constant number of observations across the temporal interval conditions, we randomly sampled a subset of TRs from each block. This allowed us to determine the amount of data needed to recover the attentional field, with a goal of examining the usability of our modeling approach in future paradigms involving more dynamic deployment of spatial attention.”

(5) I think it would be useful for the authors to make a more explicit connection to previous studies in this literature. In particular, two studies seem particularly relevant. First, how do the present results relate to those in Muller et al (2003, reference 37), which also found a zoom-lens type of neural effects. Second, how does the present method compare with spatial encoding model in Sprague & Serences (2013, reference 56), which also reconstructs the neural modulation of spatial attention. More discussions of these studies will help put the current study in the larger context.

We now make a more explicit connection to prior work in the discussion section (lines 34-54). 

“We introduced a novel modeling approach that recovered the location and the size of the attentional field. Our data show that the estimated spatial spread of attentional modulation (as indicated by the recovered FWHM) consistently broadened with the cue width, replicating prior work (Müller et al., 2003; Herrmann et al., 2010). Our results go beyond prior work by linking the spatial profiles to pRF estimates, allowing us to quantify the spread of both attentional and perceptual modulation in degrees of polar angle. Interestingly, the FWHM estimates for the attentional and perceptual spatial profiles were highly similar. Additionally, for area V3 we replicate that the population response magnitude decreased with cue width (Müller et al., 2003; Feldmann-Wüstefeld and Awh, 2020). One innovation of our method is that it directly reconstructs attention-driven modulations of responses in visual cortex, setting it apart from other methods, such as inverted encoding models (e.g. Sprague & Serences, 2013). Finally, we demonstrated that our method has potential to be used in more dynamic settings, in which changes in the attentional field need to be tracked on a shorter timescale.”

(6) Fig 4b, referenced on line 123, does not exist. 

We have corrected the text to reference the appropriate figure (Figure 5, results line 136).

Reviewer #2 (Public review):

Summary: 

The study in question utilizes functional magnetic resonance imaging (fMRI) to dynamically estimate the locus and extent of covert spatial attention from visuocortical activity. The authors aim to address an important gap in our understanding of how the size of the attentional field is represented within the visual cortex. They present a novel paradigm that allows for the estimation of the spatial tuning of the attentional field and demonstrate the ability to reliably recover both the location and width of the attentional field based on BOLD responses. 

Strengths: 

(1) Innovative Paradigm: The development of a new approach to estimate the spatial tuning of the attentional field is a significant strength of this study. It provides a fresh perspective on how spatial attention modulates visual perception. 

(2) Refined fMRI Analysis: The use of fMRI to track the spatial tuning of the attentional field across different visual regions is methodologically rigorous and provides valuable insights into the neural mechanisms underlying attentional modulation. 

(3) Clear Presentation: The manuscript is well-organized, and the results are presented clearly, which aids in the reader's comprehension of the complex data and analyses involved. 

We thank the reviewer for summarizing the strengths in our work. 

Weaknesses: 

(1) Lack of Neutral Cue Condition: The study does not include a neutral cue condition where the cue width spans 360°, which could serve as a valuable baseline for assessing the BOLD response enhancements and diminishments in both attended and non-attended areas. 

We do not think that the lack of a neutral cue condition substantially limits our ability to address the core questions of interest in the present work. We set out to estimate the locus and the spread of covert spatial attention. By definition, a neutral cue does not have a focus of attention as the whole annulus becomes task relevant. We agree with the reviewer that how spatial attention influences the magnitude of the BOLD response is still not well defined; i.e., does attending a location multiplicatively enhance responses at an attended location or does it instead act to suppress responses outside the focus of attention? A neutral cue condition would be necessary to be able to explore these types of questions. However, our findings don’t rest on any assumptions about this. Instead, we quantify the attentional modulation with a model-based approach and show that we can reliably recover its locus, and reveal a broadening in the attentional modulation with wider cues. 

We realize that throughout the original manuscript we often used the term ‘attentional enhancement,’ which might inadvertently specify an increase with respect to a neutral condition. To be more agnostic to the directionality of the effect, we have changed this to ‘attentional modulation’ and ‘attentional gain’ throughout the manuscript. Additionally, we have added results and visualizations for the baseline parameter to all results figures (Figures 4-7) to help readers further interpret our findings.  

(2) Clarity on Task Difficulty Ratios: The explicit reasoning for the chosen letter-to-number ratios for various cue widths is not detailed. Ensuring clarity on these ratios is crucial, as it affects the task difficulty and the comparability of behavioral performance across different cue widths. It is essential that observed differences in behavior and BOLD signals are attributable solely to changes in cue width and not confounded by variations in task difficulty.  

The ratios were selected to be as similar as possible given the size and spacing of our stimuli (aside from the narrowest cue width of one bin, the proportions for the others were 0.67, 0.60, and 0.67). We have updated the methods section to state this explicitly (methods lines 36-38): 

“The ratios were selected to be as similar as possible given the size and spacing of our stimuli (aside from the one-bin cue, the proportions for the other cues were 0.67, 0.60, 0.67).”

As Figure 1b shows, task accuracy showed small and non-monotonic changes across the three larger cue widths, dissociable from the monotonic pattern seen for the modelestimated width of the attentional field. Furthermore, as prior work has indicated that there is a relationship between task difficulty and the overall magnitude of the BOLD response (e.g., Ress, Backus & Heeger, 2000), we would primarily expect effects of task difficulty on the gain or baseline rather than the width. How exactly task difficulty influences the BOLD response and whether this would, in fact, interact with the width of the attentional field is an important topic, and we hope that future work will investigate this relationship more directly.  

We have clarified these points within the text, and now explicitly motivate future work looking at these important interactions (discussion lines 57-67):

“The observed effects of attentional field width were unlikely to be directly attributable to variation in task difficulty. Participants' task in our study was to discriminate whether more numbers or more letters were presented within a cued region of an iso-eccentric annulus of white noise. For our different cue widths, the ratios of numbers and letters were selected to be as similar as possible given the size and spacing of our stimuli. Changes in accuracy across the three larger cue widths were small and non-monotonic, implying task difficulty was dissociable from width per se. This dissociation bolsters the interpretability of our model fits; nevertheless, future work should further investigate how task difficulty interacts with the spread of the attentional field and the amplitude of attention-related BOLD effects (cf. Ress, Backus & Heeger, 2000).”

Reviewer #3 (Public review):

Summary: 

In this report, the authors tested how manipulating the contiguous set of stimuli on the screen that should be used to guide behavior - that is, the scope of visual spatial attention - impacts the magnitude and profile of well-established attentional enhancements in visual retinotopic cortex. During fMRI scanning, participants attended to a cued section of the screen for blocks of trials and performed a letter vs digit discrimination task at each attended location (and judged whether the majority of characters were letters/digits). Importantly, the visual stimulus was identical across attention conditions, so any observed response modulations are due to topdown task demands rather than visual input. The authors employ population receptive field (pRF) models, which are used to sort voxel activation with respect to the location and scope of spatial attention and fit a Gaussian-like function to the profile of attentional enhancement from each region and condition. The authors find that attending to a broader region of space expands the profile of attentional enhancement across the cortex (with a larger effect in higher visual areas), but does not strongly impact the magnitude of this enhancement, such that each attended stimulus is enhanced to a similar degree. Interestingly, these modulations, overall, mimic changes in response properties caused by changes to the stimulus itself (increase in contrast matching the attended location in the primary experiment). The finding that attentional enhancement primarily broadens, but does not substantially weaken in most regions, is an important addition to our understanding of the impact of distributed attention on neural responses, and will provide meaningful constraints to neural models of attentional enhancement. 

Strengths: 

(1) Well-designed manipulations (changing location and scope of spatial attention), and careful retinotopic/pRF mapping, allow for a robust assay of the spatial profile of attentional enhancement, which has not been carefully measured in previous studies.

(2) Results are overall clear, especially concerning width of the spatial region of attentional enhancement, and lack of clear and consistent evidence for reduction in the amplitude of enhancement profile.

(3) Model-fitting to characterize spatial scope of enhancement improves interpretability of findings.

We thank the reviewer for highlighting the strengths of our study. 

Weaknesses: 

(1) Task difficulty seems to vary as a function of spatial scope of attention, with varying ratios of letters/digits across spatial scope conditions, which may complicate interpretations of neural modulation results  

The reviewer is correct in observing that task accuracy varied across cue widths. Though we selected the task ratios to be as similar as possible given the size and spacing of our stimuli (aside from the narrowest cue width of one bin, the proportions for the others were 0.67, 0.60, and 0.67), behavioral accuracy across the three larger cue widths was not identical. Prior research has shown that there is a relationship between task difficulty and the overall magnitude of the BOLD response (e.g., Ress, Backus & Heeger, 2000). Thus, we would primarily expect effects of task difficulty on gain rather than width. How task difficulty influences the BOLD response and whether this would, in fact, interact with the width of the attentional field is an important topic, and we hope that future work will investigate this relationship more directly.  

To clarify these points and highlight the potential for future work looking at these important interactions, we added the following text to the discussion section (discussion lines 57-67):

“The observed effects of attentional field width were unlikely to be directly attributable to variation in task difficulty. Participants' task in our study was to discriminate whether more numbers or more letters were presented within a cued region of an iso-eccentric annulus of white noise. For our different cue widths, the ratios of numbers and letters were selected to be as similar as possible given the size and spacing of our stimuli. Changes in accuracy across the three larger cue widths were small and non-monotonic, implying task difficulty was dissociable from width per se. This dissociation bolsters the interpretability of our model fits; nevertheless, future work should further investigate how task difficulty interacts with the spread of the attentional field and the amplitude of attention-related BOLD effects (cf. Ress, Backus and Heeger, 2000).”

(2) Some aspects of analysis/data sorting are unclear (e.g., how are voxels selected for analyses?) 

We apologize for not describing our voxel selection in sufficient detail. Some of the questions raised in the private comments are closely related to this point, we therefore aim to clarify all concerns below:

- Voxel selection: To select voxels that contribute to the 1D spatial profiles, we relied on the independent pRF dataset. We first defined some general requirements that needed to be met. Specifically, 1) the goodness of fit (R²) of the pRF fits needed to be greater than 10%; 2) the estimated eccentricity had to fall within [0.7 9.1] degree eccentricity (to exclude voxels in the fovea and voxels with estimated eccentricities larger than the pRF mapping stimulus); 3) the estimated size must be greater than 0.01 degree visual angle. 

Next, we included only voxels whose pRF overlapped with the white noise annulus. Estimated eccentricity was used to select all voxels whose eccentricity estimate fell within the annulus bounds. However, here it is also important to take the size of the pRF into account. Some voxels’ estimated eccentricity might fall just outside the annulus, but will still have substantial overlap due to the size of their pRF. Therefore, we further included all voxels whose estimated pRF size resulted in overlap with the annulus. 

This implies that some voxels with greater eccentricities and larger pRF sizes contribute to the 1D profile, which will influence the spatial specificity of the 1D profiles. However, we want to emphasize that in our view, the exact FWHM value is not so much of interest, as this will always be dependent on the voxel selection and many other data processing steps. Instead, we focus on the relative differences of the FWHM driven by the parametric attentional cue width manipulation. 

- Data sorting and binning. The reviewer raises an important point about how the FWHM value should be interpreted considering the data processing steps. To generate the 1D spatial profile, we binned voxels based on their estimated polar angle preference into 6degree bins and applied a moving average of 18 degrees to smooth the 1D profiles. Both of these processing steps will influence the spatial specificity of the profile. The binning step facilitates recentering based on cue center and combining across trials.

To explore the extent to which the moving average substantially impacted our results, we reran our analyses without that smoothing step. The vast majority of the results held. In V1, we found a significant effect of cue width on FWHM where the result was not significant previously (t(7)=2.52, p\=.040). Additionally, when looking at the minimum number of TRs needed to see a significant effect of cue width on FWHM, without the smoothing step in V1 it took 10 TRs (not significant at 10 TRs previously), in V2 it took 5 TRs (10 previously), and in V3 it took 3 TRs (2 previously). The other notable difference is that FWHM was generally a bit larger when the moving average smoothing was performed. We have visualized the group results for the FWHM estimates below to help with comparison. 

Author response image 1.

No moving average smoothing:

Voxel selection methods have been clarified in methods section lines 132-139:

“Within each ROI, pRF modeling results were used to constrain voxel selection used in the main experiment. We excluded voxels with a preferred eccentricity outside the bounds of the pRF stimulus (<0.7° and >9.1°), with a pRF size smaller than 0.01°, or with poor spatial selectivity as indicated by the pRF model fit (R2 < 10%). Following our 2D visualizations (see below), we further constrained voxel selection by only including voxels whose pRF overlapped with the white noise annulus. We included all voxels with an estimated eccentricity within the annulus bounds, as well as voxels with an estimated pRF size that would overlap the annulus.”

Data binning methods have been clarified in methods section lines 154-159: 

“Voxels with pRFs overlapping the white noise annulus were grouped into 60 bins according to their pRF polar angle estimate (6° polar angle bin width). We computed a median BOLD response within each bin. This facilitated the recentering of each profile to align all cue centers for subsequent combining across trials. To improve the signal-to-noise ratio, the resulting profile was smoothed with a moving average filter (width 18° polar angle; see Figure 2b).”

(3) While the focus of this report is on modulations of visual cortex responses due to attention, the lack of inclusion of results from other retinotopic areas (e.g. V3AB, hV4, IPS regions like IPS0/1) is a weakness 

We agree with the reviewer that using this approach in other retinotopic areas would be of significant interest. In this case, population receptive field mapping occurred in a separate session with a field of view only covering the occipital cortex (in contrast to the experimental session, which had whole-brain coverage). Because our modeling approach relies on these pRF estimates, we were unable to explore higher visual areas. However, we hope future work will follow up on this.

We have added the following text to the methods section describing the pRF mapping session (lines 87-89):

“In this session, the field of view was restricted to the occipital cortex to maximize SNR, thereby limiting the brain regions for which we had pRF estimates to V1, V2, and V3.”

(4) Additional analyses comparing model fits across amounts of data analyzed suggest the model fitting procedure is biased, with some parameters (e.g., FWHM, error, gain) scaling with noise. 

In this analysis, we sought to test how much data was needed to recover the attentional field, in view of the need for additional fMRI-based tools for use in tasks that involve more rapid dynamic adaptation of attention. Though we did find that more data reduced noise (and accordingly decreased absolute error and amplitude while increasing FWHM and R²), absolute angular error remained low across different temporal intervals (well below the chance level of 90°). With regard to FWHM, we believe that the more important finding is that the model-estimated FWHM was modulated by cue width at shorter timescales of as few as two TRs while maintaining relatively low angular error. We refrain from drawing conclusions here on the basis of the exact FWHM values, both because we don’t have a ground truth for the attentional field and because various processing pipeline steps can impact the values as well. Rather, we are looking at relative value and overall patterns in the estimates. The observed patterns imply that the model recovers meaningful modulation of the attentional field even at shorter time scales.

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

Additional data reporting and discussion of results are needed as outlined in the public review. 

Reviewer #2 (Recommendations for the authors):

(1) The current experimental design effectively captured the impact of varying cue widths on the BOLD response in the visual cortex. However, the inclusion of a neutral cue condition, where the cue width spans 360{degree sign} and all peripheral stimuli are attended, could serve as a valuable baseline. This would enable a quantitative assessment of how much the BOLD response is enhanced in specific spatial regions due to focused cues and, conversely, how much it is diminished in non-attended areas, along with the spatial extent of these effects. 

Please refer to our response in the public review. 

(2) While the study provides valuable insights into BOLD signal changes in visual areas corresponding to the focus of attention, it does not extend its analysis to the impact on regions outside the focus of attention. It would be beneficial to explore whether there is a corresponding decrease in BOLD signal in non-attended regions, and if identified, to describe the spatial extent and position of this effect relative to the attended area. Such an analysis could yield deeper insights into how attention influences activity across the visual cortex. 

We agree with the reviewer that it is very interesting to examine the spread of attention across the whole visual field. Our experiment was designed to focus on width modulations at a fixed eccentricity, but future work should explore how the attentional field changes with eccentricity and interacts with spatial variations across the visual field. This is highlighted in our discussion section (lines 76-81): 

“Future work can help provide a better understanding of the contribution of spatial attention by considering how the attentional field interacts with these well described spatial variations across the visual field. Measuring the full spatial distribution of the attentional field (across both eccentricity and polar angle) will shed light on how spatial attention guides perception by interacting with the non-uniformity of spatial representations.”

The addition of figure panels for the estimated baseline parameter in Figures 4-7 provides further information about BOLD effects in unattended regions of the annulus.  

(3) The rationale behind the selection of task difficulty ratios for different cue widths, specifically the letter-to-number ratios of 1:0, 1:2, 2:3, and 3:6 (or vice versa) for cue widths of 18{degree sign}, 54{degree sign}, 90{degree sign}, and 162{degree sign} respectively, was not explicitly discussed. It would be beneficial to clarify the basis for these ratios, as they may influence the perceived difficulty of the task and thus the comparability of behavioral performance across different cue widths. Ensuring that the task difficulty is consistent across conditions is crucial for attributing differences in behavior and BOLD signals solely to changes in cue width and not confounded by variations in task difficulty. 

Please refer to our response in the public review. We now clarify why we selected these ratios, and acknowledge more explicitly that behavioral performance differed across width conditions. See also our reply to private comment 1 from Reviewer 3 for some additional analyses examining task related influences.

Reviewer #3 (Recommendations for the authors):

(1) Task difficulty: the task seems exceptionally challenging. Stimuli are presented at a relativelyeccentric position for a very brief duration, and a large number of comparisons must be made across a broad region of space. This is reflected in the behavioral performance, which decreases rapidly as the scope of attention increases (Fig. 1). Because trials are blocked, does this change in task difficulty across conditions impact the degree to which neural responses are modulated? How should we consider differences in task difficulty in interpreting the conclusions (especially with respect to the amplitude parameter)? Also, note that the difficulty scales both with number of stimuli - as more need to be compared - but also with the ratio, which differs nonmonotonically across task conditions. One way to dissociate these might be RT: for 54/162, which both employ the same ratio of letter/digits and have similar accuracy, is RT longer for 162, which requires attending more stimuli? 

In addition to our comments in response to the public review, we emphasize that the reviewer makes an important point that there are differences in task difficulty, though the ratios are as close as they can be given the size and spacing of our stimuli. Behavioral performance varied non-monotonically with cue width, bolstering our confidence that our monotonically increasing model-estimated width is likely not entirely driven by task difficulty. There nevertheless remain open questions related to how task difficulty does impact BOLD attentional modulation, which we hope future work will more directly investigate.

The reviewer's comments identify two ways our data might preliminarily speak to questions about BOLD attentional modulation and task difficulty. First: how might the amplitude parameter reflect task difficulty? This is an apt question as we agree with the reviewer that it would be a likely candidate in which to observe effects of task difficulty. We do find a small effect of cue width on our amplitude estimates (amplitude decreases with width) in V3. Using the same analysis technique to look at the relationship between task difficulty and amplitude, we find no clear relationship in any of the visual areas (all p >= 0.165, testing whether the slopes differed from zero at the group level using a one-sample t-test). We believe future work using other experimental manipulations should look more systematically at the relationship between task difficulty and amplitude of the attentional BOLD enhancement.

Second: Does the same ratio at different widths elicit different behavioral responses (namely accuracy and RT)? We followed the reviewer’s suggestion to compare performance between cue widths of three and nine (identical ratios, different widths; see Author response image 2 and Figure 5). We found that, using a paired t-test, behavioral accuracy differed between the two cue widths (mean accuracy of 0.73 versus 0.69, p = 0.008), with better performance for cue width three. RT did not differ significantly between the two conditions (paired t-test, p = 0.729). This could be due to the fact that participants were not incentivized to respond as quickly as possible, they merely needed to respond before the end of the response window (1.25 s) following the stimulus presentation (0.5 s). The comparisons for accuracy and RT (calculated from time of stimulus appearance) are plotted below:

Author response image 2.

In summary, with matched stimulus ratios, the wider cue was associated with worse (though not slower) performance. This could be due to the fact that more elements are involved and/or that tasks become more difficult when attending to a broader swath of space. Given these results, we believe that future studies targeting difficulty effects should use direct and independent manipulations of task difficulty and attentional width. 

(2) Eye movements: while the authors do a good job addressing the average eccentricity of fixation, I'm not sure this fully addresses concerns with eye movements, especially for the character-discrimination task which surely benefits from foveation (and requires a great deal of control to minimize saccades!). Can the authors additionally provide data on, e.g., # of fixations within the attended stimulus annulus, or fixation heatmap, or # of saccades, or some other indicator of likelihood of fixating the letter stimuli for each condition? 

We agree with the reviewer that this task is surely much easier if one foveated the stimuli, and it did indeed require control to minimize saccades to the annulus. (We appreciate the effort and motivation of our participants!) We are happy to provide additional data to address these reasonable concerns about eye movements. Below, we have visualized the number of fixations to the annulus, separated by participant and width. Though there is variability across participants, there are at most 16 instances of fixations to the annulus for a given participant, combined across all width conditions. The median number of fixations to the annulus per width is zero (shown in red). Considering the amount of time participants engaged in the task (between 8 and 12 runs of the task, each run with 100 trials), this indicates participants were generally successful at maintaining central fixation while the stimuli were presented.

Author response image 3.

We added the results of this analysis to the methods section (lines 205-208):

“Additionally, we examined the number of fixations to the white noise annulus itself. No participant had more than 16 fixations (out of 800-1200 trials) to the annulus during the task, further suggesting that participants successfully maintained fixation.”

(3) pRF sorting and smoothing: Throughout, the authors are analyzing data binned based on pRF properties with respect to the attended location ("voxels with pRFs overlapping with the white noise annulus", line 243-244) First, what does this mean? Does the pRF center need to be within the annulus? Or is there a threshold based on the pRF size? If so, how is this implemented? Additionally, considering the methods text in lines 242-247, the authors mention that they bin across 6 deg-wide bins and smooth with a moving average (18 deg), which I think will lead to further expansion of the profile of attentional enhancement (see also below) 

We provide a detailed response in the public review. Furthermore, we have clarified the voxel selection procedure in the Methods (lines 132–139 & 154–159).

(4) FWHM values: The authors interpret the larger FWHMs estimated from their model-fitting than the actual size of the attended region as a meaningful result. However, depending on details of the sorting procedure above, this may just be due to the data processing itself. One way to identify how much expansion of FWHM occurs due to analysis is by simulating data given estimates of pRF properties for a 'known' shape of modulation (e.g., square wave exactly spanning the attended aperture) and compare the resulting FWHM to that observed for attention and perception conditions (e.g., Fig. 7c). 

We provide a detailed response in the public review. The essence of our response is to refrain from interpreting the precise recovered FWHM values, which will be influenced by multiple processing steps, and instead to focus on relative differences as a function of the attentional cue width. Accordingly, we did not add simulations to the revised manuscript, although we agree with the reviewer that such simulations could shed light on the underlying spatial resolution, and how binning and smoothing influences the estimated FWHM. We have clarified our interpretation of FWHM results in the manuscript as follows:

Results lines 137-141:

“One possibility is that the BOLD-derived FWHM might tend to overestimate the retinotopic extent of the modulation, perhaps driven by binning and smoothing processing steps to create the 1D spatial profiles. If this were the case, we would expect to obtain similar FWHM estimates when modeling the perceptual modulations as well.”

Results lines 169-175:

“Mirroring the results from the attentional manipulation, FWHM estimates systematically exceeded the nominal size of the perceptually modulated region of the visual field. Comparing the estimated FWHMs of the perceptual and attentional spatial profiles (Figure 7c) revealed that the estimated widths were highly comparable (Pearson correlation r=0.664 across width conditions and visual regions). Importantly, the relative differences in FWHM show meaningful effects of both cue and contrast width in a similar manner for both attentional and perceptual forms of modulation.”

Discussion lines 16-22:

“We also found that the estimated spatial spread of the attentional modulation (as indicated by the recovered FWHM) was consistently wider than the cued region itself. We therefore compared the spread of the attention field with the spatial profile of a perceptually induced width manipulation. The results were comparable in both the attentional and perceptual versions of the task, suggesting that cueing attention to a region results in a similar 1D spatial profile to when the stimulus contrast is simply increased in that region.”

(5) Baseline parameter: looking at the 'raw' response profiles shown in Fig. 2b, it looks, at first, like the wider attentional window shows substantially lower enhancement. However, this seems to be mitigated by the shift of the curve downwards. Can the authors analyze the baseline parameter in a similar manner as their amplitude analyses throughout? This is especially interesting in contrast to the perception results (Fig. 7), for which the baseline does not seem to scale in a similar way. 

We agree with the reviewer that the baseline parameter is worth examining, and have therefore added panels displaying the baseline parameter into all results figures (Figures 4-7). There was no significant association between cue width and baseline offset in any of the three visual regions.

(6) Outlier: Fig. 5, V2, Amplitude result seems to have a substantial outlier - is there any notable difference in e.g. retinotopy in this participant? 

One participant indeed has a notably larger median amplitude estimate in V2. Below, we plot the spatial coverage from the pRF data for this participant (022), as well as all other participants.

Author response image 4.

Each subplot represents a participant's 2D histogram of included voxels for the 1D spatial profiles; the colors indicate the proportion of voxels that fell within a specific x,y coordinate bin. Note that this visualization only shows x and y estimates and does not take into account size of the pRF. While there is variation across participants in the visual field coverage, the overall similarity of the maps indicates that retinotopy is unlikely to be the explanation. 

To further explore whether this participant might be an outlier, we additionally looked at behavioral performance, angular error and FWHM parameters as well as the goodness of fit of the model. On all these criteria this participant did not appear to be an outlier. We therefore see no reason to exclude this participant from the analyses.  

(7) Fig. 4 vs Fig. 5: I understand that Fig. 4 shows results from a single participant, showing variability across blocks, while Fig. 5 shows aggregate results across participants. However, the Angular Error figure shows complementary results - Fig. 4 shows the variability of best-fit angular error, while Fig. 5 shows the average deviation (approximately the width of the error distribution). This makes sense I think, but perhaps the abs(error) for the single participant shown in Fig. 4 should be included in the caption so we can easily compare between figures. 

That's right: the Figure 4 results show the signed error, whereas the Figure 5 results show the absolute error. We agree that reporting the absolute error values for the example participant would facilitate comparison. Rather than add the values to the text, we have made the example participant’s data visually distinct within Figure 5 for easy comparison.  

(8) Bias in model fits: the analysis shown in Fig. 6 compares the estimated parameters across amounts of data used to compute attentional modulation profiles for fitting those parameters. If the model-fitting procedure were unbiased, my sense is we would likely see no impact of the number of TRs on the parameters (R^2 should improve, abs(error) should improve, but FWHM, amplitude, baseline, etc should be approximately stable, if noisier). However, instead, it looks like more/less data leads to biased estimates, such that FWHM is biased to be smaller with more noise, and amplitude is biased to be larger. This suggests (to me) that the fit is landing on a spiky function that captures a noise wiggle in the profile. I don't think this is a problem for the primary results across the whole block of 10 TRs, which is the main point of the paper. Indeed, I'm not sure what this figure is really adding, since the single-TR result isn't pursued further (see below). 

Please refer to our response in the public review, comment 4. 

(9) 'Dynamics': The paper, starting in the title, claims to get at the 'dynamics' of attention fields. At least to me, that word implies something that changes over time (rather than across trials). Maybe I'm misinterpreting the intent of the authors, but at present, I'm not sure the use of the word is justified. That said, if the authors could analyze the temporal evolution of the attention field through each block of trials at 1- or 2-TR resolution, I think that could be a neat addition to the paper and would support the claim that the study assays dynamic attention fields. 

We thank the reviewer for giving us a chance to speak more directly to the dynamic aspect of our approach. Here, we specifically use the word “dynamic” to refer to trial-to-trial dynamics.  Importantly, our temporal interval analysis suggests that we can recover information about the attentional field at a relatively fine-grained temporal resolution (a few seconds, or 2 TRs). Following this methodological proof-of-concept to dynamically track the attentional field, we are excited about future work that can more directly investigate the manner in which the attentional field evolves through time, especially in comparison to other methods that first require training on large amounts of data.

(10) Correction for multiple comparisons across ROIs: it seems that it may be necessary to correct statistical tests for multiple comparisons across each ROI (e.g., Fig. 5 regression tests). If this isn't necessary, the authors should include some justification. I'm not sure this changes any conclusions, but is worth considering. 

We appreciate the opportunity to explain our reasoning regarding multiple comparisons. We thought it appropriate not to correct as we are not comparing across regions and are not treating tests of V1, V2, and V3 as multiple opportunities to support a common hypothesis. Rather, the presence or absence of an effect in each visual region is a separate question. We would typically perform correction for multiple comparisons to control the familywise error rate when conducting a family of tests addressing a common hypothesis. We have added this to the Methods section (lines 192-195): 

“No multiple comparison correction was applied, as the different tests for each region are treated as separate questions. However, using a threshold of 0.017 for p-values would correct for comparisons across the three brain regions.”

However, we are happy to provide corrected results. If we use Bonferroni correction across ROIs (i.e. multiply p-values by three), there are some small changes from significant to only trending towards significance, but these changes don’t affect any core results. The changes that go from significant to trending are:

Associated with Figure 5 – In V3, the relationship of cue width to amplitude goes from a p-value of 0.017 to 0.051.

Associated with Figure 6 –

V1: the effect of cue width on FWHM goes from p = 0.043 to 0.128.

V2: the effect of TR on both FWHM and R2 goes from p = ~0.02 to ~0.06. 

V3: the effect of cue width on amplitude goes from p = 0.024 to 0.073.

Author Response

The following is the authors’ response to the original reviews.

We thank the reviewers and the editors for their careful reading of our manuscript and for the detailed and constructive feedback on our work. Please find attached the revised version of the manuscript. We performed an extensive revision of the manuscript to address the issues raised by the referees. We provide new analyses (regarding the response consistency and the neural complexity), added supplementary figures and edits to figures and texts. Based on the reviewers’ comments, we introduced several major changes to the manuscript.

Most notably, we

• added a limitation statement to emphasize the speculative nature of our interpretation of the timing of word processing/associative binding

• emphasized the limitations of the control condition

• added analyses on the interaction between memory retrieval after 12h versus 36h

• clarified our definition of episodic memory

• added detailed analyses of the “Feeling of having heard” responses and the confidence ratings

We hope that the revised manuscript addresses the reviewers' comments to their satisfaction. We believe that the revised manuscript has been significantly improved owing to the feedback provided. Below you can find a point-by-point response to each reviewer comment in blue. We are looking forward that the revision will be published in the Journal eLife.

Reviewer #1 (Public Review):

The authors show that concurrently presenting foreign words and their translations during sleep leads to the ability to semantically categorize the foreign words above chance. Specifically, this procedure was successful when stimuli were delivered during slow oscillation troughs as opposed to peaks, which has been the focus of many recent investigations into the learning & memory functions of sleep. Finally, further analyses showed that larger and more prototypical slow oscillation troughs led to better categorization performance, which offers hints to others on how to improve or predict the efficacy of this intervention. The strength here is the novel behavioral finding and supporting physiological analyses, whereas the biggest weakness is the interpretation of the peak vs. trough effect.

R1.1. Major importance:

I believe the authors could attempt to address this question: What do the authors believe is the largest implication of this studies? How far can this technique be pushed, and how can it practically augment real-world learning?

We revised the discussion to put more emphasis on possible practical applications of this study (lines 645-656).

In our opinion, the strength of this paper is its contribution to the basic understanding of information processing during deep sleep, rather than its insights on how to augment realworld learning. Given the currently limited data on learning during sleep, we believe it would be premature to make strong claims about potential practical applications of sleep-learning. In addition, as pointed out in the discussion section, we do not know what adverse effects sleep-learning has on other sleep-related mechanisms such as memory consolidation.

R1.2. Lines 155-7: How do the authors argue that the words fit well within the half-waves when the sounds lasted 540 ms and didn't necessarily start right at the beginning of each half-wave? This is a major point that should be discussed, as part of the down-state sound continues into the up-state. Looking at Figure 3A, it is clear that stimulus presented in the slow oscillation trough ends at a time that is solidly into the upstate, and would not neurolinguists argue that a lot of sound processing occurs after the end of the sound? It's not a problem for their findings, which is about when is the best time to start such a stimulus, but it's a problem for the interpretation. Additionally, the authors could include some discussion on whether possibly presenting shorter sounds would help to resolve the ambiguities here.

The word pairs’ presentations lasted on average ~540 ms. Importantly, the word pairs’ onset was timed to occur 100 ms before the maximal amplitude of the targeted peaks/troughs.

Therefore, most of a word’s sound pattern appeared during the negative going half-wave (about 350ms of 540ms). Importantly, Brodbeck and colleagues (2022) have shown that phonemes are continuously analyzed and interpreted with delays of about 50-200 ms, peaking at 100ms delay. These results suggest that word processing started just following the negative maximum of a trough and finished during the next peak. Our interpretation (e.g. line 520+) suggests that low-level auditory processing reaches the auditory cortex before the positive going half-wave. During the positive going half-wave the higher-level semantic networks appear the extract the presented word's meaning and associate the two simultaneously presented words. We clarified the time course regarding slow-wave phases and sound presentation in the manuscript (lines 158-164). Moreover, we added the limitation that we cannot know for sure when and in which slow-wave phase words were processed (lines 645-656). Future studies might want to look at shorter lasting stimuli to narrow down the timing of the word processing steps in relation to the sleep slow waves.

R1.3. Medium importance:

Throughout the paper, another concern relates to the term 'closed-loop'. It appears this term has been largely misused in the literature, and I believe the more appropriate term here is 'real-time' (Bergmann, 2018, Frontiers in Psychology; Antony et al., 2022, Journal of Sleep Research). For instance, if there were some sort of algorithm that assessed whether each individual word was successfully processed by the brain during sleep and then the delivery of words was subsequently changed, that could be more accurately labelled as 'closed-loop'.

We acknowledge that the meaning of “closed-loop” in its narrowest sense is not fulfilled here. We believe that “slow oscillation phase-targeted, brain-state-dependent stimulation” is the most appropriate term to describe the applied procedure (BSDBS, Bergmann, 2018). We changed the wording in the manuscript to brain-state-dependent stimulation algorithm. Nevertheless, we would like to point out that the algorithm we developed and used (TOPOSO) is very similar to the algorithms often termed closed-loop algorithm in memory and sleep (e.g. Esfahani et al., 2023; Garcia-Molina et al., 2018; Ngo et al., 2013, for a comparison of TOPOSO to these techniques see Wunderlin et al., 2022 and for more information about TOPOSO see Ruch et al., 2022).

R1.4. Figure 5 and corresponding analyses: Note that the two conditions end up with different sounds with likely different auditory complexities. That is, one word vs. two words simultaneously likely differ on some low-level acoustic characteristics, which could explain the physiological differences. Either the authors should address this via auditory analyses or it should be added as a limitation.

This is correct, the two conditions differ on auditory complexities. Accordingly, we added this issue as another limitation of the study (line 651-653). We had decided for a single word control condition to ensure that no associative learning (between pseudowords) could take place in the control condition because this was the critical learning process in the experimental condition. We would like to point out that we observed significant differences in brain responses to the presentation of word-pairs (experimental condition) vs single pseudowords (control condition) in the Trough condition, but not the Peak condition. If indeed low-level acoustic characteristics explained the EEG differences occurring between the two conditions then one would expect these differences occurring in both the trough and the peak condition because earlier studies showed that low-level acoustic processing proceeds in both phases of slow waves (Andrillon et al., 2016; Batterink et al., 2016; Daltrozzo et al., 2012).

R1.5. Line 562-7 (and elsewhere in the paper): "episodic" learning is referenced here and many times throughout the paper. But episodic learning is not what was enhanced here. Please be mindful of this wording, as it can be confusing otherwise.

The reported unconscious learning of novel verbal associations during sleep may not match textbook definitions of episodic memory. However, the traditional definitions of episodic memory have long been criticised (e.g., Dew & Cabeza, 2011; Hannula et al., 2023; Henke, 2010; Reder et al., 2009; Shohamy & Turk-Browne, 2013).

We stand by our claim that sleep-learning was of episodic nature. Here we use a computational definition of episodic memory (Cohen & Eichenbaum, 1993; Henke, 2010; O’Reilly et al., 2014; O’Reilly & Rudy, 2000) and not the traditional definition of episodic memory that ties episodic memory to wakefulness and conscious awareness (Gabrieli, 1998; Moscovitch, 2008; Schacter, 1998; Squire & Dede, 2015; Tulving, 2002). We revised the manuscript to clarify that and how our definition differs from traditional definitions. Please see reviewer comment R3.1 for a more extensive answer.

Reviewer #2 (Public Review):

In this project, Schmidig, Ruch and Henke examined whether word pairs that were presented during slow-wave sleep would leave a detectable memory trace 12 and 36 hours later. Such an effect was found, as participants showed a bias to categorize pseudowords according to a familiar word that they were paired with during slow-wave sleep. This behavior was not accompanied by any sign of conscious understanding of why the judgment was made, and so demonstrates that long-term memory can be formed even without conscious access to the presented content. Unconscious learning occurred when pairs were presented during troughs but not during peaks of slow-wave oscillations. Differences in brain responses to the two types of presentation schemes, and between word pairs that were later correctly- vs. incorrectly-judged, suggest a potential mechanism for how such deep-sleep learning can occur.

The results are very interesting, and they are based on solid methods and analyses. Results largely support the authors' conclusions, but I felt that there were a few points in which conclusions were not entirely convincing:

R2.1. As a control for the critical stimuli in this study, authors used a single pseudoword simultaneously played to both ears. This control condition (CC) differs from the experimental condition (EC) in a few dimensions, among them: amount of information provided, binaural coherence and word familiarity. These differences make it hard to conclude that the higher theta and spindle power observed for EC over CC trials indicate associative binding, as claimed in the paper. Alternative explanations can be made, for instance, that they reflect word recognition, as only EC contains familiar words.

We agree. In the revised version of the manuscript, we emphasise this as a limitation of our study (line 653-656). Moreover, we understand that the differences between stimuli of the control and the experimental condition must not rely only on the associative binding of two words. We cautioned our interpretation of the findings.

Interestingly, EC vs CC exhibits differences following trough- but not peak targeting (see R1.4). If indeed all the EC vs CC differences were unrelated to associative binding, we would expect the same EC vs CC differences when peaks were targeted. Hence, the selective EC vs CC differences in the trough condition suggest that the brain is more responsive to sound, information, word familiarity and word semantics during troughs, where we found successful learning, compared to peaks, where no learning occurred. Troughtargeted word pairs (EC) versus foreign words (CC) enhanced the theta power 336 at 500 ms following word onset and this theta enhancement correlated significantly with interindividual retrieval performance indicating that theta probably promoted associative learning during sleep. This correlation was insignificant for spindle power.

R2.2. The entire set of EC pairs were tested both following 12 hours and following 36 hours. Exposure to the pairs during test #1 can be expected to have an effect over memory one day later, during test #2, and so differences between the tests could be at least partially driven by the additional activation and rehearsal of the material during test #1. Therefore, it is hard to draw conclusions regarding automatic memory reorganization between 12 and 36 hours after unconscious learning. Specifically, a claim is made regarding a third wave of plasticity, but we cannot be certain that the improvement found in the 36 hour test would have happened without test #1.

We understand that the retrieval test at 12h may have had an impact on performance on the retrieval test at 36h. Practicing retrieval of newly formed memories is known to facilitate future retrieval of the same memories (e.g. Karpicke & Roediger, 2008). Hence, practicing the retrieval of sleep-formed memories during the retrieval test at 12h may have boosted performance at 36h.

However, recent literature suggests that retrieval practice is only beneficial when corrective feedback is provided (Belardi et al., 2021; Metcalfe, 2017). In our study, we only presented the sleep-played pseudowords at test and participants received no feedback regarding the accuracy of their responses. Thus, a proper conscious re-encoding could not take place. Nevertheless, the retrieval at 12h may have altered performance at 36h in other ways. For example, it could have tagged the reactivated sleep-formed memories for enhanced consolidation during the next night (Rabinovich Orlandi et al., 2020; Wilhelm et al., 2011).

We included a paragraph on the potential carry-over effects from retrieval at 12h on retrieval at 36h in the discussion section (line 489-496; line 657-659). Furthermore, we removed the arguments about the “third wave of plasticity”.

R2.3. Authors claim that perceptual and conceptual processing during sleep led to increased neural complexity in troughs. However, neural complexity was not found to differ between EC and CC, nor between remembered and forgotten pairs. It is therefore not clear to me why the increased complexity that was found in troughs should be attributed to perceptual and conceptual word processing, as CC contains meaningless vowels. Moreover, from the evidence presented in this work at least, I am not sure there is room to infer causation - that the increase in HFD is driven by the stimuli - as there is no control analysis looking at HFD during troughs that did not contain stimulation.

With the analysis of the HFD we would like to provide an additional perspective to the oscillation-based analysis. We checked whether the boundary condition of Peak and Trough targeting changes the overall complexity or information content in the EEG. Our goal was to assess the change in neural complexity (relative to a pre-stimulus baseline) following the successful vs unsuccessful encoding of word pairs during sleep.

We acknowledge that a causal interpretation about HFD is not warranted, and we revised the manuscript accordingly. It was unexpected that we could not find the same results in the contrast of EC vs CC or correct vs incorrect word pairs. We suggest that our signal-to noise ratio might have been too weak.

One could argue that the phase targeting alone (without stimulation) induces peak/trough differences in complexity. We cannot completely rule out this concern. But we tried to use the EEG that was not influenced by the ongoing slow-wave: the EEG 2000-500ms before the stimulus onset and 500-2000ms after the stimulus onset. Therefore, we excluded the 1s of the targeted slow-wave, hoping that most of the phase inherent complexity should have faded out (see Figure 2). We could not further extend the time window of analysis due to the minimal stimulus onset interval of 2s. Of course we cannot exclude that the targeted Trough impacted the following HFD. We clarified this in the manuscript (line 384-425).

Furthermore, we did find a difference of neural complexity between the pre-stimulus baseline and the post-stimulus complexity in the Peak condition but not in the Trough condition (we now added this contrast to the manuscript, line 416-419). Hence, the change in neural complexity is a reaction to the interaction of the specific slow-wave phase with the processing of the word pairs. Even though these results cannot provide unambiguous, causal links, we think they can figure as an important start for other studies to decipher neural complexity during slow wave sleep.

Reviewer #3 (Public Review):

The study aims at creating novel episodic memories during slow wave sleep, that can be transferred in the awake state. To do so, participants were simultaneously presented during sleep both foreign words and their arbitrary translations in their language (one word in each ear), or as a control condition only the foreign word alone, binaurally. Stimuli were presented either at the trough or the peak of the slow oscillation using a closed-loop stimulation algorithm. To test for the creation of a flexible association during sleep, participant were then presented at wake with the foreign words alone and had (1) to decide whether they had the feeling of having heard that word before, (2) to attribute this word to one out of three possible conceptual categories (to which translations word actually belong), and (3) to rate their confidence about their decision.

R3.1. The paper is well written, the protocol ingenious and the methods are robust. However, the results do not really add conceptually to a prior publication of this group showing the possibility to associate in slow wave sleep pairs of words denoting large or small object and non words, and then asking during ensuing wakefulness participant to categorise these non words to a "large" or "small" category. In both cases, the main finding is that this type of association can be formed during slow wave sleep if presented at the trough (versus the peak) of the slow oscillation. Crucially, whether these associations truly represent episodic memory formation during sleep, as claimed by the authors, is highly disputable as there is no control condition allowing to exclude the alternative, simpler hypothesis that mere perceptual associations between two elements (foreign word and translation) have been created and stored during sleep (which is already in itself an interesting finding). In this latter case, it would be only during the awake state when the foreign word is presented that its presentation would implicitly recall the associated translation, which in turn would "ignite" the associative/semantic association process eventually leading to the observed categorisation bias (i.e., foreign words tending to be put in the same conceptual category than their associated translation). In the absence of a dis-confirmation of this alternative and more economical hypothesis, and if we follow Ocam's razor assumption, the claim that there is episodic memory formation during sleep is speculative and unsupported, which is a serious limitation irrespective of the merits of the study. The title and interpretations should be toned down in this respect

Our study conceptually adds to and extends the findings by Züst et al. (a) by highlighting the precise time-window or brain state during which sleep-learning is possible (e.g. slow-wave trough targeting), (b) by demonstrating the feasibility of associative learning during night sleep, and (c) by uncovering the longevity of sleep-formed memories.

We acknowledge that the reported unconscious learning of novel verbal associations during sleep may not match textbook definitions of episodic memory. However, the traditional definitions of episodic memory have long been criticised (e.g, (Dew & Cabeza, 2011; Hannula et al., 2023; Henke, 2010; Reder et al., 2009; Shohamy & Turk-Browne, 2013). We stand by our claim that sleep-learning was of episodic nature. We use a computational definition of episodic memory (Cohen & Eichenbaum, 1993; Henke, 2010; O’Reilly et al., 2014; O’Reilly & Rudy, 2000), and not the traditional definition of episodic memory that ties episodic memory to wakefulness and conscious awareness (Gabrieli, 1998; Moscovitch, 2008; Schacter, 1998; Squire & Dede, 2015; Tulving, 2002). The core computational features of episodic memory are 1) rapid learning, 2) association formation, and 3) a compositional and flexible representation of the associations in long-term memory.

Therefore, we revised the manuscript to emphasize how our definition differs from traditional definitions (line 64).

For the current study, we designed a retrieval task that calls on the core computational features of episodic memory by assessing flexible retrieval of sleep-formed compositional word-word associations. Reviewer 3 suggests an alternative interpretation for the learning observed here: mere perceptual associations between foreign words and translations words are stored during sleep, and semantic associations are only inferred at retrieval testing during ensuing wakefulness. First, these processing steps would require the rapid soundsound associative encoding, long-term storage, and the flexible sound retrieval, which would still require hippocampal processing and computations in the episodic memory system. Second, this mechanism seems highly laborious and inefficient. The sound pattern of a word at 12 hours after learning triggers the reactivation of an associated sound pattern of another word. This sound pattern then elicits the activation of the translation words’ semantics leading to the selection of the correct superordinate semantic category at test.

Overall, we believe that our pairwise-associative learning paradigm triggered a rapid conceptual-associative encoding process mediated by the hippocampus that provided for flexible representations of foreign and translation words in episodic memory. This study adds to the existing literature by examining specific boundary conditions of sleep-learning and demonstrates the longevity (at least 36 hours) of sleep-learned associations.

Other remarks:

R3.2. Lines 43-45 : the assumption that the sleeping brain decides whether external events can be disregarded, requires awakening or should be stored for further consideration in the waking state is dubious, and the supporting references date from a time (the 60') during which hypnopedia was investigated in badly controlled sleep conditions (leaving open the doubt about the possibility that it occurred during micro awakenings)

We revised the manuscript to add timelier and better controlled studies that bolster the 60ties-born claim (line 40-51). Recently, it has been shown that the sleeping brain preferentially processes relevant information. For example the information conveyed by unfamiliar voices (Ameen et al., 2022), emotional content (Holeckova et al., 2006; Moyne et al., 2022), our own compared to others’ names (Blume et al., 2018).

R3.3. 1st paragraph, lines 48-53 , the authors should be more specific about what kind of new associations and at which level they can be stored during sleep according to recent reports, as a wide variety of associations (mostly elementary levels) are shown in the cited references. Limitations in information processing during sleep should also be acknowledged.

In the lines to which R3 refers, we cite an article (Ruch & Henke, 2020) in which two of the three authors of the current manuscript elaborate in detail what kind of associations can be stored during sleep. We revised these lines to more clearly present the current understanding of the potential and the limitations of sleep-learning (line 40-51). Although information processing during sleep is generally reduced (Andrillon et al., 2016), a variety of different kinds of associations can be stored, ranging from tone-odour to word-word association (Arzi et al., 2012, 2014; Koroma et al., 2022; Züst et al., 2019).

R3.4. The authors ran their main behavioural analyses on delayed retrieval at 36h rather than 12h with the argument that retrieval performance was numerically larger at 36 than 12h but the difference was non-significant (line 181-183), and that effects were essentially similar. Looking at Figure 2, is the trough effect really significant at 12h ? In any case, the fact that it is (numerically) higher at 36 than 12h might suggest that the association created at the first 12h retrieval (considering the alternative hypothesis proposed above) has been reinforced by subsequent sleep.

The Trough effect at 12h is not significant, as stated on line 185 (“Planned contrasts against chance level revealed that retrieval performance significantly exceeded chance at 36 hours only (P36hours = 0.036, P12hours = 0.094).”). It seems that our wording was not clear. Therefore, we refined the description of the behavioural analysis in the manuscript (lines 188-193).

In brief, we report an omnibus ANOVA with a significant main effect of targeting type (Trough vs Peak, main effect Peak versus Trough: F(1,28) = 5.237, p = 0.030, d = 0.865). Because Trough-targeting led to significantly better memory retention than Peak-targeting, we computed a second ANOVA, solely including participants with through-targeted word-pair encoding. The memory retention in the Trough condition is above chance (MTrough = 39.11%, SD = 10.76; FIntercept (1,14) = 5.660, p = 0.032) and does not significantly differ between the 12h and 36h retrieval (FEncoding-Test Delay (1,14) = 1.308, p = 0.272). However, the retrieval performance at 36h numerically exceeds the performance at 12h and the direct comparison against chance reveals that the 36h but not the 12h retrieval was significant (P36hours = 0.036, P12hours = 0.094). Hence, we found no evidence for above chance performance at the 12h retrieval and focused on the retrieval after 36h in the EEG analysis.

We agree with the reviewer that the subsequent sleep seems to have improved consolidation and subsequent retrieval. We assume that the reviewer suggests that participants merely formed perceptual associations during sleep and encoded episodic-like associations during testing at 12h (as pointed out in R 3.1). However, we believe that it is unlikely that the awake encoding of semantic associations during the 12h retrieval led to improved performance after 36h. We changed the discussion regarding the interaction between retrieval at 12h and 36h (line 505-512, also see R 2.2)

R3.5> In the discussion section lines 419-427, the argument is somehow circular in claiming episodic memory mechanisms based on functional neuroanatomical elements that are not tested here, and the supporting studies conducted during sleep were in a different setting (e.g. TMR)

Indeed, the TMR and animal studies are a different setting compared to the present study. We re-wrote this part and only focused on the findings of Züst and colleagues (2019), who examined hippocampal activity during the awake retrieval of sleep-formed memories (lines 472-482). Additionally, we would like to emphasise that our main reasoning is that the task requirements called upon the episodic memory system.

R3.6. Supplementary Material: in the EEG data the differentiation between correct and incorrect ulterior classifications when presented at the peak of the slow oscillation is only significant in association with 36h delayed retrieval but not at 12h, how do the authors explain this lack of effect at 12 hour ?

We assume that the reviewer refers to the TROUGH condition (word-pairs targeted at a slow-wave trough) and not as written to the peak condition. We argue that the retention performance at 12h is not significantly above chance (M12hours = 37.4%, P12hours = 0.094).

Hence, the distinction between “correctly” and “incorrectly” categorised word pairs was not informative for the EEG analysis during sleep. For whatever reason the 12h retrieval was not significantly above chance, the less successful memory recall and thus a less balanced trial count makes recall accuracy a worse delineator for separating EEG trials then the recall performance after 36 hours.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Minor importance:

Abstract: The opening framing is confusing here and in the introduction. Why frame the paper in the broadest terms about awakenings and threats from the environment when this is a paper about intersections between learning & memory and sleep? I do understand that there is an interesting point to be made about the counterintuitive behavioral findings with respect to sleep generally being perceived as a time when stimuli are blocked out, but this does not seem to me to be the broadest points or the way to start the paper. The authors should consider this but of course push back if they disagree.

We understand the reviewer’s criticism but believe that this has more to do with personal preferences than with the scientific value or validity of our work. We believe that it is our duty as researchers to present our study in a broader context because this may help readers from various fields to understand why the work is relevant. To some readers, evidence for learning during sleep may seem trivial, to others, it may seem impossible or a weird but useless conundrum. By pointing out potential evolutionary benefits of the ability to acquire new information during sleep, we help the broad readership of eLife understand the relevance of this work.

Lines 31-32: "Neural complexity" -> "neural measures of complexity" because it isn't clear what "neural complexity" means at this point in the abstract. Though, note my other point that I believe this analysis should be removed.

To our understanding, “neural complexity” is a frequently used term in the field and yields more than 4000 entries on google scholar. Whereas ‘neural measures of complexity’ only finds 3 hits on google scholar [September 2023]. In order to link our study with other studies on neural complexity, we would like to keep this terminology. As an example, two recent publications using “neural complexity” are Lee et al. (2020) and Frohlich et al. (2022).

Lines 42-43: The line of work on 'sentinel' modes would be good to cite here (e.g., Blume et al., 2017, Brain & Language).

We added the suggested citation to the manuscript (lines 52).

Lines 84-90: While I appreciate the authors desire to dig deep and try to piece this all together, this is far too speculative in my opinion. Please see my other points on the same topic.

In this paragraph, we point out why both peaks and troughs are worth exploring for their contributions to sensory processing and learning during sleep. Peaks and troughs are contributing mutually to sleep-learning. Our speculations should inspire further work aimed at pinning down the benefits of peaks and troughs for sleep-learning. We clarified the purpose and speculative nature of our arguments in the revised version of the manuscript.

Line 109: "outlasting" -> "lasting over" or "lasting >"

We changed the wording accordingly.

Line 111: I believe 'nonsense' is not the correct term here, and 'foreign' (again) would be preferred. Some may be offended to hear their foreign word regarded as 'nonsense'. However, please let me know if I have misunderstood.

We would like to use the linguistic term “pseudoword” (aligned with reviewer 2’s comment) and we revised the manuscript accordingly.

Figure 1A: "Enconding" -> "Encoding"

Thank you for pointing this out.

Lines 201-2: Were there interactions between confidence and correctness on the semantic categorization task? Were correct responses given with more confidence than incorrect ones? This would not necessarily be a problem for the authors' account, as there can of course be implicit influences on confidence (i.e., fluency).

As is stated in the results section, confidence ratings did not differ significantly between correct and incorrect assignments (Trough condition: F(1,14) = 2.36, p = 0.15); Peak condition: F(1,14) = 0.48, p = 0.50).

Line 236: "Nicknazar" -> "Niknazar"

Thank you for pointing this out.

Line 266: "profited" -> "benefited"

We changed the wording accordingly.

Lines 280-4: There seems some relevance here with Malerba et al. (2018) and her other papers to categorize slow oscillations.

Diving into the details on how to best categorise slow oscillations is beyond the scope of this manuscript. Here, we build on work from the field of microstate analyses and use two measures to describe and quantify the targeted brain states: the topography of the electric field (i.e., the correlation of the electric field with an established template or “microstate”), and the field strength (global field power, GFP). While the topography of a quasi-stable electric field reflects activity in a specific neural network, the strength (GFP) of a field most likely mirrors the degree of activation (or inactivity) in the specific network. Here, we find that consistent targeting of a specific network state yielding a strong frontal negativity benefitted learning during sleep. For a more detailed explanation of the slow-wave phase targeting see (Ruch et al., 2022).

Lines 343-6: Was it intentional to have 0.5 s (0.2-0.7 s) surrounding the analysis around 500 ms but only 0.4 s (0.8-1.2 s) surrounding the analysis around 1 s? Could the authors use the same size interval or justify having them be different?

We apologise for the misleading phrasing and we clarified this in the revised manuscript. We applied the same procedure for the comparison of later correctly vs incorrectly classified pseudowords as we did for the comparison between EC and CC. Hence, we analysed the entire window from 0s to 2.5s with a cluster-based permutation approach. Contrary to the EC vs CC contrast, no cluster remained significant for the comparison of the subsequent memory effect. By mistake we reported the wrong time window. In the revised manuscript, the paragraph is corrected (lines 364-369).

Line 356-entire HFD section: it is unclear what's gained by this analysis, as it could simply be another reflection of the state of the brain at the time of word presentation. In my opinion, the authors should remove this analysis and section, as it does not add clarity to other aspects of the paper.

(If the authors keep the section) Line 361-2 - "Moreover, high HFD values have been associated with cognitive processing (Lau et al., 2021; Parbat & Chakraborty, 2021)." This statement is vague. Could the authors elaborate?

Please see our answer to Reviewer 2 (2.3) for a more detailed explanation. In brief, we would like to keep the analysis with the broad time window of -2 to -0.5 and from 0.5 to 2 s.

Lines 403-4: How was it determined that these neural networks mediated both conscious/unconscious processes? Perhaps the authors meant to make a different point, but the way it reads to me is that there is evidence that some neural networks are conscious and others are not and both forms engage in similar functions.

We revised the manuscript to be more precise and clear: “The conscious and unconscious rapid encoding and flexible retrieval of novel relational memories was found to recruit the same or similar networks including the hippocampus(Henke et al., 2003; Schneider et al., 2021). This suggests that conscious and unconscious relational memories are processed by the same memory system.” (p. 22, top).

Lines 433-41: Performance didn't actually significantly increase from 12 to 36 hours, so this is all too speculative in my opinion.

We removed the speculative claim that performance may have increased from the retrieval at 12 hours to the retrieval at 36 hours.

Line 534: "assisted by enhanced" -> "coincident with". It's unclear whether theta reflects successful processing as having occurred or whether it directly affects or assists with it.

We have adjusted the wording to be more cautious, as suggested (line 588).

Line 572-4: Rothschild et al. (2016) is relevant here.

Unfortunately, we do not see the relevance of this article within the context of our work.

Line 577 paragraph: The authors may consider adding a note on the importance of ethical considerations surrounding this form of 'inception'.

We extended this part by adding ethical considerations to the discussion section (Stickgold et al., 2021, line 657).

Line 1366: It would be better if the authors could eventually make their data publicly available. This is obviously not required, but I encourage the authors to consider it if they have not considered it already.

In my opinion, the discussion is too long. I really appreciate the authors trying to figure out the set of precise times in which each level of neural processing might occur and how this intersects with their slow oscillation phase results. However, I found a lot of this too speculative, especially given that the sounds may bleed into parts of other phases of the slow oscillation. I do not believe this is a problem unique to these authors, as many investigators attempting to target certain phases in the target memory reactivation literature have faced the same problem, but I do believe the authors get ahead of the data here. In particular, there seems to be one paragraph in the discussion that is multiple pages long (p. 22-24). This paragraph I believe has too much detail and should be broken up regardless, as it is difficult for the reader to follow.

Considering the recent literature, we believe this interpretation best explains the data. As argued earlier, we believe that a speculative interpretation of the reported phenomena can provide substantial added value because it inspires future experimental work. We have improved the manuscript by clearly distinguishing between data and interpretation. We do declare the speculative nature of some offered interpretations. We hope that these speculations, which are testable hypotheses (!), will eventually be confirmed or refuted experimentally.

Reviewer #2 (Recommendations For The Authors):

I very much enjoyed the paper and think it describes important findings. I have a few suggestions for improvement, and minor comments that caught my eye during reading:

(1) I was missing an analysis of CC ERP, and its comparison to EC ERP.

We added this analysis to the manuscript (line 299-301). The comparison of CC ERP with EC ERP did not yield any significant cluster for either the peak (cluster-level Monte Carlo p=0.54) or the trough (cluster-level Monte Carlo p>0.37). We assume that the noise level was too high for the identification of differences between CC and EC ERP.

(2) Regarding my public review comment #2, some light can be shed on between-test effects, I believe, using an item-based analysis - looking at correlations between items' classifications in test #1 and test #2. The assumption seems to be that items that were correct in test #1 remained correct in test #2 while other new correct classifications were added, owing to the additional consolidation happening between the two tests. But that is an empirical question that can be easily tested. If no consistency in item classification is found, on the other hand, or if only consistency in correct classification is found, that would be interesting in itself. This item-based analysis can help tease away real memory from random correct classification. For instance, the subset of items that are consistently classified correctly could be regarded as non-fluke at higher confidence and used as the focus of subsequent-memory analysis instead of the ones that were correct only in test #2.

Thanks, we re-analysed the data accordingly. Participants were consistent at choosing a specific object category for an item at 12 hours and 36 hours (consistency rate = 47% same category, chance level is 1/3). Moreover, the consistency rate did not differ between the Trough and the Peak condition (MTrough = 47.2%, MPeak = 47.0%, P = 0.98). The better retrieval performance in the Trough compared to the Peak condition after 36 hours is due to: A) if participants were correct at 12h, they chose again the correct answer at 36h (Trough: 20% & Peak: 14%). B) Following an incorrect answer at 12h, participants switched to another object category at 36h (Trough: 72%, Peak: 67%). C) If participants switched the object category following an incorrect answer at 12h, they switched more often to the correct category at 36h in the trough versus the peak condition (Trough: in 56% & Peak: 53%). Hence, the data support the reviewer’s assumption: items that were correct after 12 hours remained correct after 36 hours, while other new correct classifications were generated at 36h owing to the additional consolidation happening between the two tests. We added this finding to the manuscript (line 191-200, Figure S6):

Author response image 1.

As suggested, we re-analysed the ERP with respect to the subsequent memory effect. This time we computed four conditions according to the reviewer’s argument about consistently correctly classified pseudowords, presented in the figure below: ERP of trials that were correctly classified at 36h (blue), ERP of trials that were incorrectly classified at 36h (light blue), ERP of trials that were correctly classified twice (brown) and ERP of trials that were not correctly classified twice (orange, all trials that are not in brown). Please note that the two blue lines are reported in the manuscript and include all trials. The brown and the orange line take the consistency into account and together include as well all trials.

Author response image 2.

By excluding even more trials from the group of correct retrieval responses, the noise level gets high. Therefore, the difference between the twice-correct and the not-twice-correct trials is not significant (cluster-level Monte Carlo p > 0.27). Because the ERP of twice-correct trials seems very similar to the ERP of the trials correctly classified at 36h at frontal electrodes, we assume that our ERP effect is not driven by a few extreme subjects. Similarly, not-twicecorrect trials (orange) have a stronger frontal trough than the trials incorrectly classified at 36h (light blue).

(3) In a similar vein, a subject-based analysis would be highly interesting. First and foremost, readers would benefit from seeing the lines that connect individual dots across the two tests in figures 2B and 2C. It is reasonable to expect that only a subset of participants were successful learners in this experiment. Finding them and analyzing their results separately could be revealing.

We added a Figure S1 to the supplementary material, providing the pairing between performance of the 12h and the 36h retrieval.

It is an interesting idea to look at successful learners alone. We computed the ERP of the subsequent memory effect for those participants, who had an above change retrieval accuracy at 36h. The result shows a similar effect as reported for all participants (frontal cluster ~0-0.3s). The p-value is only 0.08 because only 9 of 15 participants exhibited an above chance retrieval performance at 36 hours.

Author response image 3.

ERP effect of correct (blue) vs incorrect (light blue) pseudoword category assignment of participants with a retrieval performance above chance at 36h (SD as shades):

We prefer to not include this data in the manuscript, but are happy to provide it here.

(4) I wondered why the authors informed subjects of the task in advance (that they will be presented associations when they slept)? I imagine this may boost learning as compared to completely naïve subjects. Whether this is the reason or not, I think an explanation of why this was done is warranted, and a statement whether authors believe the manipulation would work otherwise. Also, the reader is left wondering why subjects were informed only about test #1 and not about test #2 (and when were they told about test #2).

Subjects were informed of all the tests upfront. We apologize for the inconsistency in the manuscript and revised the method part. The explanation of why participants were informed is twofold: a) Participants had to sleep with in-ear headphones. We wanted to explain to participants why these are necessary and why they should not remove them. b) We hoped that participants would be expecting unconsciously sounds played during sleep, would process these sounds efficiently and would remain deeply asleep (no arousals).

(5) FoHH is a binary yes/no question, and so may not have been sensitive enough to demonstrate small differences in familiarity. For comparison, the Perceptual Awareness Scale (Ramsøy & Overgaard, 2004) that is typically used in studies of unconscious processing is of a 4-point scale, and this allows to capture more nuanced effects such as partial consciousness and larger response biases. Regardless, it would be informative to have the FoHH numbers obtained in this study, and not just their comparison between conditions. Also, was familiarity of EC and CC pseudowords compared? One may wonder whether hearing the pseudowords clearly vs. in one ear alongside a familiar word would make the word slightly more familiar.

We apologize for having simplified this part too much in the manuscript. Indeed, the FoHH is comparable to the PAS. We used a 4-point scale, where participants rated their feeling of whether they have heard the pseudoword during previous sleep. In the revised manuscript, we report the complete results (line 203-223). The FoHH did not differ between any of the suggested contrasts. Thus, for both the peak and the trough condition, the FoHH did not differ between sleep-played vs new; correct EC trials vs new; correct vs incorrect EC trials; EC vs CC trials. To illustrate the results, a figure of the FoHH has been added to the supplement (Figure S4).

(6) Similarly, it would be good to report the numbers of the confidence ratings in the paper as well.

In the revised manuscript, we extended the description of the confidence rating results. We added the descriptive statistics (line 224-236) and included a corresponding figure in the supplement (Figure S5).

Minor/aesthetic comments:

We implemented all the following suggestions.

(1) I suggest using "pseudoword" or "nonsense word" instead of "foreign word", because "foreign word" typically means a real word from a different language. It is quite confusing when starting to read the paper.

After reconsidering, we think that pseudoword is the appropriate linguistic term and have revised the manuscript accordingly.

(2) Lines 1000-1001: "The required sample size of N = 30 was determined based on a previous sleep-learning study". I was missing a description of what study you are referring to.

(3) I am not sure I understood the claim nor the rationale made in lines 414-417. Is the claim that pairs did not form one integrated engram? How do we know that? And why would having one engram not enable extracting the meaning from a visual-auditory presentation of the cue? The sentence needs some rewording and/or unpacking.

(4) Were categories counterbalanced (i.e., did each subjects' EC contain 9 animal words, 9 tool words and 9 place words)?

(5) Asterisks indicating significant effects are missing from Figure 4 and S2.

(6) Fig1 legend: "Participants were played with pairs" is ungrammatical.

(7) Line 1093: no need for a comma.

(8) Line 1336: missing opening parenthesis

(9) Line 430: "observe" instead of "observed".

(10) Line 466: two dots instead of one..

Reviewer #3 (Recommendations For The Authors):

Methods: 2 separate ANOVAs are performed (lines 160-185), but would not it make more sense to combine both in one ? If kept separated then a correction for multiple comparisons might be needed (p/2 = 0.025)

We computed an omnibus ANOVA. In a next step, we examined the effect in the significant targeting condition by computing another ANOVA. For further explanations, see reviewer comment 3.4.

References

Ameen, M. S., Heib, D. P. J., Blume, C., & Schabus, M. (2022). The Brain Selectively Tunes to Unfamiliar Voices during Sleep. Journal of Neuroscience, 42(9), 1791–1803. https://doi.org/10.1523/JNEUROSCI.2524-20.2021

Andrillon, T., Poulsen, A. T., Hansen, L. K., Léger, D., & Kouider, S. (2016). Neural Markers of Responsiveness to the Environment in Human Sleep. The Journal of Neuroscience, 36(24), Article 24. https://doi.org/10.1523/JNEUROSCI.0902-16.2016

Arzi, A., Holtzman, Y., Samnon, P., Eshel, N., Harel, E., & Sobel, N. (2014). Olfactory Aversive Conditioning during Sleep Reduces Cigarette-Smoking Behavior. Journal of Neuroscience, 34(46), Article 46. https://doi.org/10.1523/JNEUROSCI.2291-14.2014

Arzi, A., Shedlesky, L., Ben-Shaul, M., Nasser, K., Oksenberg, A., Hairston, I. S., & Sobel, N. (2012). Humans can learn new information during sleep. Nature Neuroscience, 15(10), Article 10. https://doi.org/10.1038/nn.3193

Batterink, L. J., Creery, J. D., & Paller, K. A. (2016). Phase of Spontaneous Slow Oscillations during Sleep Influences Memory-Related Processing of Auditory Cues. Journal of Neuroscience, 36(4), 1401–1409. https://doi.org/10.1523/JNEUROSCI.3175-15.2016

Belardi, A., Pedrett, S., Rothen, N., & Reber, T. P. (2021). Spacing, Feedback, and Testing Boost Vocabulary Learning in a Web Application. Frontiers in Psychology, 12. https://www.frontiersin.org/articles/10.3389/fpsyg.2021.757262

Bergmann, T. O. (2018). Brain State-Dependent Brain Stimulation. Frontiers in Psychology, 9, 2108. https://doi.org/10.3389/fpsyg.2018.02108

Blume, C., del Giudice, R., Wislowska, M., Heib, D. P. J., & Schabus, M. (2018). Standing sentinel during human sleep: Continued evaluation of environmental stimuli in the absence of consciousness. NeuroImage, 178, 638–648. https://doi.org/10.1016/j.neuroimage.2018.05.056

Brodbeck, C., & Simon, J. Z. (2022). Cortical tracking of voice pitch in the presence of multiple speakers depends on selective attention. Frontiers in Neuroscience, 16. https://www.frontiersin.org/articles/10.3389/fnins.2022.828546

Cohen, N. J., & Eichenbaum, H. (1993). Memory, Amnesia, and the Hippocampal System. A Bradford Book.

Daltrozzo, J., Claude, L., Tillmann, B., Bastuji, H., & Perrin, F. (2012). Working memory is partially preserved during sleep. PloS One, 7(12), Article 12.

Dew, I. T. Z., & Cabeza, R. (2011). The porous boundaries between explicit and implicit memory: Behavioral and neural evidence. Annals of the New York Academy of Sciences, 1224(1), 174–190. https://doi.org/10.1111/j.1749-6632.2010.05946.x

Esfahani, M. J., Farboud, S., Ngo, H.-V. V., Schneider, J., Weber, F. D., Talamini, L. M., & Dresler, M. (2023). Closed-loop auditory stimulation of sleep slow oscillations: Basic principles and best practices. Neuroscience & Biobehavioral Reviews, 153, 105379. https://doi.org/10.1016/j.neubiorev.2023.105379

Frohlich, J., Chiang, J. N., Mediano, P. A. M., Nespeca, M., Saravanapandian, V., Toker, D., Dell’Italia, J., Hipp, J. F., Jeste, S. S., Chu, C. J., Bird, L. M., & Monti, M. M. (2022). Neural complexity is a common denominator of human consciousness across diverse regimes of cortical dynamics. Communications Biology, 5(1), Article 1. https://doi.org/10.1038/s42003-022-04331-7

Gabrieli, J. D. E. (1998). Cognitive neuroscience of human memory. Annual Review of Psychology, 87–115.

Garcia-Molina, G., Tsoneva, T., Jasko, J., Steele, B., Aquino, A., Baher, K., Pastoor, S., Pfundtner, S., Ostrowski, L., Miller, B., Papas, N., Riedner, B., Tononi, G., & White, D. P. (2018). Closed-loop system to enhance slow-wave activity. Journal of Neural Engineering, 15(6), 066018. https://doi.org/10.1088/1741-2552/aae18f

Hannula, D. E., Minor, G. N., & Slabbekoorn, D. (2023). Conscious awareness and memory systems in the brain. WIREs Cognitive Science, 14(5), e1648. https://doi.org/10.1002/wcs.1648

Henke, K. (2010). A model for memory systems based on processing modes rather than consciousness. Nature Reviews Neuroscience, 11(7), Article 7. https://doi.org/10.1038/nrn2850

Henke, K., Mondadori, C. R. A., Treyer, V., Nitsch, R. M., Buck, A., & Hock, C. (2003). Nonconscious formation and reactivation of semantic associations by way of the medial temporal lobe. Neuropsychologia, 41(8), Article 8. https://doi.org/10.1016/S0028-3932(03)00035-6

Holeckova, I., Fischer, C., Giard, M.-H., Delpuech, C., & Morlet, D. (2006). Brain responses to a subject’s own name uttered by a familiar voice. Brain Research, 1082(1), 142–152. https://doi.org/10.1016/j.brainres.2006.01.089

Karpicke, J. D., & Roediger, H. L. (2008). The Critical Importance of Retrieval for Learning. Science, 319(5865), 966–968. https://doi.org/10.1126/science.1152408

Koroma, M., Elbaz, M., Léger, D., & Kouider, S. (2022). Learning New Vocabulary Implicitly During Sleep Transfers With Cross-Modal Generalization Into Wakefulness. Frontiers in Neuroscience, 16, 801666. https://doi.org/10.3389/fnins.2022.801666

Lee, Y., Lee, J., Hwang, S. J., Yang, E., & Choi, S. (2020). Neural Complexity Measures. Advances in Neural Information Processing Systems, 33, 9713–9724. https://proceedings.neurips.cc/paper/2020/hash/6e17a5fd135fcaf4b49f2860c2474c7 c-Abstract.html

Metcalfe, J. (2017). Learning from Errors. Annual Review of Psychology, 68(1), 465–489. https://doi.org/10.1146/annurev-psych-010416-044022

Moscovitch, M. (2008). The hippocampus as a “stupid,” domain-specific module: Implications for theories of recent and remote memory, and of imagination. Canadian Journal of Experimental Psychology/Revue Canadienne de Psychologie Expérimentale, 62, 62–79. https://doi.org/10.1037/1196-1961.62.1.62

Moyne, M., Legendre, G., Arnal, L., Kumar, S., Sterpenich, V., Seeck, M., Grandjean, D., Schwartz, S., Vuilleumier, P., & Domínguez-Borràs, J. (2022). Brain reactivity to emotion persists in NREM sleep and is associated with individual dream recall. Cerebral Cortex Communications, 3(1), tgac003. https://doi.org/10.1093/texcom/tgac003

Ngo, H.-V. V., Martinetz, T., Born, J., & Mölle, M. (2013). Auditory Closed-Loop Stimulation of the Sleep Slow Oscillation Enhances Memory. Neuron, 78(3), Article 3. https://doi.org/10.1016/j.neuron.2013.03.006

O’Reilly, R. C., Bhattacharyya, R., Howard, M. D., & Ketz, N. (2014). Complementary Learning Systems. Cognitive Science, 38(6), 1229–1248. https://doi.org/10.1111/j.1551-6709.2011.01214.x

O’Reilly, R. C., & Rudy, J. W. (2000). Computational principles of learning in the neocortex and hippocampus. Hippocampus, 10(4), 389–397. https://doi.org/10.1002/1098-1063(2000)10:4<389::AID-HIPO5>3.0.CO;2-P

Rabinovich Orlandi, I., Fullio, C. L., Schroeder, M. N., Giurfa, M., Ballarini, F., & Moncada, D. (2020). Behavioral tagging underlies memory reconsolidation. Proceedings of the National Academy of Sciences, 117(30), 18029–18036. https://doi.org/10.1073/pnas.2009517117

Reder, L. M., Park, H., & Kieffaber, P. D. (2009). Memory systems do not divide on consciousness: Reinterpreting memory in terms of activation and binding. Psychological Bulletin, 135(1), Article 1. https://doi.org/10.1037/a0013974

Ruch, S., & Henke, K. (2020). Learning During Sleep: A Dream Comes True? Trends in Cognitive Sciences, 24(3), 170–172. https://doi.org/10.1016/j.tics.2019.12.007

Ruch, S., Schmidig, F. J., Knüsel, L., & Henke, K. (2022). Closed-loop modulation of local slow oscillations in human NREM sleep. NeuroImage, 264, 119682. https://doi.org/10.1016/j.neuroimage.2022.119682

Schacter, D. L. (1998). Memory and Awareness. Science, 280(5360), 59–60. https://doi.org/10.1126/science.280.5360.59

Schneider, E., Züst, M. A., Wuethrich, S., Schmidig, F., Klöppel, S., Wiest, R., Ruch, S., & Henke, K. (2021). Larger capacity for unconscious versus conscious episodic memory. Current Biology, 31(16), 3551-3563.e9. https://doi.org/10.1016/j.cub.2021.06.012

Shohamy, D., & Turk-Browne, N. B. (2013). Mechanisms for widespread hippocampal involvement in cognition. Journal of Experimental Psychology: General, 142(4), 1159–1170. https://doi.org/10.1037/a0034461

Squire, L. R., & Dede, A. J. O. (2015). Conscious and Unconscious Memory Systems. Cold Spring Harbor Perspectives in Biology, 7(3), a021667. https://doi.org/10.1101/cshperspect.a021667

Stickgold, R., Zadra, A., & Haar, A. J. H. (2021). Advertising in Dreams is Coming: Now What? Dream Engineering. https://dxe.pubpub.org/pub/dreamadvertising/release/1

Tulving, E. (2002). Episodic Memory: From Mind to Brain. Annual Review of Psychology, 53(1), 1–25. https://doi.org/10.1146/annurev.psych.53.100901.135114

Wilhelm, I., Diekelmann, S., Molzow, I., Ayoub, A., Mölle, M., & Born, J. (2011). Sleep Selectively Enhances Memory Expected to Be of Future Relevance. Journal of Neuroscience, 31(5), 1563–1569. https://doi.org/10.1523/JNEUROSCI.3575-10.2011

Wunderlin, M., Koenig, T., Zeller, C., Nissen, C., & Züst, M. A. (2022). Automatized online prediction of slow-wave peaks during non-rapid eye movement sleep in young and old individuals: Why we should not always rely on amplitude thresholds. Journal of Sleep Research, 31(6), e13584. https://doi.org/10.1111/jsr.13584

Züst, M. A., Ruch, S., Wiest, R., & Henke, K. (2019). Implicit Vocabulary Learning during Sleep Is Bound to Slow-Wave Peaks. Current Biology, 29(4), 541-553.e7. https://doi.org/10.1016/j.cub.2018.12.038

Author Response

The following is the authors’ response to the original reviews.

Reviewer #1

As written in my public review I consider the science of this work to be high quality. I have some suggestions for the write-up though. As a general comment, I think that too much has been put into the appendices. In particular, the main text could contain more details about the model.

We are pleased that this Reviewer feels that our work to be of “high quality”. We value the reviewer’s insightful suggestions and comments. Following this Reviewer’s suggestion we have moved certain sections to the main text.

In what follows, we provide responses to each of the reviewer’s inquiry, and indicate the appropriate changes in the revised version.

P2 -

ϕ is introduce as packing fraction - on p3 it’s called cell density. Also it is not clear whether it is an area fraction or a cell number density. Please define properly and I would suggest sticking to one notion.

ϕ is the cell packing fraction. In two dimensions (as is the case in our simulations) it is the area fraction. However, in order to stick to one general notation (independent of dimension) we use “packing fraction” to represent how densely the cells are packed. We changed it the revised manuscript to ensure uniformity.

P3 -

“which should and should slow down the overall dynamics” Typo?

Corrected it in the revised manuscript.

“One would intuitively expect that the ϕfree should decrease with increasing cell density” Please, define ϕfree

ϕfree is defined in Eqn. 4. We ought to have defined it in the introduction.

“When ϕ exceeds ϕS, the free area ϕfree saturates because the soft cells interpenetrate each other,” I suggest clearly distinguishing between biological cells and the agents (disks) used in the simulation. Please, also clarify What interpenetration of agents corresponds to in tissues?

We have rewritten the sentence as, ”The simulations show that when..” Soft disks used in the simulations seem to be not an unrealistic model for biological cells. The small deformations noted in our model is not that different from the cells in the tissues. For visual reference, please see Author response image 1. In the left panel of the figure, a 2D snapshot of the experimental zebrafish tissue, displays the deformation of cells labeled as 1 and 2. Likewise, the right panel illustrates the extent to which such deformations are replicated in the simulation by allowing two cells to overlap (the white area in the right panel of Author response image 1 represents the interpenetration). In the revised manuscript, we have made the necessary change from “soft cells” to “soft disks.”

Author response image 1.

Snapshots of zebrafish tissue (left panel) (Ref. [14] main text) and model two dimensional tissue (right). In the right panel the white area represents the overlap and the black vertical line represents the intersection.

“The facilitation mechanism, invoked in glassy systems [22] allows large cells to move with low mobility.” What is the facilitation mechanism?

Facilitation, which is an intuitive idea, that refers to a mechanism by which cells in a in highly jammed environment can only move if the neighboring cells get out of the way. In our case (as shown in the text (Fig.3 (A) and Fig. 13 (A) & (B)) the smaller cells move faster almost independent of ϕ. When a small cell moves, it creates a void which could facilitate neighboring cells (including big ones) to move.

“η (or relaxation time)” I suggest explaining the link between η and the relaxation time.

First, in making this point on aging we only showed that the relaxation time is independent of the waiting time. In the revised manuscript we deleted η.

Although not germane to this study, in the literature on glass transition, it is not uncommon to use relaxation time τα (as a proxy of viscosity η) to describe the dynamics. The relation between τα and η is given by

where G∞ is the “infinite frequency” shear modulus, which holds in unjammed or in liquids. This relation suggests that τα is proportional to η, which is almost never satisfied in glass forming systems.

P5 - “In addition, the elastic forces characterizing cell-cell interactions are soft, which implies that the cells can penetrate with rij − (Ri + Rj) < 0 when they are jammed.” Is this about the model or the biological tissue? Presumably the former, because real cells do not penetrate each other, right? What are rij, Ri and Rj?

This is about the model. The cells are sufficiently soft that they can be deformed, which allows for modest interpenetration. Real cells exhibit similar behavior (see Fig. 1). In inset of Fig. 4 (b) rij is the center to center distance between cells with radii Ri and Rj. It is better to use the word overlap instead of penetrate, which is what we have done in the revised version.

“we simulated a highly polydisperse system (PDs) in which the cell sizes vary by a factor of ∼ 8” Is it important to have a factor 8 - the zebra fish tissue presents a factor 5 − 6?

This is an important question, which is difficult to answer using analytic theory. It does require simulations unfortunately. We do not know a priori the polysipersity value needed to observe saturation in η at high value of ϕ. However, we have shown that the a system with one type of cell (monodisperse) crystallizes. Furthermore, mixtures of two cell types do not show any saturation in η over the parameter range that we explored. A systematic simulation study is needed to explore a range of parameter values to determine the minimum PD, which would match the experimental findings.

We performed 3D simulations to figure out if much less PD would yield saturation in η. Preliminary simulations in three dimensions with a lower value of PD (11.5% with a size variations by a factor of ≈ 2 ) exhibits saturation in the relaxation time. For comparison, the value of PD in the current work is ≈ 24% with a size variation by a factor of 8.

P6 -

“which is related to the Doolittle equation [26] for fluidity ( )” what is the Doolittle equation? Is it important here? Also: “VFT equation for cells”? Is it the same as given on p.2 - so nothing special for cells - or a different one?

Historically, the Doolittle equation was proposed to describe the change in η in terms of free volume in the context polymer systems over 60 years ago. The physics in the polymers is very different from the soft models for cells considered here. Nevertheless, the equations has meaning in the context as well. The Doolittle (other names associated with similar equations are Ferry, Flory... ) equation is given by

, where A and B are constants, V is the total volume and Vhc is the hardcore volume. Essentially, is the relative free volume. It can be shown that one can arrive at the VFT equation starting from the Doolittle equation.

The VFT equation for cells is same as given in page 2, which we restate for completeness. Here, we introduce the apparent activation energy.

“The stress-stress tensor” Why not simply stress tensor?

We have corrected it.

“shows qualitatively the same behavior as the estimate of viscosity (using dimensional arguments) made in experiments.” Where is this shown?

The dependence of viscosity as a function ϕ is shown in Figure 1 (c).

P7 -

Fig 2A caption “dashed line” Maybe full line?

This should be full line. It is fixed in in the revised manuscript.

P8 -

“a puzzling finding that is also reflected” Why is it puzzling?

In figure 2 (C), it shows that the increase in the duration in the plateau of Fs(q,t) ceases when ϕ exceeds ≈ 0.90. This to us is puzzling (always a matter of perspective) because we expected that the duration of Fs(q,t) plateau to increase as a function of ϕ based on the VFT behavior for ϕ ≤ ϕS. As a result, we imagined that the relaxation time τα would continue to increase beyond ϕS. However, the simulations show that the relaxation time is essentially a constant for ϕ > 0.90, which implies that the soft disk system (our model for the tissue) is an unusual with behavior that has no counter part in the material world.

“If the VFT relation continues” –“If the VFT relation continued”

We have fixed it.

First paragraph does not seem to be coherent

What is RS (or Rs)?

RS is the radius of the small cell. In the revised manuscript we have made this clear.

P10 -

Please, define the waiting time.

The waiting time refers to the period between sample preparation and data collection either in experiments or in simulations. In an ergodic system, the properties should not depend on the waiting time provided provided it is large. In other words, after the system reaches thermal equilibrium, the waiting time tω should not have an impact on the properties of the system.

“fully jammed” Please, define.

The term “fully jammed” refers to a state in which the constituent particles in a system do not move. For example, it a hard sphere system at a packing fraction of approximately 0.84 is fully jammed, which implies there is wiggle room for a particle move without violating the excluded volume restriction. At this specific packing fraction, the hard sphere system undergoes a jamming transition, resulting in the particles becoming completely immobile. The nonconfluent tissue modeled here is not fully jammed.

P11 -

Fig.4 it is hard to see that the width of P(hij) increases with ϕ.

Please see Author response image 2 with a less number of curves for a better visualization. We have replaced this figure in the revised version.

Author response image 2.

Probability of overlap (hij) between two cells, P(hij), for various ϕ values.

“Thus, even if the cells are highly jammed at ϕ ≈ ϕS, free area is available because of an increase in the overlap between cells.” This conclusion seems premature at this point.

The Referee is correct. This is shown in Fig. 5. We amended the ends of the sentence to reflect this observation.

P12 -

“as is the case when the extent of compression increases” extent of compression = density?

This is correct. Extent of compression corresponds to the packing fraction or the density.

“This effect is expected to occur with high probability at ϕS and beyond,” Why? What is special about ϕS.

To achieve high packing fractions beyond a certain value of ϕ soft cells have, which would occur at a certain value ϕS. In the system studied here, ϕ ≈ 0.90 = ϕS. Note that ϕS could be altered by changing the system parameters.

P15 -

“local equilibrium” In a thermodynamic sense? There is also cell migration, so thermodynamic equilibrium does not seem to be appropriate.

This is an important point. The observation that equilibrium concepts hold in what is manifestly a non-equilibrium system is a surprise. It is referred in a thermodynamic sense. We agree with the reviewer because of cell division (in Ref. [14] main text), cell death, thermodynamic equilibrium does not seems to be appropriate. This is exactly the point we raise in the introduction. However, considering the timescale of cell division and death it appears that there may be a local steady state, which we we call a “local equilibrium”. As a consequence phase transition ideas and Green-Kubo relations are applicable. Indeed, a surprise in the conclusion in Ref. [14] is that in the zebrafish morphogenesis equilibrium description seems adequate.

“number of near neighbor cells that is in contact with the ith cell. The jth cell is the nearest neighbor of the ith cell, if hij > 0” A neighbour cell or the nearest neihbor?

A neighbour cell is accurate.

P16 -

“In our model there is no dynamics with only systematic forces because the temperature is zero.” What is a systematic force? I do not understand the sentence.

Systematic force between two cells is defined in Eqn. 5 in the main text. Because temperature is not a relevant variable in our model, we want to emphasize that in the absence of self propulsion, the cells would not move at all.

Reviewer #2

Major comments:

A/ Role of size polydispersity

In the text, and also in the methods (Appendix A), the authors mention that they need large polydispersity of particle sizes to explain the viscous plateau, as the dynamics of small vs large cells are ”dramatically different” (Appendix G). They simulate a system where cell sizes vary by a factor 8, mentioning this is typical in tissues, but I found this quite surprising - this would be heterogeneities in cell volume of 500, many orders of magnitude above what has been measured in tissues. As far as I’m aware, divisions are quite symmetric and synchronous in early vertebrate embryogenesis, so volume variations are expected to be very small (similarly in epithelial tissues, where jamming has been looked at extensively, I’m not aware of examples with ratio of 8 between cell diameters). One question I had is that when the authors look at ”small polydispersity”, there are 50 − 50 mixtures. Would small polydispersity with continuous distributions change this picture? Could they take their current simulations but smoothly change the ratio of polydispersity from 8 to 0 to see exactly how much they need to explain viscosity plateauing, and at which point is the transition?

We thank the reviewer for raising this important question, which was also a concern for Reviewer #1. The value of polydispersity (PD) required to observe such behavior is not known a priori even within the simple model used. We selected a PD value, with a size variation of a factor of 8, guided in part by the experiment (projection onto 2D) shown in Figure 1(B) and Figure 6(D). We also showed that the monodisperse system crystallizes, and the binary system do not show signs of saturation within the explored range of parameter space and ϕ. This suggests that a certain degree of size dispersity is necessary to obtain saturation in η.

As discussed in Appendix B, the binary system is characterized by the variables , where RB and RS represent the radii of the big and small cells, respectively, and the packing fraction ϕ. By more fully exploring the parameter space encompassing λ and ϕ than we did, it maybe possible, as the Referee suggests, that a system with two different cell sizes would yield the experimentally observed dependence of η on ϕ.

As part of an answer to the Reviewer #1 on a the same issue, we mentioned results of preliminary simulations in three dimensions with reduced levels of polydispersity, and discovered that at lower levels of polydispersity (variation in size by a factor of ≈ 2 and polydispersity value 11.50%), the relaxation time does saturate beyond a certain packing fraction (see Fig. 3). We have not established if η, the key quantity of interest, would exhibit a similar behavior in 3D.

Author response image 3.

(A) τα as a function of ϕ for 11% polydispersity with size variation by a factor of ∼ 2 in the three dimensional system. (B) Same as (A) except polydispersity value is 24% and a size variation by a factor of ∼ 8.

B/ Role of fluctuations/self-propulsion in this system, and relationship to recent findings

“A priori it is unclear why equilibrium concepts should hold in zebrafish morphogenesis, which one would expect is controlled by non-equilibrium processes such as self-propulsion, growth and cell division. ”

This is raised as a key paradox, but is not very clear to me in the context raised by the authors. In particular, they use self-propulsion as a source of activity and explain the evolution of viscosity but a facilitation process involving re-arrangements/motility. But I don’t think self-propulsion has been argued to play a role in zebrafish blastoderm - Ref 14 argues that this is effectively a zerotemperature phenomenon and that cell motility/rearrangements do not show any correlation with viscosity. So this part of the model assumption was not clear to me in relationship with the proposed experimental system. Active noise has been proposed to play key roles in other systems, including motility-driven and tension fluctuation-driven unjamming (among many others Bi et al, PRX, 2016, Mitchel et al, Nat Comm, 2020, Pinheiro et al, Nat Phys, 2022 as well as Kim & Campas, Nat Physics, 2021) - maybe this is somewhere where the author model could fit? In Kim & Campas, Nat Phys, 2021 in particular, the authors develop simulations of non-confluent tissues with noise, that seems to bear some resemblance to the model developed here, so it would be important to discuss the similarities and distinctions (usually I think polydispersity is not considered indeed). In general, the authors look here at a particle based model, but cells have adhesions with well-defined contact angles, so there is a question of the cross-over between their findings and the large body of recent literature on active foams/vertex models (which are not really discussed there).

We appreciate the lengthy comment here, and there is a lot to unpack. We also thank the referee for the references, some of which we did not know about earlier.

The primary objective of our study is to determine the simplest minimal model that would explain the experimentally observed dependence of viscosity in zebrafish blastoderm tissue as ϕ is increased beyond a certain packing fraction during morphogenesis. In Reference 14, the authors analyzed the data using the framework of rigidity percolation theory and presented evidence of a genuine equilibrium phase transition. Consequently, one would that expect zebrafish blastoderm tissue to be in equilibrium, which is surprising from many perspectives. However, since the tissue is a growing system involving numerous cell divisions and cell death, it is not immediately evident whether the assumption of equilibrium is valid. Indeed, the same problem arises when considering the glass transition where rapid cooling drives the system out of equilibrium. Nevertheless, heat capacity and η are often analyzed using the notion of equilibrium. Hence, considering this issue within the context of our research appears to be reasonable.

To the best of our knowledge, the authors in Ref. 14 did not provide an explanation for the η behavior. The focus was, which was excellent and is the basis on which we initiated this study, was on the use of rigidity percolation theory to explain the results. Indeed, they performed an experiment by mildly reducing myosin II activity, which apparently affects cell motility. The quantitative effect was not reported.

We did not impose any requirement of cell rearrangements etc in the model. There is essentially one variable, free area available, that explains the η dependence on ϕ. It is possible that one can come up with other zero temperature models that could also explain the data. To the best of our knowledge, it has not been proposed.

It would be interesting to set our model in the context of other models that the referee points out. This would be an interesting research topic to explore. The only comment we would like to make is that it is unclear how vertex model for confluent tissues could explain the viscosity data.

C/ Calculation of the effective shear viscosity

The authors calculate viscosity from a Green-Kubo relation, although it would be good to clarify at which time scale (and maybe even shear amplitude) they expect this to be valid. These kinds of model would be expected to show plastic rearrangements for large deformations for instance, could the authors simulate realistic rheological deformations (e.g. Kim & Campas, 2021 applying external shear on the simulations) to see how much this matches both their expectation and the data?

Once it is established that there is local equilibrium (as implied by the use of phase transition ideas to analyse the experimental data in Ref. 14), it is natural to use the Green-Kubo relation to calculate transport properties. Hence, for our purposes, it is valid for all time scales and amplitude. The Reviewer also wonders if the model could be used to simulate response to shear in order to probe rheological properties. There is no conceptual issue here and indeed this is an excellent suggestion that we intend to pursue in the future.

D/ Role of cell adhesion

The authors consider soft elastic disks of different sizes but unless I missed it, there is no adhesion being considered. This is expected to play a key role in jamming and multicellular mechanics, so I think the authors should either look at what this changes in their simulations, or at least discuss why they are neglecting it. One reason I’m asking is that it’s not totally clear to me that the ”free space” picture, coming from the fact that cells can interpenetrate in their model would hold in a model of deformable cells adhering to each other with constant volume (leading to more equilibration of deformations it would seem?).

The referee raises another question regarding the lack of adhesion in the simulations. As pointed out before, we were trying to create a minimal model to account for the experimental observations for η upon changing the packing fraction. Thus, we a coarse-grained model where we considered poly-disperse cells with elastic interactions which recapitulates the experimental observations. The referee is correct that adhesion plays a role in jammed systems, and examination of how it would affect is an aspect that would be interesting to consider in the future. We hasten to add that even systems without attractive adhesion-type interaction become jammed. In principle, in many-body systems, the parameter space is large and one needs to carefully determine which parameter is important for the problem at hand. Therefore, in the first pass we did not find the need to consider the role of adhesion.

Minor comments:

The writing could be condensed in some places, with some details being moved to SI (for instance, section E on ageing is very short and seem more suited for supplements, or at least not as an independent section, note that the figure numbering also jumps to Fig. 9 there, although it’s Fig. 3 just before and Fig. 9 just after - re-ordering into main and supporting figures would be clearer.

We thank the Reviewer for this recommendation. The ageing section, although is short, it does provide a line of evidence that equilibrium approaches could be valid. We have modestly expanded the section by moving Appendix D to the main text, a general suggestion made by Referee 1. We have tried to be consistent in the numbering of figures in the revision.

Reviewer #3

I am very much in favor of the manuscript in its present form - I only suggest commenting (in the manuscript) on the issue described below.

Motivated by the fact that the experimental system consists of living, motile cells the authors use an active particle model (eq. 6) with stochastic selfpropulsion as the only source for noise (zero-temperature). It would be useful to elaborate briefly how important this stochastic self-propulsion is for the emergent rheological properties of the system (as summarized above): would these properties also be present in the “passive” version of the same model at “non-vanishing” temperature, and if not, why? Or analogously in a “passive” version which is “shaken”, reminiscent of shaken granular matter? To clarify these issues would relate this study to (or discriminate it from) passive, but complex, liquids or granular matter.

We appreciate the reviewer’s positive feedback on our work. The reviewer has raised an important question concerning our model in which self-propulsion serves as the source of noise. Without self-propulsion, the system would come to a stationary state after reaching mechanical equilibrium. As mentioned in Eqn. (6) (in the main text), we can define a characteristic time . It is possible that scaling the time t by τ would not alter the results.

The second question raised by the reviewer is also important. A passive version of the model would be to consider Eq. 6 in our article, and instead of using activity use the standard stochastic force. The resulting force would be at a finite temperature,. The coefficient of noise (a diffusion term) would be related to γi through the Fluctuation dissipation theorem(FDT)). Such a system of equations cannot ne mapped to Eq. 6 in which µ and γi are independently varied. It is unlikely that such a model, incorporating a “non-vanishing” temperature, would not result in the observed dependence of η on ϕ for the following reason. The passive model represents a polydisperse system, which would form a glass with η increasing with volume fraction, following the VFT law, as has been demonstrated in the glass transition literature for harmonic glasses. The other proposal whether the shaken version version would explain the experiments is also interesting. These are worth pursuing in future studies.

Author response:

The following is the authors’ response to the current reviews.

Public Reviews:

Reviewer #1 (Public review):

Summary:

Zanetti et al use biophysical and cellular assays to investigate the interaction of the birnavirus VP3 protein with the early endosome lipid PI3P. The major novel finding is that association of the VP3 protein with an anionic lipid (PI3P) appears to be important for viral replication, as evidenced through a cellular assay on FFUs.

Strengths:

Support previously published claims that VP3 associates with early endosome membrane, potentially through binding to PI3P. The finding that mutating a single residue (R200) critically affects early endosome binding and that the same mutation also inhibits viral replication suggests a very important role for this binding in the viral life cycle.

Weaknesses:

The manuscript is relatively narrowly focused: the specifics of the bi-molecular interaction between the VP3 of an unusual avian virus and a host cell lipid (PIP3). Further, the affinity of this interaction is low and its specificity relative to other PIPs is not tested, leading to questions about whether VP3-PI3P binding is relevant.

Regarding the manuscript’s focus, we challenge the notion that studying a single bi-molecular interaction makes the scope of the paper overly narrow. This interaction—between VP3 and PI3P—plays a critical role in the replication of the birnavirus, which is the central theme of our work. Moreover, identifying and understanding such distinct interactions is a fundamental aspect of molecular virology, as they shed light on the precise mechanisms that viruses exploit to hijack the host cell machinery. Consequently, far from being narrowly focused, we believe our work contributes to the broader understanding of host-pathogen interactions.

As for the low affinity of the VP3-PI3P interaction, we argue that this is not a limitation but rather a biologically relevant feature. As discussed in the manuscript, the moderate strength of this interaction is likely critical for regulating the turnover rate of VP3/endosomal PI3P complexes, which in turn could optimize viral replication efficiency. A stronger affinity might trap VP3 on the endosomal membrane, whereas weaker interactions might reduce its ability to efficiently target PI3P. Thus, the observed affinity may reflect a fine-tuned balance that supports the viral life cycle.

With regard to specificity, we emphasize that in the context of the paper, we refer to biological specificity, which is not necessarily the same as chemical specificity. The binding of PI3P to early endosomes is “biologically” preconditioned by the distribution of PI3P within the cell. PI3P is predominantly localized in endosomal membranes, which “biologically precludes” interference from other PIPs due to their distinct cellular distributions. Moreover, while early endosomes also contain other anionic lipids, our work demonstrates that among these, PI3P plays a distinctive role in VP3 binding. This highlights its functional relevance in the context of early endosome dynamics.

Reviewer #3 (Public review):

Summary:

Infectious bursal disease virus (IBDV) is a birnavirus and an important avian pathogen. Interestingly, IBDV appears to be a unique dsRNA virus that uses early endosomes for RNA replication that is more common for +ssRNA viruses such as for example SARS-CoV-2. This work builds on previous studies showing that IBDV VP3 interacts with PIP3 during virus replication. The authors provide further biophysical evidence for the interaction and map the interacting domain on VP3.

Strengths:

Detailed characterization of the interaction between VP3 and PIP3 identified R200D mutation as critical for the interaction. Cryo-EM data show that VP3 leads to membrane deformation.

We thank the reviewer for the feedback.

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

Zanetti et al. use biophysical and cellular assays to investigate the interaction of the birnavirus VP3 protein with the early endosome lipid PI3P. The major novel finding is that the association of the VP3 protein with an anionic lipid (PI3P) appears to be important for viral replication, as evidenced through a cellular assay on FFUs.

Strengths:

Supports previously published claims that VP3 may associate with early endosomes and bind to PI3P-containing membranes. The claim that mutating a single residue (R₂₀₀) critically affects early endosome binding and that the same mutation also inhibits viral replication suggests a very important role for this binding in the viral life cycle.

Weaknesses:

The manuscript is relatively narrowly focused: one bimolecular interaction between a host cell lipid and one protein of an unusual avian virus (VP3-PI3P). Aspects of this interaction have been described previously. Additional data would strengthen claims about the specificity and some technical issues should be addressed. Many of the core claims would benefit from additional experimental support to improve consistency.

Indeed, our group has previously described aspects of the VP3-PI3P interaction, as indicated in lines 100-105 from the manuscript. In this manuscript, however, we present biochemical and biophysical details that have not been reported before about how VP3 connects with early endosomes, showing that it interacts directly with the PI3P. Additionally, we have now identified a critical residue in VP3—the R₂₀₀—for binding to PI3P and its key role in the viral life cycle. Furthermore, the molecular dynamics simulations helped us come up with a mechanism for VP3 to connect with PI3P in early endosomes. This constitutes a big step forward in our understanding of how these "non-canonical" viruses replicate.

We have now incorporated new experimental and simulation data; and have carefully revised the manuscript in accordance with the reviewers’ recommendations. We are confident that these improvements have further strengthened the manuscript.

Reviewer #2 (Public Review):

Summary:

Birnavirus replication factories form alongside early endosomes (EEs) in the host cell cytoplasm. Previous work from the Delgui lab has shown that the VP3 protein of the birnavirus strain infectious bursal disease virus (IBDV) interacts with phosphatidylinositol-3-phosphate (PI3P) within the EE membrane (Gimenez et al., 2018, 2020). Here, Zanetti et al. extend this previous work by biochemically mapping the specific determinants within IBDV VP3 that are required for PI3P binding in vitro, and they employ in silico simulations to propose a biophysical model for VP3-PI3P interactions.

Strengths:

The manuscript is generally well-written, and much of the data is rigorous and solid. The results provide deep knowledge into how birnaviruses might nucleate factories in association with EEs. The combination of approaches (biochemical, imaging, and computational) employed to investigate VP3-PI3P interactions is deemed a strength.

Weaknesses:

(1) Concerns about the sources, sizes, and amounts of recombinant proteins used for co-flotation: Figures 1A, 1B, 1G, and 4A show the results of co-flotation experiments in which recombinant proteins (control His-FYVE v. either full length or mutant His VP3) were either found to be associated with membranes (top) or non-associated (bottom). However, in some experiments, the total amounts of protein in the top + bottom fractions do not appear to be consistent in control v. experimental conditions. For instance, the Figure 4A western blot of His-2xFYVE following co-flotation with PI3P+ membranes shows almost no detectable protein in either top or bottom fractions.

Liposome-based methods, such as the co-flotation assay, are well-established and widely regarded as the preferred approach for studying protein-phosphoinositide interactions. However, this approach is rather qualitative, as density gradient separation reveals whether the protein is located in the top fractions (bound to liposomes) or the bottom fractions (unbound). Our quantifications aim to demonstrate differences in the bound fraction between liposome populations with and without PI3P. Given the setting of the co-flotation assays, each protein-liposome system [2xFYVE-PI3P(-), 2xFYVE-PI3P(+), VP3-PI3P(-), or VP3-PI3P(+)] is assessed separately, and even if the experimental conditions are homogeneous, it is not surprising to observe differences in the protein level between different experiments. Indeed, the revised version of the manuscript includes membranes with more similar band intensities, as depicted in the new versions of Figures 1 and 4.

Reading the paper, it was difficult to understand which source of protein was used for each experiment (i.e., E. coli or baculovirus-expressed), and this information is contradicted in several places (see lines 358-359 v. 383-384). Also, both the control protein and the His-VP3-FL proteins show up as several bands in the western blots, but they don't appear to be consistent with the sizes of the proteins stated on lines 383-384. For example, line 383 states that His-VP3-FL is ~43 kDa, but the blots show triplet bands that are all below the 35 kDa marker (Figures 1B and 1G). Mass spectrometry information is shown in the supplemental data (describing the different bands for His-VP3-FL) but this is not mentioned in the actual manuscript, causing confusion. Finally, the results appear to differ throughout the paper (see Figures 1B v. 1G and 1A v. 4A).

Thank you for pointing out these potentially confusing points in the previous version of the manuscript. Indeed, we were able to produce recombinant VP3 from the two sources: Baculovirus and Escherichia coli. Initially, we opted for the baculovirus system, based on evidence from previous studies showing that it was suitable for ectopic expression of VP3. Subsequently, we successfully produced VP3 using Escherichia coli. On the other side, the fusion proteins His-2xFYVE and GST-2xFYVE were only produced in the prokaryotic system, also following previous reported evidence. We confirmed that VP3, produced in either system, exhibited similar behavior in our co-flotation and bio-layer interferometry (BLI) assays. However, the results of co-flotation and BLI assays shown in Figs. 1 and 4 were performed using the His-VP3 FL, His-VP3 FL R₂₀₀D and His-VP3 FL DCt fusion proteins produced from the corresponding baculoviruses. We have clarified this in the revised version of our manuscript. Please, see lines 430-432.

Additionally, we have made clear that the His-VP3 FL protein purification yielded four distinct bands, and we confirmed their VP3 identity through mass spectrometry in the revised version of the manuscript. Please, see lines 123-124.

Finally, we replaced membranes for Figs. 4A and 1G (left panel) with those with more similar band intensities. Please, see the new version of Figures 1 and 4.

(2) Possible "other" effects of the R₂₀₀D mutation on the VP3 protein. The authors performed mutagenesis to identify which residues within patch 2 on VP3 are important for association with PI3P. They found that a VP3 mutant with an engineered R₂₀₀D change (i) did not associate with PI3P membranes in co-floatation assays, and (ii) did not co-localize with EE markers in transfected cells. Moreover, this mutation resulted in the loss of IBDV viability in reverse genetics studies. The authors interpret these results to indicate that this residue is important for "mediating VP3-PI3P interaction" (line 211) and that this interaction is essential for viral replication. However, it seems possible that this mutation abrogated other aspects of VP3 function (e.g., dimerization or other protein/RNA interactions) aside from or in addition to PI3P binding. Such possibilities are not mentioned by the authors.

The arginine amino acid at position 200 of VP3 is not located in any of the protein regions associated with its other known functions: VP3 has a dimerization domain located in the second helical domain, where different amino acids across the three helices form a total of 81 interprotomeric close contacts; however, R₂₀₀ is not involved in these contacts (Structure. 2008 Jan;16(1):29-37, doi:10.1016/j.str.2007.10.023); VP3 has an oligomerization domain mapped within the 42 C-terminal residues of the polypeptide, i.e., the segment of the protein composed by the residues at positions 216-257 (J Virol. 2003 Jun;77(11):6438–6449, doi: 10.1128/jvi.77.11.6438-6449.2003); VP3’s ability to bind RNA is facilitated by a region of positively-charged amino acids, identified as P1, which includes K₉₉, R₁₀₂, K₁₀₅, and K₁₀₆ (PLoS One. 2012;7(9):e45957, doi: 10.1371/journal.pone.0045957). Furthermore, our findings indicate that the R₂₀₀D mutant retains a folding pattern similar to the wild-type protein, as shown in Figure 4B. All these lead us to conclude that the loss of replication capacity of R₂₀₀D viruses results from impaired, or even loss of, VP3-PI3P interaction.

We agree with the reviewer that this is an important point and have accordingly addressed it in the Discussion section of the revised manuscript. Please, see lines 333-346.

(3) Interpretations from computational simulations. The authors performed computational simulations on the VP3 structure to infer how the protein might interact with membranes. Such computational approaches are powerful hypothesis-generating tools. However, additional biochemical evidence beyond what is presented would be required to support the authors' claims that they "unveiled a two-stage modular mechanism" for VP3-PI3P interactions (see lines 55-59). Moreover, given the biochemical data presented for R₂₀₀D VP3, it was surprising that the authors did not perform computational simulations on this mutant. The inclusion of such an experiment would help tie together the in vitro and in silico data and strengthen the manuscript.

We acknowledge that the wording used in the previous version of the manuscript may have overstated the "unveiling" of the two-stage binding mechanism of VP3. Our intention was to propose a potential mechanism, that is consistent both with the biophysical experiments and the molecular simulations. In the revised version of the manuscript, we have tempered these claims and framed them more appropriately.

Regarding the simulations for the R₂₀₀D VP3 mutant, these simulations were indeed performed and included in the original manuscript as part of Figure S14 in the Supplementary Information. However, we realize that this was not sufficiently emphasized in the main text, an oversight on our part. We have now revised the manuscript to highlight these results more clearly.

Additionally, to further strengthen the connection between experimental and simulation trends, we have now included a new figure in the Supplementary Information (Figure S15). This figure depicts the binding energy of VP3 ΔNt and two of its mutants, VP3 ΔNt R₂₀₀D and VP3 ΔNt P2 Mut, as a function of salt concentration. The results show that as the number of positively charged residues in VP3 is systematically reduced, the binding of the protein to the membrane becomes weaker. The effect is more pronounced at lower salt concentrations, which highlights the weight of electrostatic forces on the adsorption of VP3 on negatively charged membranes. Please, see Supplementary Information (Figure S15).

Reviewer #3 (Public Review):

Summary:

Infectious bursal disease virus (IBDV) is a birnavirus and an important avian pathogen. Interestingly, IBDV appears to be a unique dsRNA virus that uses early endosomes for RNA replication that is more common for +ssRNA viruses such as for example SARS-CoV-2.

This work builds on previous studies showing that IBDV VP3 interacts with PIP3 during virus replication. The authors provide further biophysical evidence for the interaction and map the interacting domain on VP3.

Strengths:

Detailed characterization of the interaction between VP3 and PIP3 identified R₂₀₀D mutation as critical for the interaction. Cryo-EM data show that VP3 leads to membrane deformation.

Weaknesses:

The work does not directly show that the identified R₂₀₀ residues are directly involved in VP3-early endosome recruitment during infection. The majority of work is done with transfected VP3 protein (or in vitro) and not in virus-infected cells. Additional controls such as the use of PIP3 antagonizing drugs in infected cells together with a colocalization study of VP3 with early endosomes would strengthen the study.

In addition, it would be advisable to include a control for cryo-EM using liposomes that do not contain PIP3 but are incubated with HIS-VP3-FL. This would allow ruling out any unspecific binding that might not be detected on WB.

The authors also do not propose how their findings could be translated into drug development that could be applied to protect poultry during an outbreak. The title of the manuscript is broad and would improve with rewording so that it captures what the authors achieved.

In previous works from our group, we demonstrated the crucial role of the VP3 P2 region in targeting the early endosomal membranes and for viral replication, including the use of PI3K inhibitors to deplete PI3P, showing that both the control RFP-2xFYVE and VP3 lost their ability to associate with the early endosomal membranes and reduces the production of an infective viral progeny (J Virol. 2018 May 14;92(11):e01964-17, doi: 10.1128/jvi.01964-17; J Virol. 2021 Feb 24;95(6):e02313-20, doi: 10.1128/jvi.02313-20). In the present work, to further characterize the role of R₂₀₀ in binding to early endosomes and for viral replication, we show that: i) the transfected VP3 R₂₀₀D protein loses the ability to bind to early endosomes in immunofluorescence assays (Figure 2E and Figure 3); ii) the recombinant His-VP3 FL R₂₀₀D protein loses the ability to bind to liposomes PI3P(+) in co-flotation assays (Figure 4A); and, iii) the mutant virus R₂₀₀D loses replication capacity (Figure 4C).

Regarding the cryo-electron microscopy observation, we verified that there is no binding of gold particles to liposomes PI3P(-) when they are incubated solely with the gold-particle reagent, or when they are pre-incubated with the gold-particle reagent with either His-2xFYVE or His-VP3 FL. We have incorporated a new panel in Figure 1C showing a representative image of these results. Please, see lines 143-144 in the revised version of our manuscript and our revised version of Figure 1C.

We have replaced the title of the manuscript by a more specific one. Thus, our current is " On the Role of VP3-PI3P Interaction in Birnavirus Endosomal Membrane Targeting".

Regarding the question of how our findings could be translated into drug development, indeed, VP3-PI3P binding constitutes a good potential target for drugs that counteract infectious bursal disease. However, we did not mention this idea in the manuscript, first because it is somewhat speculative and second because infected farms do not implement any specific treatment. The control is based on vaccination.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Critical issues to address:

(1) The citations in the important paragraph on lines 101-5 are not identifiable. These references are described as showing that VP3 is associated with EEs via P2 and PI3P, which is basically what this paper also shows. The significant advance here is unclear.

We apologize for this mistake. These citations are identifiable in the revised version of the manuscript (lines 100-105). As mentioned before, in this manuscript we present biochemical and biophysical details that have not been reported before about how VP3 connects with early endosomes, showing that it interacts directly with the PI3P. Additionally, we have now identified a critical residue in VP3 P2—the R₂₀₀—for binding to PI3P and its key role in the viral life cycle. Furthermore, the molecular dynamics simulations helped us come up with a mechanism for VP3 to connect with PI3P in early endosomes. This constitutes a big step forward in our understanding of how these "non-canonical" viruses replicate.

(2) Even if all the claims were to be clearly supported through major revamping, authors should make the significance of knowing that this protein binds to early endosomes through PI3P more clear?

Thank you for the recommendation, which aligns with a similar suggestion from Reviewer #2. In response, we have revised the significance paragraph to emphasize the mechanistic aspects of our findings. Please refer to lines 62–67 in the revised manuscript.

(3) Flotation assay shows binding, but this is not quantitative. An estimate of a Kd would be useful. BLI experiments suggest that half of the binding disappears at 0.5 mM, implying a very low binding affinity.

We agree with the reviewer that our biophysical and molecular simulation results suggest a specific but weak interaction of VP3 with PI3P bearing membranes. Indeed, our previous version of the manuscript already contained a paragraph in this regard. Please, see lines 323-332 in the revised version of the manuscript.

From a biological point of view, a low binding affinity of VP3 for the endosomes may constitute an advantage for the virus, in the sense that its traffic through the endosomes may be short lived during its infectious cycle. Indeed, VP3 has been demonstrated to be a "multifunctional" protein involved in several processes of the viral cycle (detailed in lines 84-90), and in our laboratory we have shown that the Golgi complex and the endoplasmic reticulum are organelles where further viral maturation occurs. Taking all of this into account, a high binding affinity of VP3 for endosomes could result in the protein becoming trapped on the endosomal membrane, potentially hindering the progression of the viral infection within the host cell.

(4) There are some major internal inconsistencies in the data: Figure 1B quantifies VP3-FL T/B ratio ~4 (which appears inconsistent with the image shown, as the T lanes are much lighter than the B) whereas apparently the same experiment in Figure 1G shows it to be ~0.6. With the error bars shown, these results would appear dramatically different from each other, despite supposedly measuring the same thing. The same issue with the FYVE domain between Figures 1A and 4A.

We appreciate the reviewer’s comment, as it made us aware of an error in Figure 1B. There, the mean value for the VP3-FL Ts/B ratio is 3.0786 for liposomes PI3P(+) and 0.4553 for liposomes PI3P(-) (Please, see the new bar graph on Figure 1B). This may have occurred because, due to the significance of these experiments, we performed multiple rounds of quantification in search of the most suitable procedure for our observations, leading to a mix-up of data sets. Anyway, it’s possible that these corrected values still seem inconsistent given that T lanes are much lighter than the B for VP3-FL in the image shown. Flotation assays are quite labor-intensive and, at least in our experience, yield fairly variable results in terms of quantification. To illustrate this point, the following image shows the three experiments conducted for Figure 1B, where it is clear that, despite producing visually distinct images, all three yielded the same qualitative observation. For Figure 1B, we chose to present the results from experiment #2. However, all three experiments contributed to a Ts/B ratio of 3.0786 for His-VP3 FL, which may account for the apparent inconsistency when focusing solely on the image in Figure 1B.

Author response image 1.

We acknowledge that, at first glance, some inconsistencies may appear in the results, and we have thoroughly discussed the best approach for quantification. However, we believe the observations are robust in terms of reproducibility and reliable, as the VP3-PI3P interaction was consistently validated by comparison with liposomes lacking PI3P, where no binding was observed.

(5) Comparison of PA (or PI) to PI3P at the same molar concentration is inappropriate because PI3P has at least double charge. The more interesting question about specificity would be whether PI45P2 (or even better PI35P2) binds or not. Without this comparison, no claim to specificity can be made.

For us, "specificity" refers to the requirement of a phosphoinositide in the endosomal membrane for VP3 binding. Phosphoinositides have a conspicuous distribution among cellular compartments, and knowing that VP3 associates with early endosomes, our specificity assays aimed to demonstrate that PI3P is strictly required for the binding of VP3. To validate this, we used PI (lacking the phosphate group) and PA (lacking the inositol group) despite their similar charges. In spite of the potential chemical interactions between VP3 and various phosphoinositides, our experimental results suggest that the virus specifically targets endosomal membranes by binding to PI3P, a phosphoinositide present only in early endosomes.

That said, we agree with the reviewer’s point and consider adequate to smooth our specificity claim in the manuscript as follows: “We observed that His-VP3 FL bound to liposomes PI3P(+), but not to liposomes PA or PI, reinforcing the notion that a phosphoinositide is required since neither a single negative charge nor an inositol ring are sufficient to promote VP3 binding to liposomes (SI Appendix, Fig. S2)” (Lines 136-139).

(6) In the EM images, many of the gold beads are inside the vesicles. How do they cross the membranes?

They do not cross the membrane. Our EM images are two-dimensional projections, meaning that the gold particles located on top or beneath the plane appear to be inside the liposome.

(7) Images in Figure 2D are very low quality and do not show the claimed difference between any of the mutants. All red signal looks basically cytosolic in all images. It is not clear what criteria were used for the quantification in Figure 2E. The same issue is in Figure 2E, where no red WT puncta are observable at all. Consistently, there is minimal colocalization in the quantification in Figure S3, which appears to show no significant differences between any of the mutants, in direct contradiction to the claim in the manuscript.

We apologize for the poor quality of panels in Figures 2D and 2E. Unfortunately, this was due to the PDF conversion of the original files. Please, check the high-quality version of Figure 2. As suggested by reviewers #2 and #3, we have incorporated zoomed panels, which help the reader to better see the differences in distribution.

As mentioned in the legend to Figure 2, the quantification in Figure 2D was performed by calculating the percentage of cells with punctuated fluorescent red signal (showing VP3 distribution) for each protein. The data were then normalized to the P2 WT protein, which is the VP3 wild type.

Figure S3 certainly shows a tendency which positively correlates with the results shown in Figure 3, where we used FYVE to detect PI3P on endosomes and observed significantly less co-localization when VP3 bears its P2 region all reversed or lacks the R₂₀₀

(8) The only significant differences in colocalization are in Figure 3B, whose images look rather dramatically different from the rest of the manuscript, leading to some concern about repeatability. Also, it is unclear how colocalization is quantified, but this number typically cannot be above 1. Finally, it is unclear what is being colocalized here: with three fluorescent components, there are 3 possible binary colocalizations and an additional ternary colocalization.

We thank the reviewer for pointing out those aspects related to Figure 3. The experiments performed for Figure 3B were conducted by a collaborator abroad handling the purified GST-2xFYVE, which recognizes endogenous PI3P, while the rest of the cell biology experiments were conducted in our laboratory in Argentina. This is why they are aesthetically different. We have made an effort in homogenizing the way they look for the revised version of the manuscript. Please, see the new version of Figure 3.

For quantification of the co-localization of VP3 and EGFP-2xFYVE (Figure 3A), the Manders M2 coefficient was calculated out of approximately 30 cells per construct and experiment. The M2 coefficient, which reflects co-localization of signals, is defined as the ratio of the total intensities of magenta image pixels for which the intensity in the blue channel is above zero to the total intensity in the magenta channel. JACoP plugin was utilized to determine M2. For VP3 puncta co-distributing with EEA1 and GST-FYVE (Figure 3B), the number of puncta co-distributing for the three signals was manually determined out of approximately 40 cells per construct and experiment per 200 µm². We understand that Manders or Pearson coefficients, typically ranging between 0 and 1, is the most commonly used method to quantify co-localizing immunofluorescent signals; however, this “manual” method has been used and validated in previous published manuscripts [Figures 3 and 7 from (Morel et al., 2013); Figure 7 in (Khaldoun et al., 2014); and Figure 4 in (Boukhalfa et al., 2021)].

(9) SegA/B plasmids are not introduced, and it is not clear what these are or how this assay is meant to work. Where are the foci forming units in the images of Figure 4C? How does this inform on replication? Again, this assay is not quantitative, which is essential here: does the R₂₀₀ mutant completely kill activity (whatever that is here)? Or reduce it somewhat?

We apologize for the missing information. Segments A and B are basically the components of the IBDV reverse genetics system. For their construction, we used a modification of the system described by Qi and coworkers (Qi et al., 2007), in which the full length sequences of the IBDV RNA segments A and B, flanked by a hammerhead ribozyme at the 5’-end and the hepatitis delta ribozyme at the 3’-end, were expressed under the control of an RNA polymerase II promoter within the plasmids pCAGEN.Hmz.SegA.Hdz (SegA) and pCAGEN.Hmz.SegB.Hdz (SegB). For this specific experiment we generated a third plasmid, pCAGEN.Hmz.SegA.R₂₀₀D.Hdz (SegA.R₂₀₀D), harboring a mutant version of segment A cDNA containing the R₂₀₀D substitution. Then, QM7 cells were transfected with the plasmids SegA, SegB or Seg.R₂₀₀D alone (as controls) or with a mixture of plasmids SegA+SegB (wild type situation) or SegA.R₂₀₀D+SegB (mutant situation). At 8 h post transfection (p.t.), when the new viruses have been able to assemble starting from the two segments of RNA, the cells were recovered and re-plated onto fresh non-transfected cells for revealing the presence (or not) of infective viruses. At 72 h post-plating, the generation of foci forming units (FFUs) was revealed by Coomassie staining. As expected, single-transfections of SegA, SegB or Seg.R₂₀₀D did not produce FFUs and, as shown in Figure 4C, the transfection of SegA+SegB produced detectable FFUs (the three circles in the upper panel) while no FFUs (the three circles in the lower panel) were detected after the transfection of SegA.R₂₀₀D+SegB (Figure 4C). This system is quantitative, since the FFUs detected 72 h post-plating are quantifiable by simply counting the FFUs. However, since no FFUs were detected after the transfection of SegA.R₂₀₀D+SegB, evidenced by a complete monolayer of cells stained blue, we did not find any sense in quantifying. In turn, this drastic observation indicates that viruses bearing the VP3 R₂₀₀D mutation lose their replication ability (is “dead”), demonstrating its crucial role in the infectious cycle.

We agree with the reviewer that a better explanation was needed in the manuscript, so we have incorporated a paragraph in the results section of our revised version of the manuscript (lines 209-219).

(10) Why pH 8 for simulation?

The Molecular Theory calculations were performed at pH 8 for consistency with the experimental conditions used in our biophysical assays. These biophysical experiments were also performed at pH 8, following the conditions established in the original study where VP3 was first purified for crystallization (DOI: 10.1016/j.str.2007.10.023).

(11) There is minimal evidence for the sequential binding model described in the abstract. The simulations do not resolve this model, nor is truly specific PI3P binding shown.

In response to your concerns, we would like to emphasize that our simulations provide robust evidence supporting the two more important aspects of the sequential binding model: 1) Membrane Approach: In all simulations, VP3 consistently approaches the membrane via its positively charged C-terminal (Ct) region. 2) PI3P Recruitment: Once the protein is positioned flat on the membrane surface, PI3P is unequivocally recruited to the positively charged P2 region. The enrichment of PI3P in the proximity to the protein is clearly observed and has been quantified via radial distribution functions, as detailed in the manuscript and supplementary material.

While we understand that opinions may vary on the sufficiency of the data to fully validate the model, we believe the results offer meaningful insights into the proposed binding mechanism. That said, we acknowledge that the specificity of VP3 binding may not be restricted solely to PI3P but could extend to phosphoinositides in general. To address this, we performed the new set of co-flotation experiments which are discussed in detail in our response to point 5.

Reviewer #2 (Recommendations For The Authors):

(1) Line 1: Consider changing the title to better reflect the mostly biochemical and computational data presented in the paper: "Mechanism of Birnavirus VP3 Interactions with PI3P-Containing Membranes". There are no data to show hijacking by a virus presented.

We appreciate this recommendation, which was also expressed by reviewer #3. Additionally, we thank for the suggested title. We have replaced the title of the manuscript by a more specific one. Thus, our current is

"On the Role of VP3-PI3P Interaction in Birnavirus Endosomal Membrane Targeting".

(2) Lines 53-54 and throughout: Consider rephrasing "demonstrate" to "validate" to give credit to Gimenez et al., 2018, 2022 for discovery.

Thanks for the suggestion. We have followed it accordingly. Please see line 52 from our revised version of the manuscript.

(3) Line 56-59 and throughout: Consider tempering and rephrasing these conclusions that are based mostly on computational data. For example, change "unveil" to "suggest" or another term.

We have now modified the wording throughout the manuscript.

(4) The abstract could also emphasize that this study sought to map the resides within VP3 that are important for P13P interaction.

Thanks for the suggestion. We have followed it accordingly. Please, see lines 53-55 from our revised version of the manuscript.

(5) Lines 63-69: This Significance paragraph seems tangential. The findings in this paper aren't at all related to the evolutionary link between birnaviruses and positive-strand RNA viruses. The significance of the work for me lies in the deep biochemical/biophysical insights into how a viral protein interacts with membranes to nucleate its replication factory.

We have re-written the significance paragraph highlighting the mechanistic aspect of our findings. Please, see lines 62-67 in our revised version of the manuscript.

(6) Line 74: Please define "IDBV" abbreviation.

We apologize for the missing information. We have defined the IBDV abbreviation in our revised version of the manuscript (please, see line 73).

(7) Line 88: Please define "pVP2" abbreviation.

We apologize for the missing information. We have defined the pVP2 abbreviation in our revised version of the manuscript (please, see line 87).

(8) Lines 101-105: Please change references (8, 9, 10) to be consistent with the rest of the manuscript (names, year).

We apologize for this mistake. These citations are identifiable and consistent in the revised version of the manuscript (lines 100-105).

(9) Line 125: For a broad audience, consider explaining that recombinant His-2xFYVE domain is known to exhibit PI3P-binding specificity and was used as a positive control.

Thanks for the recommendation. We have incorporated a brief explanation supporting the use of His-2xFYVE as a positive control in our revised version of the manuscript. Please, see lines 127-129.

(10) Lines 167-171: The quantitative data in Figure S3 shows that there was a non-significant co-localization coefficient of the R₂₀₀D mutant. For transparency, this should be stated in the Results section when referenced.

We agree with this recommendation. We have clearly mentioned it in the revised version of the manuscript. Please, see lines 177-179. Also, we have referred this fact when introducing the assays performed using the purified GST-2xFYVE, shown in Figure 3. Please, see lines 182-184.

(11) Lines 156 and 173: These Results section titles have nearly identical wording. Consider rephrasing to make it distinct.

We agree with the reviewer’s observation. In fact, we sought to do it on purpose as for them to be a “wordplay”, but we understand that could result in a awkwarded redundancy. So, in the revised version of the manuscript, both titles are:

Role of VP3 P2 in the association of VP3 with the EE membrane (line 163).

VP3 P2 mediates VP3-PI3P association to EE membranes (line 182).

(12) Line 194: Is it alternatively possible that the R₂₀₀D mutant lost its capacity to dimerize, and that in turn impacted PI3P interaction?

Thanks for the relevant question. VP3 was crystallized and its structure reported in (Casañas et al., 2008) (DOI: 10.1016/j.str.2007.10.023). In that report, the authors showed that the two VP3 subunits associate in a symmetrical manner by using the crystallographic two-fold axes. Each subunit contributes with its 30% of the total surface to form the dimer, with 81 interprotomeric close contacts, including polar bonds and van der Waals contacts. The authors identified the group of residues involved in these interactions, among which the R₂₀₀ is not included. Addittionally, the authors determined that the interface of the VP3 dimer in crystals is biologically meaningful (not due to the crystal packing).

To confirm that the lack of binding was not due to misfolding of the mutant, we compared the circular dichroism spectra of mutant and wild type proteins, without detecting significant differences (shown in Figure 4B). These observations do not exclude the possibility mentioned by the reviewer, but constitute solid evidences, we believe, to validate our observations.

(13) Lines 231-243: Consider changing verbs to past tense (i.e., change "is" to "was") for the purposes of consistency and tempering.

Thanks for the recommendation, we have proceeded as suggested. Please, see lines 249-262 in our revised version of the manuscript.

(14) Lines 306-308: Is there any information about whether it is free VP3 (v. VP3 complexed in RNP) that binds to membrane? I am just trying to wrap my head around how these factories form during infection.

Thanks for pointing this out. We first observed that in infected cell, all the components of the RNPs [VP3, VP1 (the viral polymerase) and the dsRNA] were associated to the endosomes. Since by this moment it had been already elucidated that VP3 "wrapped" de dsRNA within the RNPs (Luque et al., 2009) (DOI: 10.1016/j.jmb.2008.11.029), we sought that VP3 was most probably leading this association. We answered yes after studying its distribution, also endosome-associated, when ectopically expressed. These results were published in (Delgui et al., 2013) (DOI: 10.1128/jvi.03152-12).

Thus, in our subsequent studies, we have worked with both, the infection-derived or the ectopically expressed VP3, to advance in elucidating the mechanism by which VP3 hijacks the endosomal membranes and its relevancy for viral replication, reported in this current manuscript.

(15) Lines 320-334: This last paragraph discussing evolutionary links between birnaviruses and positive-strand RNA viruses seems tangential and distracting. Consider reducing or removing.

Thanks for highlighting this aspect of our work. Maybe difficult to follow, but in the context of other evidences reported for the Birnaviridae family of viruses, we strongly believe that there is an evolutionary aspect in having observed that these dsRNA viruses replicate associated to membranous organelles, a hallmark of +RNA viruses. However, we agree with the reviewer that this might not be the main point of our manuscript, so we reduced this paragraph accordingly. Please, see lines 358-367 in our revised version of the manuscript.

(16) Lines 322-324: Change "RdRd" to "RdRp" if keeping paragraph.

Thanks. We have corrected this mistake in lines 360 and 361.

(17) Figures 1A, 1B, and throughout: Again, please check and explain protein sizes and amounts. This would improve the clarity of the manuscript.

All our flotation assays were performed using 1 mM concentration of purified protein in a final volume of 100 mL (mentioned in M&M section). The complete fusion protein His-2xFYVE (shown in Figs. 1A and 4A left panel) is 954 base pairs-long and contains 317 residues (~35 kDa). The complete fusion protein His-VP3 FL (shown in Figs. 1B and 1G left panel) is 861 base pairs-long and contains 286 residues (~32 kDa). The complete fusion protein His-VP3 DCt (shown in Fig. 1G, right panel) is 753 bp-long and contains 250 residues (~28 kDa). The complete fusion protein His-VP3 FL R₂₀₀D (shown in Fig. 4A right panel) is 861 bp-long and contains 286 residues (~32 kDa). This latter information was incorporated in our revised version of the manuscript. Please, see lines 381-382, 396-397 and 399-400 from the M&M section, and lines in the corresponding figure legends.

(18) Figures 1B and 1G show different results for PI3P(+) membranes. I see protein associated with the top fraction in 1B, but I don't see any such result in 1G.

As already mentioned, liposome-based methods, such as the co-flotation assay, are well-established and widely regarded as the preferred approach for studying protein-phosphoinositide interactions. However, this approach is rather qualitative, as density gradient separation reveals whether the protein is located in the top fractions (bound to liposomes) or the bottom fractions (unbound). Our quantifications aim to demonstrate differences in the bound fraction between liposome populations with and without PI3P. Given the setting of the co-flotation assays, each protein-liposome system [2xFYVE-PI3P(-), 2xFYVE-PI3P(+), VP3-PI3P(-), or VP3-PI3P(+)] is assessed separately, and even if the conditions are homogeneous, it’s not surprising to observe differences in the protein level between each one. Indeed, the revised version of the manuscript include a membrane for Figure 1G, were His-VP3 FL associated with the top fraction is more clear. Please, see the new version of Figure 1G.

(19) Figure 1C: Please include cryo-EM images of the liposome PI3P(-) variables to assess the visual differences of the liposomal membranes under these conditions.

Thanks for the recommendation. it has been verified that there is no binding of gold particles to liposomes PI3P(-) when they are incubated solely with the gold-particle reagent, or when they are pre-incubated with the gold-particle reagent with either His-2xFYVE or His-VP3 FL. We have incorporated a new panel in Figure 1C showing a representative image of these results. Please, see lines 143-144 in the revised version of our manuscript and our revised version of Figure 1C.

(20) Figures 2D, 2E, and 3A: The puncta are not obvious in these images. Consider adding Zoomed panels.

We apologize for this aspect of Figures 2 and 3, also highlighted by reviewer #1. We believe that this was due to the low quality resulting from the PDF conversion of the original files. For Figure 3A, we have homogenized its aspect with those from 3B. Regarding Figure 2, we have incorporated zoomed panels, as suggested. Please, see the revised versions of both Figures.

(21) Figure 4A: There is almost no protein in the control PI3P(+) blot. Why? Also, the quantification shows no significant membrane association for this control. This result is different from Figure 1A and very confusing (and concerning).

We apologize for the confusion. We replaced membranes for Figure 4A (left panel) with more similar band intensities to that shown in Figure 1A. Please, visit our new version of Figure 4. The quantification shows no significant difference in the association to liposomes PI3P(+) compared to liposomes PI3P(+); it’s true and this is due to, once more, the intrinsically lack of homogeneity of co-flotation assays. However, this one shown in Figure 4A is a redundant control (has been shown in Figure 1A) and we believe that the new membrane is qualitative eloquent.

Reviewer #3 (Recommendations For The Authors):

(1) Overall, the title is general and does not summarize the study. I recommend making the title more specific. The current title is better suited for a review as opposed to a research article. This study provides further biophysical details on the interaction. This should be reflected in the title.

We appreciate this recommendation, which was also expressed by reviewer #2. We have chosen a new title for the manuscript: “On the Role of VP3-PI3P Interaction in Birnavirus Endosomal Membrane Targeting”.

(2) References 8,9,10 are important but they were not correctly cited in the work, this should be corrected.

We apologize for this mistake. These citations are identifiable in our revised version of the manuscript. See lines 100-105.

(3) Flotation experiments and cryo-EM convincingly show that VP3 binds to membranes in a PIP3-dependent manner. However, it would be advisable to include a control for cryo-EM using liposomes that do not contain PIP3 but are incubated with HIS-VP3-FL. This would allow us to rule out any unspecific binding that might not be detected on WB.

Thanks for the advice, also given by reviewer #2. We confirmed that no gold particles were bound on liposomes PI3P(-) even when incubated with the Ni-NTA reagent alone or pre-incubated with His-2xFYVE of His-VP3 FL. We have incorporated a new panel to Figure 1C showing a representative image of these results. Please, see lines 143-144 in the revised version of the manuscript and see the revised version of Figure 1C.

(4) It is not clear what is the difference between WB in B and WB in G. Figure 1G seems to show the same experiment as shown in B, is this a repetition? In both cases, plots next to WBs show quantification with bars, do they represent STD or SEM? Legend A mentions significance p>0.01 (**) but the plot shows ***. This should be corrected.

The Western blot membrane in Figure 1B shows the result of co-flotation assay using His-VP3 FL protein, while the Western blot membrane in Figure 1G (left panel) shows a co-flotation assay using His-VP3 FL protein as a positive control. In another words, in 1B the His-VP3 FL protein is the question while in 1G (left panel) it’s the co-flotation positive control for His-VP3 DCt. The bar plots next to Western blots show quantification, the mean and the STD. Thanks for highlighting this inconsistency. We have now corrected it on the revised version of the manuscript.

(5) It would be useful to indicate positively charged residues and P2 on the AF2 predicted structure in Fig 1.

These are indicated in panels A and B of Figure 2.

(6) Figure 1 legend: Change cryo-fixated liposomes to cryo-fixation or better to "liposomes were vitrified". There is a missing "o" in the cry-fixation in the methods section.

Thanks for the recommendation. We have modified Figure 1. legend to "liposomes were vitrified" (line 758), and fixed the word cryo-fixation in the methods section (line 512).

(7) Figure 2B. It is not clear how the punctated phenotype was unbiasedly characterized (Figure 2D). I see no difference in the representative images. Magnified images should be shown. This should be measured as colocalization (Pearson's and Mander's coefficient) with an early endosomal marker Rab5. Perhaps this figure could be consolidated with Figure 3.

Unfortunately, the lack of clarity in Figure 2D was due to the PDF conversion of the original files. Please, observe the high-quality original image above in response to reviewer #1, where we have additionally included zoomed panels, as also suggested by the other reviewers. For quantification of the co-localization of VP3 and either EGFP-Rab5 orEGFP-2xFYVE, the Manders M2 coefficient was calculated out of approximately 30 cells per construct and experiment and were shown in Figure S3 and Figure 3A, respectively, in our previous version of the manuscript.

(8) PIP3 antagonist drugs should be used to further substantiate the results. If PIP3 specifically recruits VP3, this interaction should be abolished in the presence of PIP3 drug and VP3 should show a diffused signal.

We certainly agree with this point. These experiments were performed and the results were reported in (Gimenez et al., 2020). Briefly, in that work, we blocked the synthesis of PI3P in QM7 cells in a stable cell line overexpressing VP3, QM7-VP3, with either the pan-PI3Kinase (PI3K) inhibitor LY294002, or the specific class III PI3K Vps34 inhibitor Vps34-IN1. In Figure 4, we showed that 98% of the cells treated with these inhibitors had the biosensor GFP-2FYVE dissociated from EEs, evidencing the depletion of PI3P in EEs (Figure 4A). In QM7-VP3 cells, we showed that the depletion of PI3P by either inhibitor caused the dissociation of VP3 from EEs and the disaggregation of VP3 puncta toward a cytosolic distribution (Figure 4B). Moreover, since this observation was crucial for our hipothesis, these results were further confirmed with an alternative strategy to deplete PI3P in EEs. We employed a system to inducibly hydrolyze endosomal PI3P through rapamycin-induced recruitment of the PI3P-myotubularin 1 (MTM1) to endosomes in cells expressing MTM1 fused to the FK506 binding protein (FKBP) and the rapamycin-binding domain fused to Rab5, using the fluorescent proteins mCherry-FKBP-MTM1 and iRFP-FRB-Rab5, as described in (Hammond et al., 2014). These results, shown in Figures 5, 6 and 7 in the same manuscript, further reinforced the notion that PI3P mediates and is necessary for the association of VP3 protein with EEs.

(9) The authors should show the localization of VP3 in IBDV-infected cells and treat cells with PI3P antagonists. The fact that R₂₀₀ is not rescued does not necessarily mean that this is because of the failed interaction with PI3P. As the authors wrote in the discussion: VP3 bears multiple essential roles during the viral life cycle (line 305).

Indeed, after having confirmed that the VP3 lost its localization associated to the endosomes after the treatment of the cells with PI3P antagonists, we demonstrated that depletion of PI3P significantly reduced the production of IBDV progeny. For this aim, we used two approaches, the inhibitor Vps34-IN1 and an siRNA against VPs34. In both cases, we observed a significantly reduced production of IBDV progeny (Figures 9 and 10). Specifically related to the reviewer’s question, the localization of VP3 in IBDV-infected cells and treated with PI3P antagonists was shown and quantified in Figure 9a.

(10) Could you provide adsorption-free energy profiles and MD simulations also for the R₂₀₀ mutant?

Following the reviewer’s suggestion, we have added a new figure to the supplementary information (Figure S15). Instead of presenting a full free-energy profile for each protein, we focused on the adsorption free energy (i.e., the minimum of the adsorption free-energy profile) for VP3 ΔNt and its mutants, VP3 ΔNt R₂₀₀D and VP3 ΔNt P2 Mut, as a function of salt concentration. The aim was to compare the adsorption free energy of the three proteins and evaluate the effect of electrostatic forces on it, which become increasingly screened at higher salt concentrations. As shown in the referenced figure, reducing the number of positively charged residues from VP3 ΔNt to VP3 ΔNt P2 Mut systematically weakens the protein’s binding to the membrane. This effect is particularly pronounced at lower salt concentrations, underscoring the importance of electrostatic interactions in the adsorption of the negatively charged VP3 onto the anionic membrane.

(11) Liposome deformations in the presence of VP3 are interesting (Figure 6G), were these also observed in Figure 1C?

Good question. The liposome deformations in the presence of VP3 shown in Figure 6G were a robust observation since, as mentioned, it was detectable in 36% of the liposomes PI3P(+), while they were completely absent in PI3P(-) liposomes. However, and unfortunately, the same deformations were not detectable in experiments performed using gold particles shown in Figure 1C. In this regard, we think that it might be possible that the procedure of gold particles incubation itself, or even the presence of the gold particles in the images, would somehow “mask” the deformations effect.

Bibliography

Boukhalfa A, Roccio F, Dupont N, Codogno P, Morel E. 2021. The autophagy protein ATG16L1 cooperates with IFT20 and INPP5E to regulate the turnover of phosphoinositides at the primary cilium. Cell Rep 35:109045. doi:10.1016/j.celrep.2021.109045

Casañas A, Navarro A, Ferrer-Orta C, González D, Rodríguez JF, Verdaguer N. 2008. Structural Insights into the Multifunctional Protein VP3 of Birnaviruses. Structure 16:29–37. doi:10.1016/j.str.2007.10.023

Delgui LR, Rodriguez JF, Colombo MI. 2013. The Endosomal Pathway and the Golgi Complex Are Involved in the Infectious Bursal Disease Virus Life Cycle. J Virol 87:8993–9007. doi:10.1128/JVI.03152-12

Gimenez MC, Issa M, Sheth J, Colombo MI, Terebiznik MR, Delgui LR. 2020. Phosphatidylinositol 3-Phosphate Mediates the Establishment of Infectious Bursal Disease Virus Replication Complexes in Association with Early Endosomes. J Virol 95:e02313-20. doi:10.1128/jvi.02313-20

Hammond GRV, Machner MP, Balla T. 2014. A novel probe for phosphatidylinositol 4-phosphate reveals multiple pools beyond the Golgi. J Cell Biol 205:113–126. doi:10.1083/jcb.201312072

Khaldoun SA, Emond-Boisjoly MA, Chateau D, Carrière V, Lacasa M, Rousset M, Demignot S, Morel E. 2014. Autophagosomes contribute to intracellular lipid distribution in enterocytes. Mol Biol Cell 25:118. doi:10.1091/mbc.E13-06-0324

Luque D, Saugar I, Rejas MT, Carrascosa JL, Rodríguez JF, Castón JR. 2009. Infectious Bursal Disease Virus: Ribonucleoprotein Complexes of a Double-Stranded RNA Virus. J Mol Biol 386:891–901. doi:10.1016/j.jmb.2008.11.029

Morel E, Chamoun Z, Lasiecka ZM, Chan RB, Williamson RL, Vetanovetz C, Dall’Armi C, Simoes S, Point Du Jour KS, McCabe BD, Small SA, Di Paolo G. 2013. Phosphatidylinositol-3-phosphate regulates sorting and processing of amyloid precursor protein through the endosomal system. Nature Communications 2013 4:1 4:1–13. doi:10.1038/ncomms3250

Qi X, Gao Y, Gao H, Deng X, Bu Z, Wang Xiaoyan, Fu C, Wang Xiaomei. 2007. An improved method for infectious bursal disease virus rescue using RNA polymerase II system. J Virol Methods 142:81–88. doi:10.1016/j.jviromet.2007.01.021

Author response:

The following is the authors’ response to the original reviews.

We thank the reviewers for their constructive comments and suggestions. We have prepared a revised manuscript with updated quantification of theta cycle skipping, new statistical comparisons of the difference between the two behavioral tasks, and general improvements to the text and figures.

Reviewer #1 (Public Review):

Summary

The authors provide very compelling evidence that the lateral septum (LS) engages in theta cycle skipping.

Strengths

The data and analysis are highly compelling regarding the existence of cycle skipping.

Weaknesses

The manuscript falls short on in describing the behavioral or physiological importance of the witnessed theta cycle skipping, and there is a lack of attention to detail with some of the findings and figures:

More/any description is needed in the article text to explain the switching task and the behavioral paradigm generally. This should be moved from only being in methods as it is essential for understanding the study.

Following this suggestion, we have expanded the description of the behavioral tasks in the Results section.

An explanation is needed as to how a cell can be theta skipping if it is not theta rhythmic.

A cell that is purely theta skipping (i.e., always fires on alternating theta cycles and never on adjacent theta cycles) will only have enhanced power at half theta frequency and not at theta frequency. Such a cell will therefore not be considered theta rhythmic in our analysis. Note, however, that there is a large overlap between theta rhythmic and theta skipping cell populations in our data (Figure 3 - figure supplement 2), indicating that most cells are not purely theta skipping.

The most interesting result, in my opinion, is the last paragraph of the entire results section, where there is more switching in the alternation task, but the reader is kind of left hanging as to how this relates to other findings. How does this relate to differences in decoding of relative arms (the correct or incorrect arm) during those theta cycles or to the animal's actual choice? Similarly, how does it relate to the animal's actual choice? Is this phenomenon actually behaviorally or physiologically meaningful at all? Does it contribute at all to any sort of planning or decision-making?

We agree that the difference between the two behavioral tasks is very interesting. It may provide clues about the mechanisms that control the cycle-by-cycle expression of possible future paths and the potential impact of goal-directed planning and (recent) experience. In the revised manuscript, we have expanded the analysis of the differences in theta-cycle dynamics between the two behavioral tasks. First, we confirm the difference through a new quantification and statistical comparison. Second, we performed additional analyses to explore the idea that the alternation of non-local representations reflects the number of relevant paths available to the animal (Figure 11 – figure supplements 2 and 3), but this did not appear to be the case. However, these results provide a starting point for future studies to clarify the task dependence of the theta- cycle dynamics of spatial representations and to address the important question of behavioral/physiological relevance.

The authors state that there is more cycle skipping in the alternation task than in the switching task, and that this switching occurs in the lead-up to the choice point. Then they say there is a higher peak at ~125 in the alternation task, which is consistent. However, in the final sentence, the authors note that "This result indicates that the representations of the goal arms alternate more strongly ahead of the choice point when animals performed a task in which either goal arm potentially leads to reward." Doesn't either arm potentially lead to a reward (but different amounts) in the switching task, not the alternation task? Yet switching is stronger in the alternation task, which is not constant and contradicts this last sentence.

The reviewer is correct that both choices lead to (different amounts of) reward in the switching task. As written, the sentence that the reviewer refers to is indeed not accurate and we have rephrased it to: “This result indicates that the representations of the goal arms alternate more strongly ahead of the choice point when animals performed a task in which either goal arm potentially leads to a desirable high-value reward.”.

Additionally, regarding the same sentence - "representations of the goal arms alternate more strongly ahead of the choice point when the animals performed a task in which either goal arm potentially leads to reward." - is this actually what is going on? Is there any reason at all to think this has anything to do with reward versus just a navigational choice?

We appreciate the reviewer’s feedback and acknowledge that our statement needs clarification. At the choice point in the Y-maze there are two physical future paths available to the animal (disregarding the path that the animal took to reach the choice point) – we assume this is what the reviewer refers to as “a navigational choice”. One hypothesis could be that alternation of goal arm representations is present whenever there are multiple future paths available, irrespective of the animal’s (learned) preference to visit one or the other goal arm. However, the reduced alternation of goal arm representations in the switching task that we report, suggests that the animal’s recent history of goal arm visits and reward expectations likely do influence the theta-cycle representations ahead of the choice point. We have expanded our analysis to test if theta cycle dynamics differ for trials before and after a switch in reward contingency in the switching task, but there was no statistical difference in our data. We have rewritten and expanded this part of the results to make our point more clearly.

Similarly, the authors mention several times that the LS links the HPC to 'reward' regions in the brain, and it has been found that the LS represents rewarded locations comparatively more than the hippocampus. How does this relate to their finding?

Indeed, Wirtshafter and Wilson (2020) reported that lateral septum cells are more likely to have a place field close to a reward site than elsewhere in their double-sided T-maze. It is possible that this indicates a shift towards reward or value representations in the lateral septum. In our study we did not look at reward-biased cells and whether they are more or less likely to engage in theta cycle skipping. This could be a topic for future analyses. It should be noted that the study by Wirtshafter and Wilson (2020) reports that a reward bias was predominantly present for place fields in the direction of travel away from the reward site. These reward-proximate LS cells may thus contribute to theta-cycle skipping in the inbound direction, but it is not clear if these cells would be active during theta sweeps when approaching the choice point in the outbound direction.

Reviewer #2 (Public Review)

Summary

Recent evidence indicates that cells of the navigation system representing different directions and whole spatial routes fire in a rhythmic alternation during 5-10 Hz (theta) network oscillation (Brandon et al., 2013, Kay et al., 2020). This phenomenon of theta cycle skipping was also reported in broader circuitry connecting the navigation system with the cognitive control regions (Jankowski et al., 2014, Tang et al., 2021). Yet nothing was known about the translation of these temporally separate representations to midbrain regions involved in reward processing as well as the hypothalamic regions, which integrate metabolic, visceral, and sensory signals with the descending signals from the forebrain to ensure adaptive control of innate behaviors (Carus-Cadavieco et al., 2017). The present work aimed to investigate theta cycle skipping and alternating representations of trajectories in the lateral septum, neurons of which receive inputs from a large number of CA1 and nearly all CA3 pyramidal cells (Risold and Swanson, 1995). While spatial firing has been reported in the lateral septum before (Leutgeb and Mizumori, 2002, Wirtshafter and Wilson, 2019), its dynamic aspects have remained elusive. The present study replicates the previous findings of theta-rhythmic neuronal activity in the lateral septum and reports a temporal alternation of spatial representations in this region, thus filling an important knowledge gap and significantly extending the understanding of the processing of spatial information in the brain. The lateral septum thus propagates the representations of alternative spatial behaviors to its efferent regions. The results can instruct further research of neural mechanisms supporting learning during goal-oriented navigation and decision-making in the behaviourally crucial circuits entailing the lateral septum.

Strengths

To this end, cutting-edge approaches for high-density monitoring of neuronal activity in freely behaving rodents and neural decoding were applied. Strengths of this work include comparisons of different anatomically and probably functionally distinct compartments of the lateral septum, innervated by different hippocampal domains and projecting to different parts of the hypothalamus; large neuronal datasets including many sessions with simultaneously recorded neurons; consequently, the rhythmic aspects of the spatial code could be directly revealed from the analysis of multiple spike trains, which were also used for decoding of spatial trajectories; and comparisons of the spatial coding between the two differently reinforced tasks.

Weaknesses

Possible in principle, with the present data across sessions, longitudinal analysis of the spatial coding during learning the task was not performed. Without using perturbation techniques, the present approach could not identify the aspects of the spatial code actually influencing the generation of behaviors by downstream regions.

Reviewer #3 (Public Review)

Summary

Bzymek and Kloosterman carried out a complex experiment to determine the temporal spike dynamics of cells in the dorsal and intermediate lateral septum during the performance of a Y-maze spatial task. In this descriptive study, the authors aim to determine if inputting spatial and temporal dynamics of hippocampal cells carry over to the lateral septum, thereby presenting the possibility that this information could then be conveyed to other interconnected subcortical circuits. The authors are successful in these aims, demonstrating that the phenomenon of theta cycle skipping is present in cells of the lateral septum. This finding is a significant contribution to the field as it indicates the phenomenon is present in neocortex, hippocampus, and the subcortical hub of the lateral septal circuit. In effect, this discovery closes the circuit loop on theta cycle skipping between the interconnected regions of the entorhinal cortex, hippocampus, and lateral septum. Moreover, the authors make 2 additional findings: 1) There are differences in the degree of theta modulation and theta cycle skipping as a function of depth, between the dorsal and intermediate lateral septum; and 2) The significant proportion of lateral septum cells that exhibit theta cycle skipping, predominantly do so during 'non-local' spatial processing.

Strengths

The major strength of the study lies in its design, with 2 behavioral tasks within the Y-maze and a battery of established analyses drawn from prior studies that have established spatial and temporal firing patterns of entorhinal and hippocampal cells during these tasks. Primary among these analyses, is the ability to decode the animal's position relative to locations of increased spatial cognitive demand, such as the choice point before the goal arms. The presence of theta cycle skipping cells in the lateral septum is robust and has significant implications for the ability to dissect the generation and transfer of spatial routes to goals within and between the neocortex and subcortical neural circuits.

Weaknesses

There are no major discernable weaknesses in the study, yet the scope and mechanism of the theta cycle phenomenon remain to be placed in the context of other phenomena indicative of spatial processing independent of the animal's current position. An example of this would be the ensemble-level 'scan ahead' activity of hippocampal place cells (Gupta et al., 2012; Johnson & Redish, 2007). Given the extensive analytical demands of the study, it is understandable that the authors chose to limit the analyses to the spatial and burst firing dynamics of the septal cells rather than the phasic firing of septal action potentials relative to local theta oscillations or CA1 theta oscillations. Yet, one would ideally be able to link, rather than parse the phenomena of temporal dynamics. For example, Tingley et al recently showed that there was significant phase coding of action potentials in lateral septum cells relative to spatial location (Tingley & Buzsaki, 2018). This begs the question as to whether the non-uniform distribution of septal cell activity within the Y-maze may have a phasic firing component, as well as a theta cycle skipping component. If so, these phenomena could represent another means of information transfer within the spatial circuit during cognitive demands. Alternatively, these phenomena could be part of the same process, ultimately representing the coherent input of information from one region to another. Future experiments will therefore have to sort out whether theta cycle skipping, is a feature of either rate or phase coding, or perhaps both, depending on circuit and cognitive demands.

The authors have achieved their aims of describing the temporal dynamics of the lateral septum, at both the dorsal extreme and the intermediate region. All conclusions are warranted.

Reviewer #1 (Recommendations For The Authors)

The text states: "We found that 39.7% of cells in the LSD and 32.4% of cells in LSI had significantly higher CSI values than expected by chance on at least one of the trajectories." The text in the supplemental figure indicates a p-value of 0.05 was used to determine significance. However, four trajectory categories are being examined so a Bonferroni correction should be used (significance at p<0.0125).

Indeed, a p-value correction for multiple tests should be performed when determining theta cycle skipping behavior for each of the four trajectories. We thank the reviewer for pointing out this oversight. We have implemented a Holm-Sidak p-value correction for the number of tested trajectories per cell (excluding trajectories with insufficient spikes). As a consequence, the number of cells with significant cycle-skipping activity decreased, but overall the results have not changed.

Figure 4 is very confusing as raster plots are displayed for multiple animals but it is unclear which animal the LFP refers to? The bottom of the plot is also referenced twice in the figure caption.

We apologize for the confusion. We have removed this figure in the revised manuscript, as it was not necessary to make the point about the spatial distribution of theta cycle skipping. Instead, we show examples of spatially-resolved cycle skipping in Figure 4 (formerly Figure 5 - supplementary figures 1 and 2) and we have added a plot with the spatially-resolved cycle skipping index for all analyzed cells in Figure 5A.

Figure 6 has, I think, an incorrect caption or figure. Only A and B are marked in the figure but A-G are mentioned in the caption but do not appear to correspond to anything in the figure.

Indeed, the caption was outdated. This has now been corrected.

Figure 8 is also confusing for several reasons: how is the probability scale on the right related to multiple semi-separate (top and middle) figures? In the top and bottom figures, it is not clear what the right and left sides refer to. It is also unclear why a probability of 0.25 is used for position (seems potentially low). The caption also mentions Figure A but there are no lettered "sub" figures in Figure 8.

The color bar on the right applies to both the top plot (directional decoding) and the middle plot (positional decoding). However, the maximum probability that is represented by black differs between the top and middle plots. We acknowledge that a shared color bar may lead to confusion and we have given each of the plots a separate color bar.

As for the maximum probability of 0.25 for position: this was a typo in the legend. The correct maximum value is 0.5. In general, the posterior probability will be distributed over multiple (often neighboring) spatial bins, and the distribution of maximum probabilities will depend on the number of spatial bins, the level of spatial smoothing in the decoding algorithm, and the amount of decodable information in the data. It would be more appropriate to consider the integrated probability over a small section of the maze, rather than the peak probability that is assigned to a single 5 cm bin. Also, note that a posterior probability of 0.5 is many times higher than the probability associated with a uniform distribution, which is in our case.

The left and right sides of the plots represent two different journeys that the animal ran. On the left an outbound journey is shown, and on the right an inbound journey. We have improved the figure and the description in the legend to make this clearer.

The reviewer is correct that there are no panels in Figure 8 and we have corrected the legend.

Some minor concerns

The introduction states that "a few studies have reported place cell-like activity in the lateral septum (Tingley and Buzsaki, 2018; Wirtshafter and Wilson, 2020, 2019)." However, notably and controversially, the Tingley study is one of the few studies to find NO place cell activity in the lateral septum. This is sort of mentioned later but the citation in this location should be removed.

The reviewer is correct, Tingley and Buzsaki reported a spatial phase code but no spatial rate code. We have removed the citation.

Stronger position/direction coding in the dLS consistent with prior studies and they should be cited in text (not a novel finding).

Thank you for pointing out this omission. Indeed, a stronger spatial coding in the dorsal lateral septum has been reported before, for example by Van der Veldt et al. (2021). We now cite this paper when discussing these findings.

Why is the alternation task administered for 30m but the switching task for 45m?

The reason is that rats received a larger reward in the switching task (in the high-reward goal arm) and took longer to complete trials on average. To obtain a more-or-less similar number of trials per session in both tasks, we extended the duration of switching task sessions to 45 minutes. We have added this explanation to the text.

Regarding the percentage of spatially modulated cells in the discussion, it is also worth pointing out that bits/sec information is consistent with previous studies.

Thank you for the suggestion. We now point out that the spatial information in our data is consistent with previous studies.

Reviewer #2 (Recommendations For The Authors)

While the results of the study are robust and timely, further details of behavioural training, additional quantitative comparisons, and improvements in the data presentation would make the study more comprehensible and complete.

Major comments

(1) I could not fully comprehend the behavioural protocols. They require a clearer explanation of both the specific rationale of the two tasks as well as a more detailed presentation of the protocols. Specifically:

(1.1) In the alternation task, were the arms baited in a random succession? How many trials were applied per session? Fig 1D: how could animals reach high choice accuracy if the baiting was random?

We used a continuous version of the alternation task, in which the animals were rewarded for left→home→right and right→home→left visit sequences. In addition, animals were always rewarded on inbound journeys. There was no random baiting of goal arms. Perhaps the confusion stems from our use of the word “trial” to refer to a completed lap (i.e., a pair of outbound/inbound journeys). On average, animals performed 54 of such trials per 30-minute session in the alternation task. We have expanded the description of the behavioral tasks in the Results and further clarified these points in the Methods section.

(1.2) Were they rewarded for correct inbound trials? If there was no reward, why were they considered correct?

Yes, rats received a reward at the home platform for correct inbound trials. We have now explicitly stated this in the text.

(1.3) In the switch alternation protocol, for how many trials was one arm kept more rewarding than the other, and how many trials followed after the rewarding value switch?

A switch was triggered when rats (of their own volition) visited the high-reward goal arm eight times in a row. Following a switch, the animals could complete as many trials as necessary until they visited the new high- reward goal arm in eight consecutive trials, which triggered another switch. As can be seen in Figure 1D, at the population level, animals needed ~13 trials to fully commit to the high-reward goal arm following a switch. We have further clarified the switching task protocol in the Results and Methods sections.

(1.4) What does the phrase "the opposite arm (as 8 consecutive visits)" exactly mean? Sounds like 8 consecutive visits signalled that the arm was rewarded (as if were not predefined in the protocol).

The task is self-paced and the animals initially visit both goal arms, before developing a bias for the high- reward goal arm. A switch of reward size was triggered as soon as the animal visited the high-reward goal arm for eight consecutive trials. We have rewritten the description of the switching task protocol, including this sentence, which hopefully clarifies the procedure.

(1.5) P. 15, 1st paragraph, Theta cycle skipping and alternation of spatial representations is more prominent in the alternation task. Why in the switching task, did rats visit the left and right arms approximately equally often if one was more rewarding than the other? How many switches were applied per recording session, and how many trials were there in total?

Both the left and right goal arms were sampled more or less equally by the animals because both goal arms at various times were associated with a large reward following switches in reward values during sessions. The number of switches per session varied from 1 to 3. Sampling of both goal arms was also evident at the beginning of each session and following each reward value switch, before animals switched their behavior to the (new) highly rewarded goal arm. In Table 1, we have now listed the number of trials and the number of reward-value switches for all sessions.

(1.6) Is the goal arm in figures the rewarded/highly rewarded arm only or are non-baited arms also considered here?

Both left and right arms are considered goal arms and were included in the analyses, irrespective of the reward that was received (or not received).

(2) The spatial navigation-centred behavioural study design and the interpretation of results highlight the importance of the dorsal hippocampal input to the LS. Yet, the recorded LSI cells are innervated by intermediate and ventral aspects of the hippocampus, and LS receives inputs from the amygdala and the prefrontal cortex, which together may together bring about - crucial for the adaptive behaviours regulated by the LS - reward, and reward-prediction-related aspects in the firing of LS cells during spatial navigation. Does success or failure to acquire reward in a trial modify spatial coding and cycle skipping of LSD vs. LSI cells in ensuing inbound and outbound trials?

This is an excellent question and given the length of the current manuscript, we think that exploration of this question is best left for a future extension of our study.

A related question: in Figure 10, it is interesting that cycle skipping is prominent in the goal arm for outbound switching trials and inbound trials of both tasks. Could it be analytically explained by task contingencies and behaviour (e.g. correct/incorrect trial, learning dynamics, running speed, or acceleration)?

Our observation of cycle skipping at the single-cell level in the goal arms is somewhat surprising and, we agree with the reviewer, potentially interesting. However, it was not accompanied by alternation of representations at the population level. Given the current focus and length of the manuscript, we think further investigation of cycle skipping in the goal arm is better left for future analyses.

(3) Regarding possible cellular and circuit mechanisms of cycle skipping and their relation to the alternating representations in the LS. Recent history of spiking influences the discharge probability; e.g. complex spike bursts in the hippocampus are associated with a post-burst delay of spiking. In LS, cycle skipping was characteristic for LS cells with high firing rates and was not uniformly present in all trajectories and arms. The authors propose that cycle skipping can be more pronounced in epochs of reduced firing, yet the opposite seems also possible - this phenomenon can be due to an intermittently increased drive onto some LS cells. Was there a systematic relationship between cycle skipping in a given cell and the concurrent firing rate or a recent discharge with short interspike intervals?

In our discussion, we tried to explain the presence of theta cycle skipping in the goal arms at the single-cell level without corresponding alternation dynamics at the population level. We mentioned the possibility of a decrease in excitatory drive. As the reviewer suggests, an increase in excitatory drive combined with post- burst suppression or delay of spiking is an alternative explanation. We analyzed the spatial tuning of cells with theta cycle skipping and found that, on average, these cells have a higher firing rate in the goal arm than the stem of the maze in both outbound and inbound run directions (Figure 5 – figure supplement 1). In contrast, cells that do not display theta cycle skipping do not show increased firing in the goal arm. These results are more consistent with the reviewer’s suggested mechanism and we have updated the discussion accordingly.

(4) Were the differences between the theta modulation (cycle skipping) of local vs. non-local representations (P.14, line 10-12, "In contrast...", Figure 9A) and between alternation vs. switching tasks (Figure 10 C,D) significantly different?

We have added quantification and statistical comparisons for the auto- and cross-correlations of the local/non-local representations. The results indeed show significantly stronger theta cycle skipping of the non-local representations as compared to the local representations (Figure 10 - figure supplement 1A), a stronger alternation of non-local representations in the outbound direction (Figure 10 - figure supplement 1B), and significant differences between the two tasks (Figure 11E,F).

(5) Regarding the possibility of prospective coding in LS, is the accurate coding of run direction not consistent with prospective coding? Can the direction be decoded from the neural activity in the start arm? Are the cycling representations of the upcoming arms near the choice point equally likely or preferential for the then- selected arm?

The coding of run direction (outbound or inbound) is distinct from the prospective/retrospective coding of the goal arm. As implemented, the directional decoding model does not differentiate between the two goal arms and accurate decoding of direction with this model can not inform us whether or not there is prospective (or retrospective) coding. To address the reviewer’s comments, we performed two additional analyses. First, we analyzed the directional (outbound/inbound) decoding performance as a function of location in the maze (Figure 6 - figure supplement 3E). The results show that directional decoding performance is high in both stem and goal arms. Second, we analyzed how well we can predict the trajectory type (i.e., to/from the left or right goal arm) as a function of location in the maze, and separately for outbound and inbound trajectories (Figure 6 - figure supplement 3C,D). The results show that on outbound journeys, decoding the future goal arm is close to chance when the animals are running along the stem. The decoding performance goes up around the choice point and reaches the highest level when animals are in the goal arm.

(6) Figure 10 seems to show the same or similar data as Figures 5 (A,B) and 9 (C,D).

Figure 10 (figure 11 in revised manuscript) re-analyzes the same data as presented in Figures 5 and 9, but separates the experimental sessions according to the behavioral task. We now explicitly state this.

Minor comments

(1) If cycle skipping in the periodicity of non-local representations was more prominent in alternation than in the switching task, one might expect them to be also prominent in early trials of the switching task, when the preference of a more rewarding arm is not yet established. Was this the case?

The reviewer makes an interesting suggestion. Indeed, if theta cycle skipping and the alternation of non-local representations reflect that there are multiple paths that the animal is considering, one may predict that the theta skipping dynamics are similar between the two tasks in early trials (as the reviewer suggests). Similarly, one may predict that in the switching task, the alternation of non-local representations is weaker immediately before a reward contingency switch (when the animal has developed a bias towards the goal arm with a large reward) as compared to after the switch.

We have now quantified the theta cycle dynamics of spatial representations in the early trials in each session of both tasks (Figure 11 - figure supplement 2) and in the trials before and after each switch in the switching task (Figure 11 - figure supplement 3).

The results of the early trial analysis indicate stronger alternation of non-local representations in the alternation task than in the switching task (consistent with the whole session analysis), which is contrary to the prediction.

The pre-/post-switch analysis did not reveal a significant difference between the trials before and after a reward contingency switch. If anything, there was a trend towards stronger theta cycle skipping/alternation in the trials before a switch, which would be opposite to the prediction.

These results do not appear to support the idea that the alternation of non-local representations reflects the number of relevant paths available to the animal. We have updated the text to incorporate these new data and discuss the implications.

(2) Summary: sounds like the encoding of spatial information and its readout in the efferent regions are equally well established.

Thank you for pointing this out.

(3) Summary: "motivation and reward processing centers such as the ventral tegmental area." How about also mentioning here the hypothalamus, which is a more prominent output of the lateral septum than the VTA?

We have now also mentioned the hypothalamus.

(4) "lateral septum may contribute to the hippocampal theta" - readers not familiar with details of the medial vs. lateral septum research may misinterpret the modest role of LS in theta compared to MS.

We have added “in addition to the strong theta drive originating from the medial septum” to make clear that the lateral septum has a modest role in hippocampal theta generation.

(5) "(Tingley and Buzsáki, 2018) found a lack of spatial rate coding in the lateral septum and instead reported a place coding by specific phases of the hippocampal theta rhythm (Rizzi-Wise and Wang, 2021) " needs rephrasing.

Thank you, we have rephrased the sentence.

(6) Figure 4 is a bit hard to generalize. The authors may additionally consider a sorted raster presentation of the dataset in this main figure.

We have removed this figure in the revised manuscript, as it was not necessary to make the point about the location of theta cycle skipping. Instead, we show examples of spatially-resolved cycle skipping in Figure 4 (formerly Figure 5 - supplementary figures 1 and 2), and, following the reviewer’s suggestion, we have added a plot with the spatially-resolved cycle skipping index for all analyzed cells (Figure 5A).

(7) It would help if legends of Figure 5 (and related supplementary figures) state in which of the two tasks the data was acquired, as it is done for Figure 10.

Thank you for the suggestion. The legends of Figure 4A,B (formerly Figure 5 – supplemental figures 1 and 2) and Figure 5 now include in which behavioral task the data was acquired.

(8) Page 10, "Spatial coding...", 1st Citing the initial report by Leugeb and Mizumori would be appropriate here too.

The reviewer is correct. We have added the citation.

(9) The legend in Figure 6 (panels A-G) does not match the figure (only panels A,B). What is shown in Fig. 6B, the legend does not seem to fully match.

Indeed, the legend was outdated. This has now been corrected.

(10) 7 suppl., if extended to enable comparisons, could be a main figure. Presently, Figure 7C does not account for the confounding effect of population size and is therefore difficult to interpret without complex comparisons with the Supplementary Figure which is revealing per se.

We thank the reviewer for their suggestion. We have changed Figure 7 such that it only shows the analysis of decoding performed with all LSD and LSI cells. Figure 7 – supplemental figure 1 has been transformed into main Figure 8, with the addition of a panel to show a statistical comparison between decoding performance in LSD and LSI with a fixed number of cells.

(11) 14, line 10 there is no Figure 8A

This has been corrected.

(12) 15 paragraph 1, is the discussed here model the one from Kay et al?

From Kay et al. (2020) and also Wang et al. (2020). We have added the citations.

(13) Figure 5 - Figure Supplement 1 presents a nice analysis that, in my view, can merit a main figure. I could not find the description of the colour code in CSI panels, does grey/red refer to non/significant points?

Indeed, grey/red refers to non-significant points and significant points respectively. We have clarified the color code in the figure legend. Following the reviewer’s suggestion, we have made Figure 5 Supplement 1 and 2 a main figure (Figure 4).

(14) Figure 5 -Figure Supplement 2. Half of the cells (255 and 549) seems not to be representative of the typically high SCI in the goal arm in left and right inbound trials combined (Figure 5 A). Were the changes in CSI in the right and left inbound trials similar enough to be combined in Fig 5A? Otherwise, considering left and right inbound runs separately and trying to explain where the differences come from would seem to make sense.

Figure 5 – figure supplement 2 is now part of the new main Figure 4. Originally, the examples were from a single session and the same cells as shown in the old Figure 4. However, since the old Figure 4 has been removed, we have selected examples from different sessions and both left/right trajectories that are more representative of the overall distribution. We have further added a plot with the spatially-resolved cycle skipping for all analyzed cells in Figure 5A.

(15) In the second paragraph of the Discussion, dorso-ventral topography of hippocampal projections to the LS (Risold and Swanson, Science, 90s) could be more explicitly stated here.

Thank you for the suggestion. We have now explicitly mentioned the dorsal-ventral topography of hippocampal-lateral septum projections and cite Risold & Swanson (1997).

(16) Discussion point: why do the differences in spatial information of cells in the ventral/intermediate vs. dorsal hippocampus not translate into similarly prominent differences in LSI vs. LSD?

In our data, we do observe clear differences in spatial coding between LSD and LSI. Specifically, cell activity in the LSD is more directional, has higher goal arm selectivity, and higher spatial information (we have now added statistical comparisons to Figure 6 – figure supplement 1). As a result, spatial decoding performance is much better for LSD cell populations than LSI cell populations (see updated Figure 8, with statistical comparison of decoding performance). Spatial coding in the LS is not as strong as in the hippocampus, likely because of the convergence of hippocampal inputs, which may give the impression of a less prominent difference between the two subregions.

(17) Discussion, last paragraph: citation of the few original anatomical and neurophysiological studies would be fitting here, in addition to the recent review article.

Thank you for the suggestion. We have added selected citations of the original literature.

(18) Methods, what was the reference electrode?

We used an external reference electrode that was soldered to a skull screw, which was positioned above the cerebellum. We have added this to the Methods section.

(19) Methods, Theta cycle skipping: bandwidth = gaussian kerner parameter?

The bandwidth is indeed a parameter of the Gaussian smoothing kernel and is equal to the standard deviation.

Reviewer #3 (Recommendations For The Authors)

Below I offer a short list of minor comments and suggestions that may benefit the manuscript.

(A) I was not able to access the Open Science Framework Repository. Can this be rectified?

Thank you for checking the OSF repository. The data and analysis code are now publicly available.

(B) In the discussion the authors should attempt to flesh out whether they can place theta cycle skipping into context with left/right sweeps or scan ahead phenomena, as shown in the Redish lab.

Thank you for the excellent suggestion. We have now added a discussion of the possible link between theta cycle skipping and the previously reported scan-ahead theta sweeps.

(C) What is the mechanism of cycle skipping? This could be relevant to intrinsic vs network oscillator models. Reference should also be made to the Deshmukh model of interference between theta and delta (Deshmukh, Yoganarasimha, Voicu, & Knierim, 2010).

We had discussed a potential mechanism in the discussion (2nd to last paragraph in the revised manuscript), which now includes a citation of a recent computational study (Chu et al., 2023). We have now also added a reference to the interference model in Deshmukh et al, 2010.

(D) Little background was given for the motivation and expectation for potential differences between the comparison of the dorsal and intermediate lateral septum. I don't believe that this is the same as the dorsal/ventral axis of the hippocampus, but if there's a physiological justification, the authors need to make it.

We have added a paragraph to the introduction to explain the anatomical and physiological differences across the lateral septum subregions that provide our rationale for comparing dorsal and intermediate lateral septum (we excluded the ventral lateral septum because the number of cells recorded in this region was too low).

(E) It would help to label "outbound" and "inbound" on several of the figures. All axes need to be labeled, with appropriate units indicated.

We have carefully checked the figures and added inbound/outbound labels and axes labels where appropriate.

(F) In Figure 6, the legend doesn't match the figure.

Indeed, the legend was outdated. This has now been corrected.

(G) The firing rate was non-uniform across the Y-maze. Does this mean that the cells tended to fire more in specific positions of the maze? If so, how would this affect the result? Would increased theta cycle skipping at the choice point translate to a lower firing rate at the choice point? Perhaps less overdispersion of the firing rate (Fenton et al., 2010)?

Individual cells indeed show a non-uniform firing rate across the maze. To address the reviewer’s comment and test if theta cycle skipping cells were active preferentially near the choice point or other locations, we computed the mean-corrected spatial tuning curves for cell-trajectory pairs with and without significant theta cycle skipping. This additional analysis indicates that, on average, the population of theta cycle skipping cells showed a higher firing rate in the goal arms than in the stem of the maze as compared to non-skipping cells for outbound and inbound directions (shown in Figure 5 - figure supplement 1).

(H) As mentioned above, it could be helpful to look at phase preference. Was there an increased phase preference at the choice point? Would half-cycle firing correlate with an increased or decreased phase preference? Based on prior work, one would expect increased phase preference, at least in CA1, at the choice point (Schomburg et al., 2014). In contrast, other work might predict phasic preference according to spatial location (Tingley & Buzsaki, 2018). Including phase analyses is a suggestion, of course. The manuscript is already sufficiently novel and informative. Yet, the authors should state why phase was not analyzed and that these questions remain for follow-up analyses. If the authors did analyze this and found negative results, it should be included in this manuscript.

We thank the reviewer for their suggestion. We have not yet analyzed the theta phase preference of lateral septum cells or other relations to the theta phase. We agree that this would be a valuable extension of our work, but prefer to leave it for future analyses.

(I) One of the most important aspects of the manuscript, is that there is now evidence of theta cycle skipping in the circuit loop between the EC, CA1, and LS. This now creates a foundation for circuit-based studies that could dissect the origin of route planning. Perhaps the authors should state this? In the same line of thinking, how would one determine whether theta cycle skipping is necessary for route planning as opposed to a byproduct of route planning? While this question is extremely complex, other studies have shown that spatial navigation and memory are still possible during the optogenetic manipulation of septal oscillations (Mouchati, Kloc, Holmes, White, & Barry, 2020; Quirk et al., 2021). However, pharmacological perturbation or lesioning of septal activity can have a more profound effect on spatial navigation (Bolding, Ferbinteanu, Fox, & Muller, 2019; Winson, 1978). As a descriptive study, I think it would be helpful to remind the readers of these basic concepts.

We thank the reviewer for their comment and for pointing out possible future directions for linking theta cycle skipping to route planning. Experimental manipulations to directly test this link would be very challenging, but worthwhile to pursue. We now mention how circuit-based studies may help to test if theta cycle skipping in the broader subcortical-cortical network is necessary for route planning. Given that the discussion is already quite long, we decided to omit a more detailed discussion of the possible role of the medial septum (which is the focus of the papers cited by the reviewer).

Very minor points

(A) In the introduction, "one study" begins the sentence but there is a second reference.

Thank you, we have rephrased the sentence.

(B) Also in the introduction, it could be helpful to have an operational definition of theta cycle skipping (i.e., 'enhanced rhythmicity at half theta frequency').

We followed the reviewer’s suggestion.

(C) The others should be more explicit in the introduction about their main question. Theta cycle skipping exists in CA1, and then import some of the explanations mentioned in the discussion to the introduction (i.e., attractors states of multiple routes). The main question is then whether this phenomenon, and others from CA1, translate to the output in LS.

We have edited the introduction to more clearly state the main question of our study, following the suggestion from the reviewer.

(D) There are a few instances of extra closing parentheses.

We checked the text but did not find instances of erroneous extra closing parentheses. There are instances of nested parentheses, which may have given the impression that closing parentheses were duplicated.

(E) The first paragraph of the Discussion lacks sufficient references.

We have now added references to the first paragraph of the discussion.

(F) At the end of the 2nd paragraph in the Discussion, the comparison is missing. More than what? It's not until the next reference that one can assume that the authors are referring to a dorsal/ventral axis. However, the physiological motivation for this comparison is lacking. Why would one expect a dorsal/intermediate continuum for theta modulation as there is along the dorsal/ventral axis of the hippocampus?

Thank you for spotting this omission. We have rewritten the paragraph to more clearly make the parallel between dorsal-ventral gradients in the lateral septum and hippocampus and how this relates to the topographical connections between the two structures.

Author response:

The following is the authors’ response to the original reviews.

Thank you very much for the careful and positive reviews of our manuscript. We have addressed each comment in the attached revised manuscript. We describe the modifications below. To avoid confusion, we've changed supplementary figure and table captions to start with "Supplement Figure" and "Supplementary Table," instead of "Figure" and "Table."

We have modified/added:

● Supplementary Table S1: AUC scores for the top 10 frequent epitope types (pathogens) in the testing set of epitope split.

● Supplementary Table S5: AUCs of TCR-epitope binding affinity prediction models with BLOSUM62 to embed epitope sequences.

● Supplementary Table S6: AUCs of TCR-epitope binding affinity prediction models trained on catELMo TCR embeddings and random-initialized epitope embeddings.

● Supplementary Table S7: AUCs of TCR-epitope binding affinity prediction models trained on catELMo and BLOSUM62 embeddings.

● Supplementary Figure 4: TCR clustering performance for the top 34 abundant epitopes representing 70.55% of TCRs in our collected databases.

● Section Discussion.

● Section 4.1 Data: TCR-epitope pairs for binding affinity prediction.

● Section 4.4.2 Epitope-specific TCR clustering.

Public Reviews:

Reviewer #1 (Public Review):

In this manuscript, the authors described a computational method catELMo for embedding TCR CDR3 sequences into numeric vectors using a deep-learning-based approach, ELMo. The authors applied catELMo to two applications: supervised TCR-epitope binding affinity prediction and unsupervised epitope-specific TCR clustering. In both applications, the authors showed that catELMo generated significantly better binding prediction and clustering performance than other established TCR embedding methods. However, there are a few major concerns that need to be addressed.

(1) There are other TCR CDR3 embedding methods in addition to TCRBert. The authors may consider incorporating a few more methods in the evaluation, such as TESSA (PMCID: PMC7799492), DeepTCR (PMCID: PMC7952906) and the embedding method in ATM-TCR (reference 10 in the manuscript). TESSA is also the embedding method in pMTnet, which is another TCR-epitope binding prediction method and is the reference 12 mentioned in this manuscript.

TESSA is designed for characterizing TCR repertoires, so we initially excluded it from the comparison. Our focus was on models developed specifically for amino acid embedding rather than TCR repertoire characterization. However, to address the reviewer's inquiry, we conducted further evaluations. Since both TESSA and DeepTCR used autoencoder-based models to embed TCR sequences, we selected one used in TESSA for evaluation in our downstream prediction task, conducting ten trials in total. It achieved an average AUC of 75.69 in TCR split and 73.3 in epitope split. Notably, catELMo significantly outperformed such performance with an AUC of 96.04 in TCR split and 94.10 in epitope split.

Regarding the embedding method in ATM-TCR, it simply uses BLOSUM as an embedding matrix which we have already compared in Section 2.1. Furthermore, we have provided the comparison results between our prediction model trained on catELMo embeddings with the state-of-the-art prediction models such as netTCR and ATM-TCR in Table 6 of the Discussion section.

(2) The TCR training data for catELMo is obtained from ImmunoSEQ platform, including SARS-CoV2, EBV, CMV, and other disease samples. Meanwhile, antigens related to these diseases and their associated TCRs are extensively annotated in databases VDJdb, IEDB and McPAS-TCR. The authors then utilized the curated TCR-epitope pairs from these databases to conduct the evaluations for eptitope binding prediction and TCR clustering. Therefore, the training data for TCR embedding may already be implicitly tuned for better representations of the TCRs used in the evaluations. This seems to be true based on Table 4, as BERT-Base-TCR outperformed TCRBert. Could catELMo be trained on PIRD as TCRBert to demonstrate catELMo's embedding for TCRs targeting unseen diseases/epitopes?

We would like to note that catELMo was trained exclusively on TCR sequences in an unsupervised manner, which means it has never been exposed to antigen information. We also ensured that the TCRs used in catELMo's training did not overlap with our downstream prediction data. Please refer to the section 4.1 Data where we explicitly stated, “We note that it includes no identical TCR sequences with the TCRs used for training the embedding models.”. Moreover, the performance gap (~1%) between BERT-Base-TCR and TCRBert, as observed in Table 4, is relatively small, especially when compared to the performance difference (>16%) between catELMo and TCRBert.

To further address this concern, we conducted experiments using the same number of TCRs, 4,173,895 in total, sourced exclusively from healthy ImmunoSeq repertoires. This alternative catELMo model demonstrated a similar prediction performance (based on 10 trials) to the one reported in our paper, with an average AUC of 96.35% in TCR split and an average AUC of 94.03% in epitope split.

We opted not to train catELMo on the PIRD dataset for several reasons. First, approximately 7.8% of the sequences in PIRD also appear in our downstream prediction data, which could be a potential source of bias. Furthermore, PIRD encompasses sequences related to diseases such as Tuberculosis, HIV, CMV, among others, which the reviewer is concerned about.

(3) In the application of TCR-epitope binding prediction, the authors mentioned that the model for embedding epitope sequences was catElMo, but how about for other methods, such as TCRBert? Do the other methods also use catELMo-embedded epitope sequences as part of the binding prediction model, or use their own model to embed the epitope sequences? Since the manuscript focuses on TCR embedding, it would be nice for other methods to be evaluated on the same epitope embedding (maybe adjusted to the same embedded vector length).

Furthermore, the authors found that catELMo requires less training data to achieve better performance. So one would think the other methods could not learn a reasonable epitope embedding with limited epitope data, and catELMo's better performance in binding prediction is mainly due to better epitope representation.

Review 1 and 3 have raised similar concerns regarding the epitope embedding approach employed in our binding affinity prediction models. We address both comments together on page 6 where we discuss the epitope embedding strategies in detail.

(4) In the epitope binding prediction evaluation, the authors generated the test data using TCR-epitope pairs from VDJdb, IEDB, McPAS, which may be dominated by epitopes from CMV. Could the authors show accuracy categorized by epitope types, i.e. the accuracy for TCR-CMV pair and accuracy for TCR-SARs-CoV2 separately?

The categorized AUC scores have been added in Supplementary Table 7. We observed significant performance boosts from catELMo compared with other embedding models.

(5) In the unsupervised TCR clustering evaluation, since GIANA and TCRdist direct outputs the clustering result, so they should not be affected by hierarchical clusters. Why did the curves of GIANA and TCRdist change in Figure 4 when relaxing the hierarchical clustering threshold?

For fair comparisons, we performed GIANA and TCRdist with hierarchical clustering instead of the nearest neighbor search. We have clarified it in the revised manuscript as follows.

“Both methods are developed on the BLOSUM62 matrix and apply nearest neighbor search to cluster TCR sequences. GIANA used the CDR3 of TCRβ chain and V gene, while TCRdist predominantly experimented with CDR1, CDR2, and CDR3 from both TCRα and TCRβ chains. For fair comparisons, we perform GIANA and TCRdist only on CDR3 β chains and with hierarchical clustering instead of the nearest neighbor search.”

(6 & 7) In the unsupervised TCR clustering evaluation, the authors examined the TCR related to the top eight epitopes. However, there are much more epitopes curated in VDJdb, IEDB and McPAS-TCR. In real application, the potential epitopes is also more complex than just eight epitopes. Could the authors evaluate the clustering result using all the TCR data from the databases? In addition to NMI, it is important to know how specific each TCR cluster is. Could the authors add the fraction of pure clusters in the results? Pure cluster means all the TCRs in the cluster are binding to the same epitope, and is a metric used in the method GIANA.

We would like to note that there is a significant disparity in TCR binding frequencies across different epitopes in current databases. For instance, the most abundant epitope (KLGGALQAK) has approximately 13k TCRs binding to it, while 836 out of 982 epitopes are associated with fewer than 100 TCRs in our dataset. Furthermore, there are 9347 TCRs having the ability to bind multiple epitopes. In order to robustly evaluate the clustering performance, we originally selected the top eight frequent epitopes from McPAS and removed TCRs binding multiple epitopes to create a more balanced dataset.

We acknowledge that the real-world scenario is more complex than just eight epitopes. Therefore, we conducted clustering experiments using the top most abundant epitopes whose combined cognate TCRs make up at least 70% of TCRs across three databases (34 epitopes). This is illustrated in Supplementary Figure 5. Furthermore, we extended our analysis by clustering all TCRs after filtering out those that bind to multiple epitopes, resulting in 782 unique epitopes. We found that catELMo achieved the 3rd and 2nd best performance in NMI and Purity, respectively (see Table below). These are aligned with our previous observations of the eight epitopes.

Author response table 1.

Reviewer #2 (Public Review):

In the manuscript, the authors highlighted the importance of T-cell receptor (TCR) analysis and the lack of amino acid embedding methods specific to this domain. The authors proposed a novel bi-directional context-aware amino acid embedding method, catELMo, adapted from ELMo (Embeddings from Language Models), specifically designed for TCR analysis. The model is trained on TCR sequences from seven projects in the ImmunoSEQ database, instead of the generic protein sequences. They assessed the effectiveness of the proposed method in both TCR-epitope binding affinity prediction, a supervised task, and the unsupervised TCR clustering task. The results demonstrate significant performance improvements compared to existing embedding models. The authors also aimed to provide and discuss their observations on embedding model design for TCR analysis: 1) Models specifically trained on TCR sequences have better performance than models trained on general protein sequences for the TCR-related tasks; and 2) The proposed ELMo-based method outperforms TCR embedding models with BERT-based architecture. The authors also provided a comprehensive introduction and investigation of existing amino acid embedding methods. Overall, the paper is well-written and well-organized.

The work has originality and has potential prospects for immune response analysis and immunotherapy exploration. TCR-epitope pair binding plays a significant role in T cell regulation. Accurate prediction and analysis of TCR sequences are crucial for comprehending the biological foundations of binding mechanisms and advancing immunotherapy approaches. The proposed embedding method presents an efficient context-aware mathematical representation for TCR sequences, enabling the capture and analysis of their structural and functional characteristics. This method serves as a valuable tool for various downstream analyses and is essential for a wide range of applications. Thank you.

Reviewer #3 (Public Review):

Here, the authors trained catElMo, a new context-aware embedding model for TCRβ CDR3 amino acid sequences for TCR-epitope specificity and clustering tasks. This method benchmarked existing work in protein and TCR language models and investigated the role that model architecture plays in the prediction performance. The major strength of this paper is comprehensively evaluating common model architectures used, which is useful for practitioners in the field. However, some key details were missing to assess whether the benchmarking study is a fair comparison between different architectures. Major comments are as follows:

• It is not clear why epitope sequences were also embedded using catELMo for the binding prediction task. Because catELMO is trained on TCRβ CDR3 sequences, it's not clear what benefit would come from this embedding. Were the other embedding models under comparison also applied to both the TCR and epitope sequences? It may be a fairer comparison if a single method is used to encode epitope sequence for all models under comparison, so that the performance reflects the quality of the TCR embedding only.

In our study, we indeed used the same embedding model for both TCRs and epitopes in each prediction model, ensuring a consistent approach throughout.

Recognizing the importance of evaluating the impact of epitope embeddings, we conducted experiments in which we used BLOSUM62 matrix to embed epitope sequences for all models. The results (Supplementary Table 5) are well aligned with the performance reported in our paper. This suggests that epitope embedding may not play as critical a role as TCR embedding in the prediction tasks. To further validate this point, we conducted two additional experiments.

Firstly, we used catELMo to embed TCRs while employing randomly initialized embedding matrices with trainable parameters for epitope sequences. It yielded similar prediction performance as when catELMo was used for both TCR and epitope embedding (Supplementary Table 6). Secondly, we utilized BLOSUM62 to embed TCRs but employed catELMo for epitope sequence embedding, resulting in performance comparable to using BLOSUM62 for both TCRs and epitopes (Supplementary Table 4). These experiment results confirmed the limited impact of epitope embedding on downstream performance.

We conjecture that these results may be attributed to the significant disparity in data scale between TCRs (~290k) and epitopes (less than 1k). Moreover, TCRs tend to exhibit high similarity, whereas epitopes display greater distinctiveness from one another. These features of TCRs require robust embeddings to facilitate effective separation and improve downstream performance, while epitope embedding primarily serves as a categorical encoding.

We have included a detailed discussion of these findings in the revised manuscript to provide a comprehensive understanding of the role of epitope embeddings in TCR binding prediction.

• The tSNE visualization in Figure 3 is helpful. It makes sense that the last hidden layer features separate well by binding labels for the better performing models. However, it would be useful to know if positive and negative TCRs for each epitope group also separate well in the original TCR embedding space. In other words, how much separation between these groups is due to the neural network vs just the embedding?

It is important to note that we used the same downstream prediction model, a simple three-linear-layer network, for all the discussed embedding methods. We believe that the separation observed in the t-SNE visualization effectively reflects the ability of our embedding model. Also, we would like to mention that it can be hard to see a clear distinction between positive and negative TCRs in the original embedding space because embedding models were not trained on positive/negative labels. Please refer to the t-SNE of the original TCR embeddings below.

Author response image 1.

• To generate negative samples, the author randomly paired TCRs from healthy subjects to different epitopes. This could produce issues with false negatives if the epitopes used are common. Is there an estimate for how frequently there might be false negatives for those commonly occurring epitopes that most populations might also have been exposed to? Could there be a potential batch effect for the negative sampled TCR that confounds with the performance evaluation?

Thank you for bringing this valid and interesting point up. Generating negative samples is non-trivial since only a limited number of non-binding TCR-pairs are publicly available and experimentally validating non-binding pairs is costly [1]. Standard practices for generating negative pairs are (1) paring epitopes with healthy TCRs [2, 3], and (2) randomly shuffling existing TCR-epitope pairs [4,5]. We used both approaches (the former included in the main results, and the latter in the discussion). In both scenarios, catELMo embeddings consistently demonstrated superior performance.

We acknowledge the possibility of false negatives due to the finite-sized TCR database from which we randomly selected TCRs, however, we believe that the likelihood of such occurrences is low. Given the vast diversity of human TCR clonotypes, which can exceed 10^15[6], the chance of randomly selecting a TCR that specifically recognizes a target epitope is relatively small.

In order to investigate the batch effect, we generated new negative pairs using different seeds and observed consistent prediction performance across these variations. However, we agree that there could still be a potential batch effect for the negative samples due to potential data bias.

We have discussed the limitation of generative negative samples in the revised manuscript.

• Most of the models being compared were trained on general proteins rather than TCR sequences. This makes their comparison to catELMO questionable since it's not clear if the improvement is due to the training data or architecture. The authors partially addressed this with BERT-based models in section 2.4. This concern would be more fully addressed if the authors also trained the Doc2vec model (Yang et al, Figure 2) on TCR sequences as baseline models instead of using the original models trained on general protein sequences. This would make clear the strength of context-aware embeddings if the performance is worse than catElmo and BERT.

We agree it is important to distinguish between the effects of training data and architecture on model performance.

In Section 2.4, as the reviewer mentioned, we compared catELMo with BERT-based models trained on the same TCR repertoire data, demonstrating that architecture plays a significant role in improving performance. Furthermore, in Section 2.5, we compared catELMo-shallow with SeqVec, which share the same architecture but were trained on different data, highlighting the importance of data on the model performance.

To further address the reviewer's concern, we trained a Doc2Vec model on the TCR sequences that have been used for catELMo training. We observed significantly lower prediction performance compared to catELMo, with an average AUC of 50.24% in TCR split and an average AUC of 51.02% in epitope split, making the strength of context-aware embeddings clear.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

(1) It is known that TRB CDR3, the CDR1, CDR2 on TRBV gene and the TCR alpha chain also contribute to epitope recognition, but were not modeled in catELMo. It would be nice for the authors to add this as a current limitation for catELMo in the Discussion section.

We have discussed the limitation in the revised manuscript.

“Our study focuses on modeling the TCRβ chain CDR3 region, which is known as the primary determinant of epitope binding. Other regions, such as CDR1 and CDR2 on the TRB V gene, along with the TCRα chain, may also contribute to specificity in antigen recognition. However, a limited number of available samples for those additional features can be a challenge for training embedding models. Future work may explore strategies to incorporate these regions while mitigating the challenges of working with limited samples.”

(2) I tried to follow the instructions to train a binding affinity prediction model for TCR-epitope pairs, however, the cachetools=5.3.0 seems could not be found when running "pip install -r requirements.txt" in the conda environment bap. Is this cachetools version supported after Python 3.7 so the Python 3.6.13 suggested on the GitHub repo might not work?

This has been fixed. We have updated the README.md on our github page.

Reviewer #2 (Recommendations For The Authors):

The article is well-constructed and well-written, and the analysis is comprehensive.

The comments for minor issues that I have are as follows:

(1) In the Methods section, it will be clearer if the authors interpret more on how the standard deviation is calculated in all tables. How to define the '10 trials'? Are they based on different random training and test set splits?

‘10 trials' refers to the process of splitting the dataset into training, validation, and testing sets using different seeds for each trial. Different trials have different training, validation, and testing sets. For each trial, we trained a prediction model on its training set and measured performance on its testing set. The standard deviation was calculated from the 10 measurements, estimating model performance variation across different random splits of the data.

(2) The format of AUCs and the improvement of AUCs need to be consistent, i.e., with the percent sign.

We have updated the format of AUCs.

Reviewer #3 (Recommendations For The Authors):

In addition to the recommendations in the public review, we had the following more minor questions and recommendations:

• Could you provide some more background on the data, such as overlaps between the databases, and how the training and validation split was performed between the three databases? Also summary statistics on the length of TCR and epitope sequence data would be helpful.

We have provided more details about data in our revision.

• Could you comment on the runtime to train and embed using the catELMo and BERT models?

Our training data is TCR sequences with relatively short lengths (averaging less than 20 amino acid residues). Such characteristic significantly reduces the computational resources required compared to training large-scale language models on extensive text corpora. Leveraging standard machines equipped with two GeForce RTX 2080 GPUs, we were able to complete the training tasks within a matter of days. After training, embedding one sequence can be accomplished in a matter of seconds.

• Typos and wording:

• Table 1 first row of "source": "immunoSEQ" instead of "immuneSEQ"

This has been corrected.

• L23 of abstract "negates the need of complex deep neural network architecture" is a little confusing because ELMo itself is a deep neural network architecture. Perhaps be more specific and add that the need is for downstream tasks.

We have made it more specific in our abstract.

“...negates the need for complex deep neural network architecture in downstream tasks.”

References

(1) Montemurro, Alessandro, et al. "NetTCR-2.0 enables accurate prediction of TCR-peptide binding by using paired TCRα and β sequence data." Communications biology 4.1 (2021): 1060.

(2) Jurtz, Vanessa Isabell, et al. "NetTCR: sequence-based prediction of TCR binding to peptide-MHC complexes using convolutional neural networks." BioRxiv (2018): 433706.

(3) Gielis, Sofie, et al. "Detection of enriched T cell epitope specificity in full T cell receptor sequence repertoires." Frontiers in immunology 10 (2019): 2820.

(4) Cai, Michael, et al. "ATM-TCR: TCR-epitope binding affinity prediction using a multi-head self-attention model." Frontiers in Immunology 13 (2022): 893247.

(5) Weber, Anna, et al. "TITAN: T-cell receptor specificity prediction with bimodal attention networks." Bioinformatics 37 (2021): i237-i244.

(6) Lythe, Grant, et al. "How many TCR clonotypes does a body maintain?." Journal of theoretical biology 389 (2016): 214-224.

Author response:

The following is the authors’ response to the original reviews.

Public Reviews:

Reviewer #1 (Public Review):

Summary:

The authors seek to establish what aspects of nervous system structure and function may explain behavioral differences across individual fruit flies. The behavior in question is a preference for one odor or another in a choice assay. The variables related to neural function are odor responses in olfactory receptor neurons or in the second-order projection neurons, measured via calcium imaging. A different variable related to neural structure is the density of a presynaptic protein BRP. The authors measure these variables in the same fly along with the behavioral bias in the odor assays. Then they look for correlations across flies between the structure-function data and the behavior.

Strengths:

Where behavioral biases originate is a question of fundamental interest in the field. In an earlier paper (Honegger 2019) this group showed that flies do vary with regard to odor preference, and that there exists neural variation in olfactory circuits, but did not connect the two in the same animal. Here they do, which is a categorical advance, and opens the door to establishing a correlation. The authors inspect many such possible correlations. The underlying experiments reflect a great deal of work, and appear to be done carefully. The reporting is clear and transparent: All the data underlying the conclusions are shown, and associated code is available online.

We are glad to hear the reviewer is supportive of the general question and approach.

Weaknesses:

The results are overstated. The correlations reported here are uniformly small, and don't inspire confidence that there is any causal connection. The main problems are

Our revision overhauls the interpretation of the results to prioritize the results we have high confidence in (specifically, PC 2 of our Ca++ data as a predictor of OCT-MCH preference) versus results that are suggestive but not definitive (such as PC 1 of Ca++ data as a predictor of Air-OCT preference).

It’s true that the correlations are small, with R2 values typically in the 0.1-0.2 range. That said, we would call it a victory if we could explain 10 to 20% of the variance of a behavior measure, captured in a 3 minute experiment, with a circuit correlate. This is particularly true because, as the reviewer notes, the behavioral measurement is noisy.

(1) The target effect to be explained is itself very weak. Odor preference of a given fly varies considerably across time. The systematic bias distinguishing one fly from another is small compared to the variability. Because the neural measurements are by necessity separated in time from the behavior, this noise places serious limits on any correlation between the two.

This is broadly correct, though to quibble, it’s our measurement of odor preference which varies considerably over time. We are reasonably confident that more variance in our measurements can be attributed to sampling error than changes to true preference over time. As evidence, the correlation in sequential measures of individual odor preference, with delays of 3 hours or 24 hours, are not obviously different. We are separately working on methodological improvements to get more precise estimates of persistent individual odor preference, using averages of multiple, spaced measurements. This is promising, but beyond the scope of this study.

(2) The correlations reported here are uniformly weak and not robust. In several of the key figures, the elimination of one or two outlier flies completely abolishes the relationship. The confidence bounds on the claimed correlations are very broad. These uncertainties propagate to undermine the eventual claims for a correspondence between neural and behavioral measures.

We are broadly receptive to this criticism. The lack of robustness of some results comes from the fundamental challenge of this work: measuring behavior is noisy at the individual level. Measuring Ca++ is also somewhat noisy. Correlating the two will be underpowered unless the sample size is huge (which is impractical, as each data point requires a dissection and live imaging session) or the effect size is large (which is generally not the case in biology). In the current version we tried in some sense to avoid discussing these challenges head-on, instead trying to focus on what we thought were the conclusions justified by our experiments with sample sizes ranging from 20 to 60. Our revision is more candid about these challenges.

That said, we believe the result we view as the most exciting — that PC2 of Ca++ responses predicts OCT-MCH preference — is robust. 1) It is based on a training set with 47 individuals and a test set composed of 22 individuals. The p-value is sufficiently low in each of these sets (0.0063 and 0.0069, respectively) to pass an overly stringent Bonferroni correction for the 5 tests (each PC) in this analysis. 2) The BRP immunohistochemistry provides independent evidence that is consistent with this result — PC2 that predicts behavior (p = 0.03 from only one test) and has loadings that contrast DC2 and DM2. Taken together, these results are well above the field-standard bar of statistical robustness.

In our revision, we are explicit that this is the (one) result we have high confidence in. We believe this result convincingly links Ca++ and behavior, and warrants spotlighting. We have less confidence in other results, and say so, and we hope this addresses concerns about overstating our results.

(3) Some aspects of the statistical treatment are unusual. Typically a model is proposed for the relationship between neuronal signals and behavior, and the model predictions are correlated with the actual behavioral data. The normal practice is to train the model on part of the data and test it on another part. But here the training set at times includes the testing set, which tends to give high correlations from overfitting. Other times the testing set gives much higher correlations than the training set, and then the results from the testing set are reported. Where the authors explored many possible relationships, it is unclear whether the significance tests account for the many tested hypotheses. The main text quotes the key results without confidence limits.

Our primary analyses are exactly what the reviewer describes, scatter plots and correlations of actual behavioral measures against predicted measures. We produced test data in separate experiments, conducted weeks to months after models were fit on training data. This is more rigorous than splitting into training and test sets data collected in a single session, as batch/environmental effects reduce the independence of data collected within a single session.

We only collected a test set when our training set produced a promising correlation between predicted and actual behavioral measures. We never used data from test sets to train models. In our main figures, we showed scatter plots that combined test and training data, as the training and test partitions had similar correlations.

We are unsure what the reviewer means by instances where we explored many possible relationships. The greatest number of comparisons that could lead to the rejection of a null hypothesis was 5 (corresponding to the top 5 PCs of Ca++ response variation or Brp signal). We were explicit that the p-values reported were nominal. As mentioned above, applying a Bonferroni correction for n=5 comparisons to either the training or test correlations from the Ca++ to OCT-MCH preference model remains significant at alpha=0.05.

Our revision includes confidence intervals around ⍴signal for the PN PC2 OCT-MCH model, and for the ORN Brp-Short PC2 OCT-MCH model (lines 170-172, 238)

Reviewer #2 (Public Review):

Summary:

The authors aimed to identify the neural sources of behavioral variation in a decision between odor and air, or between two odors.

Strengths:

-The question is of fundamental importance.

-The behavioral studies are automated, and high-throughput.

-The data analyses are sophisticated and appropriate.

-The paper is clear and well-written aside from some strong wording.

-The figures beautifully illustrate their results.

-The modeling efforts mechanistically ground observed data correlations.

We are glad to read that the reviewer sees these strengths in the study. We hope the current revision addresses the strong wording.

Weaknesses:

-The correlations between behavioral variations and neural activity/synapse morphology are (i) relatively weak, (ii) framed using the inappropriate words "predict", "link", and "explain", and (iii) sometimes non-intuitive (e.g., PC 1 of neural activity).

Taking each of these points in turn:

i) It would indeed be nicer if our empirical correlations are higher. One quibble: we primarily report relatively weak correlations between measurements of behavior and Ca++/Brp. This could be the case even when the correlation between true behavior and Ca++/Brp is higher. Our analysis of the potential correlation between latent behavioral and Ca++ signals was an attempt to tease these relationships apart. The analysis suggests that there could, in fact, be a high underlying correlation between behavior and these circuit features (though the error bars on these inferences are wide).

ii) We worked to ensure such words are used appropriately. “Predict” can often be appropriate in this context, as a model predicts true data values. Explain can also be appropriate, as X “explaining” a portion of the variance of Y is synonymous with X and Y being correlated. We cannot think of formal uses of “link,” and have revised the manuscript to resolve any inappropriate word choice.

iii) If the underlying biology is rooted in non-intuitive relationships, there’s unfortunately not much we can do about it. We chose to use PCs of our Ca++/Brp data as predictors to deal with the challenge of having many potential predictors (odor-glomerular responses) and relatively few output variables (behavioral bias). Thus, using PCs is a conservative approach to deal with multiple comparisons. Because PCs are just linear transformations of the original data, interpreting them is relatively easy, and in interpreting PC1 and PC2, we were able to identify simple interpretations (total activity and the difference between DC2 and DM2 activation, respectively). All in all, we remain satisfied with this approach as a means to both 1) limit multiple comparisons and 2) interpret simple meanings from predictive PCs.

No attempts were made to perturb the relevant circuits to establish a causal relationship between behavioral variations and functional/morphological variations.

We did conduct such experiments, but we did not report them because they had negative results that we could not definitively interpret. We used constitutive and inducible effectors to alter the physiology of ORNs projecting to DC2 and DM2. We also used UAS-LRP4 and UAS-LRP4-RNAi to attempt to increase and decrease the extent of Brp puncta in ORNs projecting to DC2 and DM2. None of these manipulations had a significant effect on mean odor preference in the OCT-MCH choice, which was the behavioral focus of these experiments. We were unable to determine if the effectors had the intended effects in the targeted Gal4 lines, particularly in the LRP experiments, so we could not rule out that our negative finding reflected a technical failure.

Author response image 1.

We believe that even if these negative results are not technical failures, they are not necessarily inconsistent with the analyses correlating features of DC2 and DM2 to behavior. Specifically, we suspect that there are correlated fluctuations in glomerular Ca++ responses and Brp across individuals, due to fluctuations in the developmental spatial patterning of the antennal lobe. Thus, the DC2-DM2 predictor may represent a slice/subset of predictors distributed across the antennal lobe. This would also explain how we “got lucky” to find two glomeruli as predictors of behavior, when we were only able to image a small portion of the glomeruli.

Reviewer #3 (Public Review):

Churgin et. al. seeks to understand the neural substrates of individual odor preference in the Drosophila antennal lobe, using paired behavioral testing and calcium imaging from ORNs and PNs in the same flies, and testing whether ORN and PN odor responses can predict behavioral preference. The manuscript's main claims are that ORN activity in response to a panel of odors is predictive of the individual's preference for 3-octanol (3-OCT) relative to clean air, and that activity in the projection neurons is predictive of both 3-OCT vs. air preference and 3-OCT vs. 4-methylcyclohexanol (MCH). They find that the difference in density of fluorescently-tagged brp (a presynaptic marker) in two glomeruli (DC2 and DM2) trends towards predicting behavioral preference between 3-oct vs. MCH. Implementing a model of the antennal lobe based on the available connectome data, they find that glomerulus-level variation in response reminiscent of the variation that they observe can be generated by resampling variables associated with the glomeruli, such as ORN identity and glomerular synapse density.

Strengths:

The authors investigate a highly significant and impactful problem of interest to all experimental biologists, nearly all of whom must often conduct their measurements in many different individuals and so have a vested interest in understanding this problem. The manuscript represents a lot of work, with challenging paired behavioral and neural measurements.

Weaknesses:

The overall impression is that the authors are attempting to explain complex, highly variable behavioral output with a comparatively limited set of neural measurements.

We would say that we are attempting to explain a simple, highly variable behavioral measure with a comparatively limited set of neural measurements, i.e. we make no claims to explain the complex behavioral components of odor choice, like locomotion, reversals at the odor boundary, etc.

Given the degree of behavioral variability they observe within an individual (Figure 1- supp 1) which implies temporal/state/measurement variation in behavior, it's unclear that their degree of sampling can resolve true individual variability (what they call "idiosyncrasy") in neural responses, given the additional temporal/state/measurement variation in neural responses.

We are confident that different Ca++ recordings are statistically different. This is borne out in the analysis of repeated Ca++ recordings in this study, which finds that the significant PCs of Ca++ variation contain 77% of the variation in that data. That this variation is persistent over time and across hemispheres was assessed in Honegger & Smith, et al., 2019. We are thus confident that there is true individuality in neural responses (Note, we prefer not to call it “individual variability” as this could refer to variability within individuals, not variability across individuals.) It is a separate question of whether individual differences in neural responses bear some relation to individual differences in behavioral biases. That was the focus of this study, and our finding of a robust correlation between PC 2 of Ca++ responses and OCT-MCH preference indicates a relation. Because behavior and Ca++ were collected with an hours-to-day long gap, this implies that there are latent versions of both behavioral bias and Ca++ response that are stable on timescales at least that long.

The statistical analyses in the manuscript are underdeveloped, and it's unclear the degree to which the correlations reported have explanatory (causative) power in accounting for organismal behavior.

With respect, we do not think our statistical analyses are underdeveloped, though we acknowledge that the detailed reviewer suggestions included the helpful suggestion to include uncertainty in the estimation of confidence intervals around the point estimate of the strength of correlation between latent behavioral and Ca++ response states – we have added these for the PN PC2 linear model (lines 170-172).

It is indeed a separate question whether the correlations we observed represent causal links from Ca++ to behavior (though our yoked experiment suggests there is not a behavior-to-Ca++ causal relationship — at least one where odor experience through behavior is an upstream cause). We attempted to be precise in indicating that our observations are correlations. That is why we used that word in the title, as an example. In the revision, we worked to ensure this is appropriately reflected in all word choice across the paper.

Recommendations for the Authors:

Reviewer #1 (Recommendations for the Authors):

Detailed comments: Many of the problems can be identified starting from Figure 4, which summarizes the main claims. I will focus on that figure and its tributaries.

Acknowledging that the strength of several of our inferences are weak compared to what we consider the main result (the relationship between PC2 of Ca++ and OCT-MCH preference),we have removed Figure 4. This makes the focus of the paper much clearer and appropriately puts focus on the results that have strong statistical support.

(1) The process of "inferring" correlation among the unobserved latent states for neural sensitivity and behavioral bias is unconventional and risky. The larger the assumed noise linking the latent to the observed variables (i.e. the smaller r_b and r_c) the bigger the inferred correlation rho from a given observed correlation R^2_cb. In this situation, the value of the inferred rho becomes highly dependent on what model one assumes that links latent to observed states. But the specific model drawn in Fig 4 suppl 1 is just one of many possible guesses. For example, models with nonlinear interactions could produce different inference.

We agree with the reviewer’s notes of caution. To be clear, we do not intend for this analysis to be the main takeaway of the paper and have revised it to make this clear. The signal we are most confident in is the simple correlation between measured Ca++ PC2 and measured behavior. We have added more careful language saying that the attempt to infer the correlation between latent signals is one attempt at describing the data generation process (lines 166-172), and one possible estimate of an “underlying” correlation.

(2) If one still wanted to go through with this inference process and set confidence bounds on rho, one needs to include all the uncertainties. Here the authors only include uncertainty in the value of R^2_c,b and they peg that at +/-20% (Line 1367). In addition there is plenty of uncertainty associated also with R^2_c,c and R^2_b,b. This will propagate into a wider confidence interval on rho.

We have replaced the arbitrary +/- 20% window with bootstrapping the pairs of (predicted preference by PN PC2, measured preference) points and getting a bootstrap distribution of R2c,b, which is, not surprisingly, considerably wider. Still, we think there is some value in this analysis as the 90% CI of 𝜌signal under this model is 0.24-0.95. That is, including uncertainty about the R2b,b and R2c,c in the model still implies a significant relationship between latent calcium and behavior signals.

(2.1) The uncertainty in R^2_cb is much greater than +/-20%. Take for example the highest correlation quoted in Fig 4: R^2=0.23 in the top row of panel A. This relationship refers to Fig 1L. Based on bootstrapping from this data set, I find a 90% confidence interval of CI=[0.002, 0.527]. That's an uncertainty of -100/+140%, not +/-20%. Moreover, this correlation is due entirely to the lone outlier on the bottom left. Removing that single fly abolishes any correlation in the data (R^2=0.04, p>0.3). With that the correlation of rho=0.64, the second-largest effect in Fig 4, disappears.

We acknowledge that removal of the outlier in Fig 1L abolishes the correlation between predicted and measured OCT-AIR preference. We have thus moved that subfigure to the supplement (now Figure 1 – figure supplement 10B), note that we do not have robust statistical support of ORN PC1 predicting OCT-AIR preference in the results (lines 177-178), and place our emphasis on PN PC2’s capacity to predict OCT-MCH preference throughout the text.

(2.2) Similarly with the bottom line of Fig 4A, which relies on Fig 1M. With the data as plotted, the confidence interval on R^2 is CI=[0.007, 0.201], again an uncertainty of -100/+140%. There are two clear outlier points, and if one removes those, the correlation disappears entirely (R^2=0.06, p=0.09).

We acknowledge that removal of the two outliers in Fig 1M between predicted and measured OCT-AIR preference abolishes the correlation. We have also moved that subfigure to the supplement (now Figure 1 – figure supplement 10F) and do not claim to have robust statistical support of PN PC1 predicting OCT-AIR preference.

(2.3) Similarly, the correlation R^2_bb of behavior with itself is weak and comes with great uncertainty (Fig 1 Suppl 1, panels B-E). For example, panel D figures prominently in computing the large inferred correlation of 0.75 between PN responses and OCT-MCH choice (Line 171ff). That correlation is weak and has a very wide confidence interval CI=[0.018, 0.329]. This uncertainty about R^2_bb should be taken into account when computing the likelihood of rho.

We now include bootstrapping of the 3 hour OCT-MCH persistence data in our inference of 𝜌signal.

(2.4) The correlation R^2_cc for the empirical repeatability of Ca signals seems to be obtained by a different method. Fig 4 suppl 1 focuses on the repeatability of calcium recording at two different time points. But Line 625ff suggests the correlation R^2_cc=0.77 all derives from one time point. It is unclear how these are related.

Because our calcium model predictors utilize principal components of the glomerulus-odor responses (the mean Δf/f in the odor presentation window), we compute R2c,c through adding variance explained along the PCs, up to the point in which the component-wise variance explained does not exceed that of shuffled data (lines 609-620 in Materials and Methods). In this revision we now bootstrap the calcium data on the level of individual flies to get a bootstrap distribution of R2c,c, and propagate the uncertainty forward in the inference of 𝜌signal.

(2.5) To summarize, two of the key relationships in Fig 1 are due entirely to one or two outlier points. These should not even be used for further analysis, yet they underlie two of the claims in Fig 4. The other correlations are weak, and come with great uncertainty, as confirmed by resampling. Those uncertainties should be propagated through the inference procedure described in Fig 4. It seems possible that the result will be entirely uninformative, leaving rho with a confidence interval that spans the entire available range [0,1]. Until that analysis is done, the claims of neuron-to-behavior correlation in this manuscript are not convincing.

It is important to note that we never thought our analysis of the relationship between latent behavior and calcium signals should be interpreted as the main finding. Instead, the observed correlation between measured behavior and calcium is the take-away result. Importantly, it is also conservative compared to the inferred latent relationship, which in our minds was always a “bonus” analysis. Our revisions are now focused on highlighting the correlations between measured signals that have strong statistical support.

As a response to these specific concerns, we have propagated uncertainty in all R2’s (calcium-calcium, behavior-behavior, calcium-behavior) in our new inference for 𝜌signal, yielding a new median estimate for PN PC 2 underlying OCT-MCH preference of 0.68, with a 90% CI of 0.24-0.95. (Lines 171-172 in results, Inference of correlation between latent calcium and behavior states section in Materials and Methods).

(3) Other statistical methods:

(3.1) The caption of Fig 4 refers to "model applied to train+test data". Does that mean the training data were included in the correlation measurement? Depending on the number of degrees of freedom in the model, this could have led to overfitting.

We have removed Figure 4 and emphasize the key results in Figure 1 and 2 that we see statistically robust signal of PN PC 2 explaining OCT-MCH preference variation in both a training set and a testing set of flies (Fig 2 – figure supplement 1C-D).

(3.2) Line 180 describes a model that performed twice as well on test data (31% EV) as it did on training data (15%). What would explain such an outcome? And how does that affect one's confidence in the 31% number?

The test set recordings were conducted several weeks after the training set recordings, which were used to establish PN PC 2 as a correlate of OCT-MCH preference. The fact that the test data had a higher R2 likely reflects sampling error (these two correlation coefficients are not significantly different). Ultimately this gives us more confidence in our model, as the predictive capacity is maintained in a totally separate set of flies.

(3.340 Multiple models get compared in performance before settling on one. For example, sometimes the first PC is used, sometimes the second. Different weighting schemes appear in Fig 2. Do the quoted p-values for the correlation plots reflect a correction for multiple hypothesis testing?

For all calcium-behavior models, we restricted our analysis to 5 PCs, as the proportion of calcium variance explained by each of these PCs was higher than that explained by the respective PC of shuffled data — i.e., there were at most five significant PCs in that data. We thus performed at most 5 hypothesis tests for a given model. PN PC 2 explained 15% of OCT-MCH preference variation, with a p-value of 0.0063 – this p-value is robust to a conservative Bonferroni correction to the 5 hypotheses considered at alpha=0.05.

The weight schemes in Figure 2 and Figure 1 – figure supplement 10 reflect our interpretations of the salient features of the PCs and are follow-up analysis of the single principal component hypothesis tests. Thus they do not constitute additional tests that should be corrected. We now state in the methods explicitly that all reported p-values are nominal (line 563).

(3.4) Line 165 ff: Quoting rho without giving the confidence interval is misleading. For example, the rho for the presynaptic density model is quoted as 0.51, which would be a sizeable correlation. But in fact, the posterior on rho is almost flat, see caption of Fig 4 suppl 1, which lists the CI as [0.11, 0.85]. That means the experiments place virtually no constraint on rho. If the authors had taken no data at all, the posterior on rho would be uniform, and give a median of 0.5.

We now provide a confidence interval around 𝜌signal for the PN PC 2 model (lines 170-172). But per above, and consistent with the new focus of this revision, we view the 𝜌signal inference as secondary to the simple, significant correlation between PN PC 2 and OCT-MCH preference.

(4) As it stands now, this paper illustrates how difficult it is to come to a strong conclusion in this domain. This may be worth some discussion. This group is probably in a better position than any to identify what are the limiting factors for this kind of research.

We thank the reviewer for this suggestion and have added discussion of the difficulties in detecting signals for this kind of problem. That said, we are confident in stating that there is a meaningful correlation between PC 2 of PN Ca++ responses and OCT-MCH behavior given our model’s performance in predicting preference in a test set of flies, and in the consistent signal in ORN Bruchpilot.

Reviewer #3 (Recommendations for the Authors):

Two major concerns, one experimental/technical and one conceptual:

(1) I appreciate the difficulty of the experimental design and problem. However, the correlations reported throughout are based on neural measurements in only 5 glomeruli (~10% of the olfactory system) at early stages of olfactory processing.

We acknowledge that only imaging 5 glomeruli is regrettable. We worked hard to develop image analysis pipelines that could reliably segment as many glomeruli as possible from almost all individual flies. In the end, we concluded that it was better to focus our analysis on a (small) core set of glomeruli for which we had high confidence in the segmentation. Increasing the number of analyzed glomeruli is high on the list of improvements for subsequent studies. Happily, we are confident that we are capturing a significant, biologically meaningful correlation between PC 2 of PN calcium (dominated by the responses in DC2 and DM2) and OCT-MCH preference.

3-OCT and MCH activate many glomeruli in addition to the five studied, especially at the concentrations used. There is also limited odor-specificity in their response matrix: notably responses are more correlated in all glomeruli within an individual, compared to responses across individuals (they note this in lines 194-198, though I don't quite understand the specific point they make here). This is a sign of high experimental variability (typically the dynamic range of odor response within an individual is similar to the range across individuals) and makes it even more difficult to resolve underlying individual variation.

We respectfully disagree with the reviewer’s interpretation here. There is substantial odor-specificity in our response matrix. This is evident in both the ORN and PN response matrices (and especially the PN matrix) as variation in the brightness across rows. Columns, which correspond to individuals, are more similar than rows, which correspond to odor-glomerulus pairs. The dynamic range within an individual (within a column, across rows) is indeed greater than the variation among individuals (within a row, across columns).

As an (important) aside, the odor stimuli are very unusual in this study. Odors are delivered at extremely high concentrations (variably 10-25% sv, line 464, not exactly sure what "variably' means- is the stimulus intensity not constant?) as compared to even the highest concentrations used in >95% of other studies (usually <~0.1% sv delivered).

We used these concentrations for a variety of reasons. First, following the protocol of Honegger and Smith (2020), we found that dilutions in this range produce a linear input-output relationship, i.e. doubling or halving one odorant yields proportionate changes in odor-choice behavior metrics. Second, such fold dilutions are standard for tunnel assays of the kind we used. Claridge-Chang et al. (2009) used 14% and 11% for MCH and OCT respectively, for instance. Finally, the specific dilution factor (i.e., within the range of 10-25%) was adjusted on a week-by-week basis to ensure that in an OCT-MCH choice, the mean preference was approximately 50%. This yields the greatest signal of individual odor preference. We have added this last point to the methods section where the range of dilutions is described (lines 442-445).

A parsimonious interpretation of their results is that the strongest correlation they see (ORN PC1 predicts OCT v. air preference) arises because intensity/strength of ORN responses across all odors (e.g. overall excitability of ORNs) partially predicts behavioral avoidance of 3-OCT. However, the degree to which variation in odor-specific glomerular activation patterns can explain behavioral preference (3-OCT v. MCH) seems much less clear, and correspondingly the correlations are weaker and p-values larger for the 3-OCT v. MCH result.

With respect, we disagree with this analysis. The correlation between ORN PC 1 and OCT v. air preference (R2 \= 0.23) is quite similar to that of PN PC 2 and OCT vs MCH preference (R2 \= 0.20). However, the former is dependent on a single outlying point, whereas the latter is not. The latter relationship is also backed up by the BRP imaging and modeling. Therefore in the revision we have de-emphasized the OCT v. air preference model and emphasized the OCT v. MCH preference models.

(2) There is a broader conceptual concern about the degree of logical consistency in the authors' interpretation of how neural variability maps to behavioral variability. For instance, the two odors they focus on, 3-OCT and MCH, barely activate ORNs in 4 of the 5 glomeruli they study. Most of the correlation of ORN PC1 vs. behavioral choice for 3-OCT vs. air, then, must be driven by overall glomerular activation by other odors (but remains predictive since responses across odors appear correlated within an individual). This gives pause to the interpretation that 3-OCT-evoked ORN activity in these five glomeruli is the neural substrate for variability in the behavioral response to 3-OCT.

Our interpretation of the ORN PC1 linear model is not that 3-OCT-evoked ORN activity is the neural substrate for variability – instead, it is the general responsiveness of an individual’s AL across multiple odors (this is our interpretation of the the uniformly positive loadings in ORN PC1). It is true that OCT and MCH do not activate ORNs as strongly as other odorants – our analysis rests on the loadings of the PCs that capture all odor/glomerulus combinations available in our data. All that said, since a single outlier in Figure 1L dominates the relationship, therefore we have de-emphasized these particular results in our revision.

This leads to the most significant concern, which is that the paper does not provide strong evidence that odor-specific patterns of glomerular activation in ORNs and PNs underlie individual behavioral preference between different odors (that each drive significant levels of activity, e.g. 3-OCT v. MCH), or that the ORN-PN synapse is a major driver of individual behavioral variability. Lines 26-31 of the abstract are not well supported, and the language should be softened.

We have modified the abstract to emphasize our confidence in PN calcium correlating with odor-vs-odor preference (removing the ORN & odor-vs-air language).

Their conclusions come primarily from having correlated many parameters reduced from the ORN and PN response matrices against the behavioral data. Several claims are made that a given PC is predictive of an odor preference while others are not, however it does not appear that the statistical tests to support this are shown in the figures or text.

For each linear model of calcium dynamics predicting preference, we restricted our analysis to the first 5 principal components. Thus, we do not feel that we correlated many parameters against the behavioral data. As mentioned below, the correlations identified by this approach comfortably survive a conservative Bonferroni correction. In this revision, a linear model with a single predictor – the projection onto PC 2 of PN calcium – is the result we emphasize in the text, and we report R2 between measured and predicted preference for both a training set of flies and for a test set of flies (Figure 1M and Figure 2 – figure supplement 1).

That is, it appears that the correlation of models based on each component is calculated, then the component with the highest correlation is selected, and a correlation and p-value computed based on that component alone, without a statistical comparison between the predictive values of each component, or to account for effectively performing multiple comparisons. (Figure 1, k l m n o p, Figure 3, d f, and associated analyses).

To reiterate, this was our process: 1) Collect a training data set of paired Ca++ recordings and behavioral preference scores. 2) Compute the first five PCs of the Ca++ data, and measure the correlation of each to behavior. 3) Identify the PC with the best correlation. 4) Collect a test data set with new experimental recordings. 5) Apply the model identified in step 3. For some downstream analyses, we combined test and training data, but only after confirming the separate significance of the training and test correlations.

The p-values associated with the PN PC 2 model predicting OCT-MCH preference are sufficiently low in each of the training and testing sets (0.0063 and 0.0069, respectively) to pass a conservative Bonferroni multiple hypothesis correction (one hypothesis for each of the 5 PCs) at an alpha of 0.05.

Additionally, the statistical model presented in Figure 4 needs significantly more explanation or should be removed- it's unclear how they "infer" the correlation, and the conclusions appears inconsistent with Figure 3 - Figure Supplement 2.

We have removed Figure 4 and have improved upon our approach of inferring the strength of the correlation between latent calcium and behavior in the Methods, incorporating bootstrapping of all sources of data used for the inference (lines 622-628). At the same time, we now emphasize that this analysis is a bonus of sorts, and that the simple correlation between Ca++ and behavior is the main result.

Suggestions:

(1) If the authors want to make the claim that individual variation in ORN or PN odor representations (e.g. glomerular activation patterns) underlie differences in odor preference (MCH v. OCT), they should generalize the weak correlation between ORN/PN activity and behavior to additional glomeruli and pair of odors, where both odors drive significant activity. Otherwise, the claims in the abstract should be tempered.

We have modified the abstract to focus on the effect we have the highest confidence in: contrasting PN calcium activation of DM2 and DC2 predicting OCT-MCH preference.

(2) One of the most valuable contributions a study like this could provide is to carefully quantify the amount of measurement variation (across trials, across hemispheres) in neural responses relative to the amount of individual variation (across individuals). Beyond the degree of variation in the amplitude of odor responses, the rank ordering of odor response strength between repeated measurements (to try to establish conditions that account for adaptation, etc.), between hemispheres, and between individuals is important. Establishing this information is foundational to this entire field of study. The authors take a good first step towards this in Figure 1J and Figure 1, supplement 5C, but the plots do not directly show variance, and the comparison is flawed because more comparisons go into the individual-individual crunch (as evidenced by the consistently smaller range of quartiles). The proper way to do this is by resampling.

We do not know what the reviewer means by “individual-individual crunch,” unfortunately. Thus, it is difficult to determine why they think the analysis is flawed. We are also uncertain about the role of resampling in this analysis. The medians, interquartile ranges and whiskers in the panels referenced by the reviewer are not confidence intervals as might be determined by bootstrap resampling. Rather, these are direct statistics on the coding distances as measured – the raw values associated with these plots are visualized in Figure 1H.

In our revision we updated the heatmaps in Figure 1 – figure supplement 3 to include recordings across the lobes and trials of each individual fly, and we have added a new supplementary figure, Figure 1 – figure supplement 4, to show the correspondence between recordings across lobes or trials, with associated rank-order correlation coefficients. Since the focus of this study was whether measured individual differences predict individual behavioral preference, a full characterization of the statistics of variation in calcium responses was not the focus, though it was the focus of a previous study (Honegger & Smith et al., 2019).

To help the reader understand the data, we would encourage displaying data prior to dimensionality reduction - why not show direct plots of the mean and variance of the neural responses in each glomerulus across repeats, hemispheres, individuals?

We added a new supplementary figure, Figure 1 – figure supplement 4, to show the correspondence between recordings across lobes or trials.

A careful analysis of this point would allow the authors to support their currently unfounded assertion that odor responses become more "idiosyncratic" farther from the periphery (line 135-36); presumably they mean beyond just noise introduced by synaptic transmission, e.g. "idiosyncrasy" is reproducible within an individual. This is a strong statement that is not well-supported at present - it requires showing the degree of similarity in the representation between hemispheres is more similar within a fly than between flies in PNs compared to ORNs (see Hige... Turner, 2015).

Here are the lines in question: “PN responses were more variable within flies, as measured across the left and right hemisphere ALs, compared to ORN responses (Figure 1 – figure supplement 5C), consistent with the hypothesis that odor representations become more idiosyncratic farther from the sensory periphery.”

That responses are more idiosyncratic farther from the periphery is therefore not an “unfounded assertion.” It is clearly laid out as a hypothesis for which we can assess consistency in the data. We stand by our original interpretation: that several observations are consistent with this finding, including greater distance in coding space in PNs compared to ORNs, particularly across lobes and across flies. In addition, higher accuracy in decoding individual identity from PN responses compared to ORN responses (now appearing as Figure 1 – figure supplement 6A) is also consistent with this hypothesis.

Still, to make confusion at this sentence less likely, we have reworded it as “suggesting that odor representations become more divergent farther from the sensory periphery.” (lines 139-140)

(3) Figure 3 is difficult to interpret. Again, the variability of the measurement itself within and across individuals is not established up front. Expression of exogenous tagged brp in ORNs is also not guaranteed to reflect endogenous brp levels, so there is an additional assumption at that level.

Figure 3 – figure supplement 1 Panels A-C display the variability of measurements (Brp volume, total fluorescence and fluorescence density) both within (left/right lobes) and across individuals (the different data points). We agree that exogenous tagged Brp levels will not be identical to endogenous levels. The relationship appears significant despite this caveat.

Again there are statistical concerns with the correlations. For instance, the claim that "Higher Brp in DM2 predicted stronger MCH preference... " on line 389 is not statistically supported with p<0.05 in the ms (see Figure 3 G as the closest test, but even that is a test of the difference of DM2 and DC2, not DM2 alone).

We have changed the language to focus on the pattern of the loadings in PC 2 of Brp-Short density and replaced “predict.” (lines 366-369).

Can the authors also discuss what additional information is gained from the expansion microscopy in the figure supplement, and how it compares to brp density in DC2 using conventional methods?

The expansion microscopy analysis was an attempt to determine what specific aspect of Brp expression was predictive of behavior, on the level of individual Brp puncta, as a finer look compared to the glomerulus-wide fluorescence signal in the conventional microscopy approach. Since this method did not yield a large sample size, at best we can say it provided evidence consistent with the observation from confocal imaging that Brp fluorescent density was the best measure in terms of predicting behavior.

I would prefer to see the calcium and behavioral datasets strengthened to better establish the relationship between ORN/PN responses and behavior, and to set aside the anatomical dataset for a future work that investigates mechanisms.

We are satisfied that our revisions put appropriate emphasis on a robust result relating calcium and behavior measurements: the relationship between OCT-MCH preference and idiosyncratic PN calcium responses. Finding that idiosyncratic Brp density has similar PC 2 loadings that also significantly predict behavior is an important finding that increases confidence in the calcium-behavior finding. We agree with the reviewer that these anatomical findings are secondary to the calcium-behavior analyses, but think they warrant a place in the main findings of the study. As the reviewer suggests, we are conducting follow-on studies that focus on the relationship between neuroanatomical measures and odor preference.

(4) The mean imputation of missing data may have an effect on the conclusions that it is possible to draw from this dataset. In particular, as shown in Figure 1, supplemental figure 3, there is a relatively large amount of missing data, which is unevenly distributed across glomeruli and between the cell types recorded from. Strikingly, DC2 is missing in a large fraction of ORN recordings, while it is present in nearly all the PN recordings. Because DC2 is one of the glomeruli implicated in predicting MCH-OCT preference, this lack of data may be particularly likely to effect the evaluation of whether this preference can be predicted from the ORN data. Overall, mean imputation of glomerulus activity prior to PCA will artificially reduce the amount of variance contributed by the glomerulus. It would be useful to see an evaluation of which results of this paper are robust to different treatments of this missing data.

We confirmed that the linear model of predicted OCT-MCH using PN PC2 calcium was minimally altered when we performed imputation via alternating least squares using the pca function with option ‘als’ to infill missing values on the calcium matrix 1000 times and taking the mean infilled matrix (see MATLAB documentation and Figure 1 – figure supplement 5 of Werkhoven et al., 2021). Fitted slope value for model using mean-infilled data presented in article: -0.0806 (SE = 0.028, model R2 \= 0.15), fitted slope value using ALS-imputed model: -0.0806 (SE 0.026, model R2 \= 0.17).

Additional comments:

(1) On line 255 there is an unnecessary condition: "non-negative positive".

Thank you – non-negative has been removed.

(2) In Figure 4 and the associated analysis, selection of +/- 20% interval around the observed $R^2$ appears arbitrary. This could be based on the actual confidence interval, or established by bootstrapping.

We have replaced the +/- 20% rule by bootstrapping the calculation of behavior-behavior R2, calcium-calcium R2, and calcium-behavior R2 and propagating the uncertainties forward (Inference of correlation between latent calcium and behavior states section in Materials and Methods).

(3) On line 409 the claim is made "These sources of variation specifically implicate the ORN-PN synapse..." While the model recapitulates the glomerulus specific variation of activity under PN synapse density variation, it also occurs under ORN identity variation, which calls into question whether the synapse distribution itself is specifically implicated, or if any variation that is expected to be glomerulus specific would be equally implicated.

We agree with this observation. We found that varying either the ORNs or the PNs that project to each glomeruli can produce patterns of PN response variation similar to what is measured experimentally. This is consistent with the idea that the ORN-PN synapse is a key site of behaviorally-relevant variation.

(4) Line 214 "... we conclude that the relative responses of DM2 vs DC2 in PNs largely explains an individual's preference." is too strong of a claim, based on the fact that using the PC2 explains much more of the variance, while using the stated hypothesis noticeable decreases the predictive power ($R^2$ = 0.2 vs $R^2$ = 0.12 )

We have changed the wording here to “we conclude that the relative responses of DM2 vs DC2 in PNs compactly predict an individual’s preference.” (lines 192-193)

Author response:

The following is the authors’ response to the original reviews.

eLife Assessment

This study attempts to resolve an apparent paradox of rapid evolutionary rates of multi-copy gene systems by using a theoretical model that integrates two classic population models. While the conceptual framework is intuitive and thus useful, the specific model is perplexing and difficult to penetrate for non-specialists. The data analysis of rRNA genes provides inadequate support for the conclusions due to a lack of consideration of technical challenges, mutation rate variation, and the relationship between molecular processes and model parameters.

Overall Responses:

Since the eLife assessment succinctly captures the key points of the reviews, the reply here can be seen as the overall responses to the summed criticisms. We believe that the overview should be sufficient to address the main concerns, but further details can be found in the point-by-point responses below. The overview covers the same grounds as the provisional responses (see the end of this rebuttal) but is organized more systematically in response to the reviews. The criticisms together fall into four broad areas. 

First, the lack of engagement with the literature, particularly concerning Cannings models and non-diffusive limits. This is the main rebuttal of the companion paper (eLife-RP-RA-2024-99990). The literature in question is all in the WF framework and with modifications, in particular, with the introduction of V(K). Nevertheless, all WF models are based on population sampling. The Haldane model is an entirely different model of genetic drift, based on gene transmission. Most importantly, the WF models and the Haldane model differ in the ability to handle the four paradoxes presented in the two papers. These paradoxes are all incompatible with the WF models.

Second, the poor presentation of the model that makes the analyses and results difficult to interpret. In retrospect, we fully agree and thank all the reviewers for pointing them out. Indeed, we have unnecessarily complicated the model. Even the key concept that defines the paradox, which is the effective copy number of rRNA genes, is difficult to comprehend. We have streamlined the presentation now. Briefly, the complexity arose from the general formulation permitting V(K) ≠ E(K) even for single copy genes. (It would serve the same purpose if we simply let V(K) = E(K) for single copy genes.) The sentences below, copied from the new abstract, should clarify the issue. The full text in the Results section has all the details.

“On average, rDNAs have C ~ 150 - 300 copies per haploid in humans. While a neutral mutation of a single-copy gene would take 4N generations (N being the population size of an ideal population) to become fixed, the time should be 4NC* generations for rRNA genes (C* being the effective copy number). Note that C* >> 1, but C* < (or >) C would depend on the drift strength. Surprisingly, the observed fixation time in mouse and human is < 4N, implying the paradox of C* < 1.”

Third, the confusion about which rRNA gene is being compared with which homology, as there are hundreds of them. We should note that the effective copy number C* indicates that the rRNA gene arrays do not correspond with the “gene locus” concept. This is at the heart of the confusion we failed to remove clearly. We now use the term “pseudo-population” to clarify the nature of rDNA variation and evolution. The relevant passage is reproduced from the main text shown below.

“The pseudo-population of ribosomal DNA copies within each individual

While a human haploid with 200 rRNA genes may appear to have 200 loci, the concept of "gene loci" cannot be applied to the rRNA gene clusters. This is because DNA sequences can spread from one copy to others on the same chromosome via replication slippage. They can also spread among copies on different chromosomes via gene conversion and unequal crossovers (Nagylaki 1983; Ohta and Dover 1983; Stults, et al. 2008; Smirnov, et al. 2021). Replication slippage and unequal crossovers would also alter the copy number of rRNA genes. These mechanisms will be referred to collectively as the homogenization process. Copies of the cluster on the same chromosome are known to be nearly identical in sequences (Hori, et al. 2021; Nurk, et al. 2022). Previous research has also provided extensive evidence for genetic exchanges between chromosomes (Krystal, et al. 1981; Arnheim, et al. 1982; van Sluis, et al. 2019).

In short, rRNA gene copies in an individual can be treated as a pseudo-population of gene copies. Such a pseudo-population is not Mendelian but its genetic drift can be analyzed using the branching process (see below). The pseudo-population corresponds to the "chromosome community" proposed recently (Guarracino, et al. 2023). As seen in Fig. 1C, the five short arms harbor a shared pool of rRNA genes that can be exchanged among them. Fig. 1D presents the possible molecular mechanisms of genetic drift within individuals whereby mutations may spread, segregate or disappear among copies. Hence, rRNA gene diversity or polymorphism refers to the variation across all rRNA copies, as these genes exist as paralogs rather than orthologs. This diversity can be assessed at both individual and population levels according to the multi-copy nature of rRNA genes.”

Fourth, the lack of consideration of many technical challenges. We have responded to the criticisms point-by-point below. One of the main criticisms is about mutation rate differences between single-copy and rRNA genes. We did in fact alluded to the parity in mutation rate between them in the original text but should have presented this property more prominently as is done now. Below is copied from the revised text:

“We now consider the evolution of rRNA genes between species by analyzing the rate of fixation (or near fixation) of mutations. Polymorphic variants are filtered out in the calculation. Note that Eq. (3) shows that the mutation rate, m, determines the long-term evolutionary rate, l. Since we will compare the l values between rRNA and single-copy genes, we have to compare their mutation rates first by analyzing their long-term evolution. As shown in Table S1, l falls in the range of 50-60 (differences per Kb) for single copy genes and 40 – 70 for the non-functional parts of rRNA genes. The data thus suggest that rRNA and single-copy genes are comparable in mutation rate. Differences between their l values will have to be explained by other means.”

While the overview should address the key issues, we now present the point-by-point response below. 

Public Reviews:

Reviewer #1 (Public Review):

The manuscript by Wang et al is, like its companion paper, very unusual in the opinion of this reviewer. It builds off of the companion theory paper's exploration of the "Wright-Fisher Haldane" model but applies it to the specific problem of diversity in ribosomal RNA arrays.

The authors argue that polymorphism and divergence among rRNA arrays are inconsistent with neutral evolution, primarily stating that the amount of polymorphism suggests a high effective size and thus a slow fixation rate, while we, in fact, observe relatively fast fixation between species, even in putatively non-functional regions.

They frame this as a paradox in need of solving, and invoke the WFH model.

The same critiques apply to this paper as to the presentation of the WFH model and the lack of engagement with the literature, particularly concerning Cannings models and non-diffusive limits. However, I have additional concerns about this manuscript, which I found particularly difficult to follow.

Response 1: We would like to emphasize that, despite the many modified WF models, there has not been a model for quantifying genetic drift in multi-copy gene systems, due to the complexity of two levels of genetic drift – within individuals as well as between individuals of the population. We will address this question in the revised manuscript (Ruan, et al. 2024) and have included a mention of it in the text as follows:

“In the WF model, gene frequency is governed by 1/N (or 1/2_N_ in diploids) because K would follow the Poisson distribution whereby V(K) = E(K). As E(K) is generally ~1, V(K) would also be ~ 1. In this backdrop, many "modified WF" models have been developed(Der, et al. 2011), most of them permitting V(K) ≠ E(K) (Karlin and McGregor 1964; Chia and Watterson 1969; Cannings 1974). Nevertheless, paradoxes encountered by the standard WF model apply to these modified WF models as well because all WF models share the key feature of gene sampling (see below and (Ruan, et al. 2024)). ”

My first, and most major, concern is that I can never tell when the authors are referring to diversity in a single copy of an rRNA gene compared to when they are discussing diversity across the entire array of rRNA genes. I admit that I am not at all an expert in studies of rRNA diversity, so perhaps this is a standard understanding in the field, but in order for this manuscript to be read and understood by a larger number of people, these issues must be clarified.

Response 2: We appreciate the reviewer’s feedback and acknowledge that the distinction between the diversity of individual rRNA gene copies and the diversity across the entire array of rRNA genes may not have been clearly defined in the original manuscript. The diversity in our manuscript is referring to the genetic diversity of the population of rRNA genes in the cell. To address this concern, we have revised the relevant paragraph in the text:

“Hence, rRNA gene diversity or polymorphism refer to the variation across all rRNA copies, as these genes exist as paralogs rather than orthologs. This diversity can be assessed at both individual and population levels according to the multi-copy nature of rRNA genes.”

Additionally, we have updated the Methods section to include a detailed description of how diversity is measured as follows:

“All mapping and analysis are performed among individual copies of rRNA genes.

Each individual was considered as a psedo-population of rRNA genes and the diversity of rRNA genes was calculated using this psedo-population of rRNA genes.”

The authors frame the number of rRNA genes as roughly equivalent to expanding the population size, but this seems to be wrong: the way that a mutation can spread among rRNA gene copies is fundamentally different than how mutations spread within a single copy gene. In particular, a mutation in a single copy gene can spread through vertical transmission, but a mutation spreading from one copy to another is fundamentally horizontal: it has to occur because some molecular mechanism, such as slippage, gene conversion, or recombination resulted in its spread to another copy. Moreover, by collapsing diversity across genes in an rRNA array, the authors are massively increasing the mutational target size.   

For example, it's difficult for me to tell if the discussion of heterozygosity at rRNA genes in mice starting on line 277 is collapsed or not. The authors point out that Hs per kb is ~5x larger in rRNA than the rest of the genome, but I can't tell based on the authors' description if this is diversity per single copy locus or after collapsing loci together. If it's the first one, I have concerns about diversity estimation in highly repetitive regions that would need to be addressed, and if it's the second one, an elevated rate of polymorphism is not surprising, because the mutational target size is in fact significantly larger.

Response 3: As addressed in previous Response2, the measurement of diversity or heterozygosity of rRNA genes is consistently done by combining copies, as there is no concept of single gene locus for rDNAs. We agree that by combining the diversity across multiple rRNA gene copies into one measurement, the mutational target size is effectively increased, leading to higher observed levels of diversity than one gene. This is in line with our text:

“If we use the polymorphism data, it is as if rDNA array has a population size 5.2 times larger than single-copy genes. Although the actual copy number on each haploid is ~ 110, these copies do not segregate like single-copy genes and we should not expect N* to be 100 times larger than N. The HS results confirm the prediction that rRNA genes should be more polymorphic than single-copy genes.”

Under this consensus, the reviewer points out that the having a large number of rRNA genes is not equivalent to having a larger population size, because the spreading of mutations among rDNA copies within a species involves two stages: within individual (horizontal transmission) and between individuals (vertical transmission). Let’s examine how the mutation spreading mechanisms influence the population size of rRNA genes.

First, an increase in the copy number of rRNA genes dose increase the actual population size (CN) of rRNA genes. If reviewer is referring to the effective population size of rRNA genes in the context of diversity (N* = CN/V*(K)), then an increase in C would also increase N*. In addition, the linkage among copies would reduce the drift effect, leading to increase diversity. Conversely, homogenization mechanism, like gene conversion and unequal crossing-over would reduce genetic variations between copies and increase V*(K), leading to lower diversity. Therefore, the C* =C/V*(K) in mice is about 5 times larger for rRNA genes than the rest of the genome (which mainly single-copy genes), even though the actual copy number is about 110, indicating a high homogenization rate.

Even if these issues were sorted out, I'm not sure that the authors framing, in terms of variance in reproductive success is a useful way to understand what is going on in rRNA arrays. The authors explicitly highlight homogenizing forces such as gene conversion and replication slippage but then seem to just want to incorporate those as accounting for variance in reproductive success. However, don't we usually want to dissect these things in terms of their underlying mechanism? Why build a model based on variance in reproductive success when you could instead explicitly model these homogenizing processes? That seems more informative about the mechanism, and it would also serve significantly better as a null model, since the parameters would be able to be related to in vitro or in vivo measurements of the rates of slippage, gene conversion, etc.

In the end, I find the paper in its current state somewhat difficult to review in more detail, because I have a hard time understanding some of the more technical aspects of the manuscript while so confused about high-level features of the manuscript. I think that a revision would need to be substantially clarified in the ways I highlighted above.

Response 4: We appreciate your perspective on modeling the homogenizing processes of rRNA gene arrays.

We employ the WFH model to track the drift effect of the multi-copy gene system. In the context of the Haldane model, the term K is often referred to as reproductive success, but it might be more accurate to interpret it as “transmission rate” in this study. As stated in the caption of Figure 1D, two new mutations can have very large differences in individual output (K) when transmitted to the next generation through homogenization process.

Regarding why we did not explicitly model different mechanisms of homogenization, previous elegant models of multigene families have involved mechanisms like unequal crossing over(Smith 1974a; Ohta 1976; Smith 1976) or gene conversion (Nagylaki 1983; Ohta 1985) for concerted evolution, or using conversion to approximate the joint effect of conversion and crossing over (Ohta and Dover 1984). However, even when simplifying the gene conversion mechanism, modeling remains challenging due to controversial assumptions, such as uniform homogenization rate across all gene members (Dover 1982; Ohta and Dover 1984). No models can fully capture the extreme complexity of factors, while these unbiased mechanisms are all genetic drift forces that contribute to changes in mutant transmission. Therefore, we opted for a more simplified and collective approach using V*(K) to see the overall strength of genetic drift.

We have discussed the reason for using V*(K) to collectively represent the homogenization effect in Discussion. As stated in our manuscript:

“There have been many rigorous analyses that confront the homogenizing mechanisms directly. These studies (Smith 1974b; Ohta 1976; Dover 1982; Nagylaki 1983; Ohta and Dover 1983) modeled gene conversion and unequal cross-over head on. Unfortunately, on top of the complexities of such models, the key parameter values are rarely obtainable. In the branching process, all these complexities are wrapped into V*(K) for formulating the evolutionary rate. In such a formulation, the collective strength of these various forces may indeed be measurable, as shown in this study.”

Reviewer #2 (Public Review):

Summary:

Multi-copy gene systems are expected to evolve slower than single-copy gene systems because it takes longer for genetic variants to fix in the large number of gene copies in the entire population. Paradoxically, their evolution is often observed to be surprisingly fast. To explain this paradox, the authors hypothesize that the rapid evolution of multi-copy gene systems arises from stronger genetic drift driven by homogenizing forces within individuals, such as gene conversion, unequal crossover, and replication slippage. They formulate this idea by combining the advantages of two classic population genetic models -- adding the V(k) term (which is the variance in reproductive success) in the Haldane model to the Wright-Fisher model. Using this model, the authors derived the strength of genetic drift (i.e., reciprocal of the effective population size, Ne) for the multi-copy gene system and compared it to that of the single-copy system. The theory was then applied to empirical genetic polymorphism and divergence data in rodents and great apes, relying on comparison between rRNA genes and genome-wide patterns (which mostly are single-copy genes). Based on this analysis, the authors concluded that neutral genetic drift could explain the rRNA diversity and evolution patterns in mice but not in humans and chimpanzees, pointing to a positive selection of rRNA variants in great apes.

Strengths:

Overall, the new WFH model is an interesting idea. It is intuitive, efficient, and versatile in various scenarios, including the multi-copy gene system and other cases discussed in the companion paper by Ruan et al.

Weaknesses:

Despite being intuitive at a high level, the model is a little unclear, as several terms in the main text were not clearly defined and connections between model parameters and biological mechanisms are missing. Most importantly, the data analysis of rRNA genes is extremely over-simplified and does not adequately consider biological and technical factors that are not discussed in the model. Even if these factors are ignored, the authors' interpretation of several observations is unconvincing, as alternative scenarios can lead to similar patterns. Consequently, the conclusions regarding rRNA genes are poorly supported. Overall, I think this paper shines more in the model than the data analysis, and the modeling part would be better presented as a section of the companion theory paper rather than a stand-alone paper. My specific concerns are outlined below.

Response 5: We appreciate the reviewer’s feedback and recognize the need for clearer definitions of key terms. We have made revisions to ensure that each term is properly defined upon its first use.

Regarding the model’s simplicity, as in the Response4, our intention was to create a framework that captures the essence of how mutant copies spread by chance within a population, relying on the variance in transmission rates for each copy (V(K)). By doing so, we aimed to incorporate the various homogenization mechanisms that do not affect single-copy genes, highlighting the substantially stronger genetic drift observed in multi-copy systems compared to single-copy genes. We believe that simplifying the model was necessary to make it more accessible and practical for real-world data analysis and provides a useful approximation that can be applied broadly. It is clearly an underestimate the actual rate as some forces with canceling effects might not have been accounted for.

(1) Unclear definition of terms

Many of the terms in the model or the main text were not clearly defined the first time they occurred, which hindered understanding of the model and observations reported. To name a few:

(i) In Eq(1), although C* is defined as the "effective copy number", it is unclear what it means in an empirical sense. For example, Ne could be interpreted as "an ideal WF population with this size would have the same level of genetic diversity as the population of interest" or "the reciprocal of strength of allele frequency change in a unit of time". A few factors were provided that could affect C*, but specifically, how do these factors impact C*? For example, does increased replication slippage increase or decrease C*? How about gene conversion or unequal cross-over? If we don't even have a qualitative understanding of how these processes influence C*, it is very hard to make interpretations based on inferred C*. How to interpret the claim on lines 240-241 (If the homogenization is powerful enough, rRNA genes would have C*<1)? Please also clarify what C* would be, in a single-copy gene system in diploid species.

Response 6: We apology for the confusion caused by the lack of clear definitions in the initial manuscript. We recognize that this has led to misunderstandings regarding the concept we presented. Our aim was to demonstrate the concerted evolution in multi-copy gene systems, involving two levels of “effective copy number” relative to single-copy genes: first, homogenization within populations then divergence between species. We used C* and Ne* to try to designated the two levels driven by the same homogenization force, which complicated the evolutionary pattern.

To address these issues, we have simplified the model and revised the abstract to prevent any misunderstandings:

“On average, rDNAs have C ~ 150 - 300 copies per haploid in humans. While a neutral mutation of a single-copy gene would take 4_N_ (N being the population size) generations to become fixed, the time should be 4_NC* generations for rRNA genes where 1<< C* (C* being the effective copy number; C* < C or C* > C would depend on the drift strength). However, the observed fixation time in mouse and human is < 4_N, implying the paradox of C* < 1. Genetic drift that encompasses all random neutral evolutionary forces appears as much as 100 times stronger for rRNA genes as for single-copy genes, thus reducing C* to < 1.”

Thus, it should be clear that the fixation time as well as the level of polymorphism represent the empirical measures of C*.We have also revised the relevant paragraph in the text to define C* and V*(K) and removed Eq. 2 for clarity:

“Below, we compare the strength of genetic drift in rRNA genes vs. that of single-copy genes using the Haldane model (Ruan, et al. 2024). We shall use * to designate the equivalent symbols for rRNA genes; for example, E(K) vs. E*(K). Both are set to 1, such that the total number of copies in the long run remains constant.

For simplicity, we let V(K) = 1 for single-copy genes. (If we permit V(K) ≠ 1, the analyses will involve the ratio of V*(K) and V(K) to reach the same conclusion but with unnecessary complexities.) For rRNA genes,  V*(K) ≥ 1 may generally be true because K for rDNA mutations are affected by a host of homogenization factors including replication slippage, unequal cross-over, gene conversion and other related mechanisms not operating on single copy genes. Hence,

where C is the average number of rRNA genes in an individual and V*(K) reflects the homogenization process on rRNA genes (Fig. 1D). Thus,

C* = C/V*(K)

represents the effective copy number of rRNA genes in the population, determining the level of genetic diversity relative to single-copy genes. Since C is in the hundreds and V*(K) is expected to be > 1, the relationship of 1 << C* ≤ C is hypothesized. Fig. 1D is a simple illustration that the homogenizing process may enhance V*(K) substantially over the WF model.

In short, genetic drift of rRNA genes would be equivalent to single copy genes in a population of size NC* (or N*). Since C* >> 1 is hypothesized, genetic drift for rRNA genes is expected to be slower than for single copy genes.”

(ii) In Eq(1), what exactly is V*(K)? Variance in reproductive success across all gene copies in the population? What factors affect V*(K)? For the same population, what is the possible range of V*(K)/V(K)? Is it somewhat bounded because of biological constraints? Are V*(K) and C*(K) independent parameters, or does one affect the other, or are both affected by an overlapping set of factors?

Response 7: - In Eq(1), what exactly is V*(K)?  In Eq(1), V*(K) refers to the variance in the number of progeny to whom the gene copy of interest is transmitted (K) over a specific time interval. When considering evolutionary divergence between species, V*(K) may correspond to the divergence time.

- What factors affect V*(K)? For the same population, what is the possible range of V*(K)/V(K)? Is it somewhat bounded because of biological constraints?  “V*(K) for rRNA genes is likely to be much larger than V(K) for single-copy genes, because K for rRNA mutations may be affected by a host of homogenization factors including replication slippage, unequal cross-over, gene conversion and other related mechanisms not operating on single-copy genes. For simplicity, we let V(K) = 1 (as in a WF population) and V*(K) ≥ 1.” Thus, the V*(K)/V(K) = V*(K) can potentially reach values in the hundreds, and may even exceed C, resulting in C*(= C/V*(K)) values less than 1. Biological constraints that could limit this variance include the minimum copy number within individuals, sequence constraints in functional regions, and the susceptibility of chromosomes with large arrays to intrachromosomal crossover (which may lead to a reduction in copy number)(Eickbush and Eickbush 2007), potentially reducing the variability of K.

- Are V*(K) and C*(K) independent parameters, or does one affect the other, or are both affected by an overlapping set of factors?  There is no C*(K), the C* is defined as follows in the text:

“C* = C/V*(K) represents the effective copy number of rRNA genes, reflecting the level of genetic diversity relative to single-copy genes. Since C is in the hundreds and V*(K) is expected to be > 1, the relationship of 1 << C* ≤ C is hypothesized.” The factors influencing V*(K) directly affect C* due to this relationship.

(iii) In the multi-copy gene system, how is fixation defined? A variant found at the same position in all copies of the rRNA genes in the entire population?

Response 8: We appreciate the reviewer's suggestion and have now provided a clear definition of fixation in the context of multi-copy genes within the manuscript.

“For rDNA mutations, fixation must occur in two stages – fixation within individuals and among individuals in the population. (Note that a new mutation can be fixed via homogenization, thus making rRNA gene copies in an individual a pseudo-population.)”

The evolutionary dynamics of multi-copy genes differ from those of single-copy (Mendelian) genes, which mutate, segregate and evolve independently in the population. Fixation in multi-copy genes, such as rRNA genes, is influenced by their ability to transfer genetic information among their copies through nonreciprocal exchange mechanisms, like gene conversion and unequal crossover (Ohta and Dover 1984). These processes can cause fluctuations in the number of mutant copies within an individual's lifetime and facilitate the spread of a mutant allele across all copies even in non-homologous chromosomes. Over time, this can result in the mutant allele replacing all preexisting alleles throughout the population, leading to fixation (Ohta 1976) meaning that the same variant will eventually be present at the corresponding position in all copies of the rRNA genes across the entire population. Without such homogenization processes, fixation would be unlikely to be obtained in multi-copy genes.

(iv) Lines 199-201, HI, Hs, and HT are not defined in the context of a multi-copy gene system. What are the empirical estimators?

Response 9: We appreciate the reviewer's comment and would like to clarify the definitions and empirical estimators for within the context of a multi-copy gene system in the text:

“A standard measure of genetic drift is the level of heterozygosity (H). At the mutation-selection equilibrium

where μ is the mutation rate of the entire gene and Ne is the effective population size. In this study, Ne = N for single-copy gene and Ne = C*N for rRNA genes. The empirical measure of nucleotide diversity H is given by

where L is the gene length (for each copy of rRNA gene, L ~ 43kb) and pi is the variant frequency at the i-th site.

We calculate H of rRNA genes at three levels – within-individual, within-species and then, within total samples (HI, HS and HT, respectively). HS and HT are standard population genetic measures (Hartl, et al. 1997; Crow and Kimura 2009). In calculating HS, all sequences in the species are used, regardless of the source individuals. A similar procedure is applied to HT. The HI statistic is adopted for multi-copy gene systems for measuring within-individual polymorphism. Note that copies within each individual are treated as a pseudo-population (see Fig. 1 and text above). With multiple individuals, HI is averaged over them.”

(v) Line 392-393, f and g are not clearly defined. What does "the proportion of AT-to-GC conversion" mean? What are the numerator and denominator of the fraction, respectively?

Response 10: We appreciate the reviewer's comment and have revised the relevant text for clarity as well as improved the specific calculation methods for f and g in the Methods section.

“We first designate the proportion of AT-to-GC conversion as f and the reciprocal, GC-to-AT, as g. Specifically, f represents the proportion of fixed mutations where an A or T nucleotide has been converted to a G or C nucleotide (see Methods). Given f ≠ g, this bias is true at the site level.”

Methods:

“Specifically, f represents the proportion of fixed mutations where an A or T nucleotide has been converted to a G or C nucleotide. The numerator for f is the number of fixed mutations from A-to-G, T-to-C, T-to-G, or A-to-C. The denominator is the total number of A or T sites in the rDNA sequence of the specie lineage.

Similarly, g is defined as the proportion of fixed mutations where a G or C nucleotide has been converted to an A or T nucleotide. The numerator for g is the number of fixed mutations from G-to-A, C-to-T, C-to-A, or G-to-T. The denominator is the total number of G or C sites in the rDNA sequence of the specie lineage.

The consensus rDNA sequences for the species lineage were generated by Samtools consensus (Danecek, et al. 2021) from the bam file after alignment. The following command was used:

‘samtools consensus -@ 20 -a -d 10 --show-ins no --show-del yes input_sorted.bam output.fa’.”

(2) Technical concerns with rRNA gene data quality

Given the highly repetitive nature and rapid evolution of rRNA genes, myriads of things could go wrong with read alignment and variant calling, raising great concerns regarding the data quality. The data source and methods used for calling variants were insufficiently described at places, further exacerbating the concern.

(i) What are the accession numbers or sample IDs of the high-coverage WGS data of humans, chimpanzees, and gorillas from NCBI? How many individuals are in each species? These details are necessary to ensure reproducibility and correct interpretation of the results.

Response 11: We apologize for not including the specific details of the sample information in the main text. All accession numbers and sample IDs for the WGS data used in this study, including mice, humans, chimpanzee, and gorilla, are already listed in Supplementary Tables S4-S5. We have revised the table captions and referenced them at the appropriate points in the Methods to ensure clarity.

“The genome sequences of human (n = 8), chimpanzee (n = 1) and gorilla (n = 1) were sourced from National Center for Biotechnology Information (NCBI) (Supplementary Table 4). … Genomic sequences of mice (n = 13) were sourced from the Wellcome Sanger Institute’s Mouse Genome Project (MGP) (Keane, et al. 2011).

The concern regarding the number of individuals needed to support the results will be addressed in Response 13.

(ii) Sequencing reads from great apes and mice were mapped against the human and mouse rDNA reference sequences, respectively (lines 485-486). Given the rapid evolution of rRNA genes, even individuals within the same species differ in copy number and sequences of these genes. Alignment to a single reference genome would likely lead to incorrect and even failed alignment for some reads, resulting in genotyping errors. Differences in rDNA sequence, copy number, and structure are even greater between species, potentially leading to higher error rates in the called variants. Yet the authors provided no justification for the practice of aligning reads from multiple species to a single reference genome nor evidence that misalignment and incorrect variant calling are not major concerns for the downstream analysis.

Response 12: While the copy number of rDNA varies in each individuals, the sequence identity among copies is typically very high (median identity of 98.7% (Nurk, et al. 2022)). Therefore, all rRNA genes were aligned against to the species-specific reference sequences, where the consensus nucleotide nearly accounts for >90% of the gene copies in the population. In minimize genotyping errors, our analysis focused exclusively on single nucleotide variants (SNVs) with only two alleles, discarding other mutation types.

Regarding sequence divergence between species, which may have greater sequence variations, we excluded unmapped regions with high-quality reads coverage below 10. In calculation of substitution rate, we accounted for the mapping length (L), as shown in the column 3 in Table 3-5.

We appreciate the reviewer’s comments and have provide details in the Methods.

(vi) It is unclear how variant frequency within an individual was defined conceptually or computed from data (lines 499-501). The population-level variant frequency was calculated by averaging across individuals, but why was the averaging not weighted by the copy number of rRNA genes each individual carries? How many individuals are sampled for each species? Are the sample sizes sufficient to provide an accurate estimate of population frequencies?

Response 13: Each individual was considered as a psedo-population of rRNA genes, varaint frequency within an individual was the proportions of mutant allele in this psedo-population. The calculation of varaint frequency is based on the number of supported reads of each individual.

The reason for calculating population-level variant frequency by averaging across individuals is relevant in the calculation of FIS and FST. In calculating FST, the standard practice is to weigh each population equally. So, when we show FST in humans, we do not consider whether there are more Africans, Caucasians or Asians. There is a reason for not weighing them even though the population sizes could be orders of magnitude different, say, in the comparison between an ethnic minority and the main population. In the case of FIS, the issue is moot. Although copy number may range from 150 to 400 per haploid, most people have 300 – 500 copies with two haploids.

As for the concern regarding the number the individuals needed to support of the results:

Considering the nature of multi-copy genes, where gene members undergo continuous exchanges at a much slower rate compared to the rapid rate of random distribution of chromosomes at each generation of sexual reproduction, even a few variant copies that arise during an individual's lifetime would disperse into the gene pool in the next generation (Ohta and Dover 1984). Thus, there is minimal difference between individuals. Our analysis is also aligns with this theory, particularly in human population (FIS = 0.059), where each individual carries the majority of the population's genetic diversity. Therefore, even a single chimpanzee or gorilla individual caries sufficient diversity with its hundreds of gene copies to calculate divergence with humans.

(vii) Fixed variants are operationally defined as those with a frequency>0.8 in one species. What is the justification for this choice of threshold? Without knowing the exact sample size of the various species, it's difficult to assess whether this threshold is appropriate.

Response 14: First, the mutation frequency distribution is strongly bimodal (see Figure below) with a peak at zero and the other at 1. This high frequency peak starts to rise slowly at 0.8, similar to FST distribution in Figure 4C. That is why we use it as the cutoff although we would get similar results at the cutoff of 0.90 (see Table below). Second, the sample size for the calculation of mutant frequency is based on the number of reads which is usually in the tens of thousands. Third, it does not matter if the mutation frequency calculation is based on one individuals or multiple individuals because 95% of the genetic diversity of the population is captured by the gene pool within each individual.

Author response image 1.

Author response table 1.

The A/T to G/C and G/C to A/T changes in apes and mouse.

New mutants with a frequency >0.9 within an individual are considered as (nearly) fixed, except for humans, where the frequency was averaged over 8 individuals in the Table 2.

The X-squared values for each species are as follows: 58.303 for human, 7.9292 for chimpanzee, and 0.85385 for M. m. domesticus.

(viii) It is not explained exactly how FIS, FST, and divergence levels of rRNA genes were calculated from variant frequency at individual and species levels. Formulae need to be provided to explain the computation.

Response 15: After we clearly defined the HI, HS, and HT in Response9, understanding FIS and F_ST_ becomes straightforward.

“Given the three levels of heterozygosity, there are two levels of differentiation. First, FIS is the differentiation among individuals within the species, defined by

FIS = [HS - HI]/HS  

FIS is hence the proportion of genetic diversity in the species that is found only between individuals. We will later show FIS ~ 0.05 in human rDNA (Table 2), meaning 95% of rDNA diversity is found within individuals.

Second, FST is the differentiation between species within the total species complex, defined as

FST = [HT – HS]/HT 

FST is the proportion of genetic diversity in the total data that is found only between species.”

(3) Complete ignorance of the difference in mutation rate difference between rRNA genes and genome-wide average

Nearly all data analysis in this paper relied on comparison between rRNA genes with the rest (presumably single-copy part) of the genome. However, mutation rate, a key parameter determining the diversity and divergence levels, was completely ignored in the comparison. It is well known that mutation rate differs tremendously along the genome, with both fine and large-scale variation. If the mutation rate of rRNA genes differs substantially from the genome average, it would invalidate almost all of the analysis results. Yet no discussion or justification was provided.

Response 16: We appreciate the reviewer's observation regarding the potential impact of varying mutation rates across the genome. To address this concern, we compared the long-term substitution rates on rDNA and single-copy genes between human and rhesus macaque, which diverged approximately 25 million years ago. Our analysis (see Table S1 below) indicates that the substitution rate in rDNA is actually slower than the genome-wide average. This finding suggests that rRNA genes do not experience a higher mutation rate compared to single-copy genes, as stated in the text:

“Note that Eq. (3) shows that the mutation rate, m, determines the long-term evolutionary rate, l. Since we will compare the l values between rRNA and single-copy genes, we have to compare their mutation rates first by analyzing their long-term evolution. As shown in Table S1, l falls in the range of 50-60 (differences per Kb) for single copy genes and 40 – 70 for the non-functional parts of rRNA genes. The data thus suggest that rRNA and single-copy genes are comparable in mutation rate. Differences between their l values will have to be explained by other means.”

However, given the divergence time (Td) being equal to or smaller than Tf, even if the mutation rate per nucleotide is substantially higher in rRNA genes, these variants would not become fixed after the divergence of humans and chimpanzees without the help of strong homogenization forces. Thus, the presence of divergence sites (Table 5) still supports the conclusion that rRNA genes undergo much stronger genetic drift compared to single-copy genes.

Related to mutation rate: given the hypermutability of CpG sites, it is surprising that the evolution/fixation rate of rRNA estimated with or without CpG sites is so close (2.24% vs 2.27%). Given the 10 - 20-fold higher mutation rate at CpG sites in the human genome, and 2% CpG density (which is probably an under-estimate for rDNA), we expect the former to be at least 20% higher than the latter.

Response 17: While it is true that CpG sites exhibit a 10-20-fold higher mutation rate, the close evolution/fixation rates of rDNA with and without CpG sites (2.24% vs 2.27%) may be attributed to the fact that fixation rates during short-term evolutionary processes are less influenced by mutation rates alone. As observed in the Human-Macaque comparison in the table above, the substitution rate of rDNA in non-functional regions with CpG sites is 4.18%, while it is 3.35% without CpG sites, aligning with your expectation of 25% higher rates where CpG sites are involved.

This discrepancy between the expected and observed fixation rates may be due to strong homogenization forces, which can rapidly fix or eliminate variants, thereby reducing the overall impact of higher mutation rates at CpG sites on the observed fixation rate. This suggests that the homogenization mechanisms play a more dominant role in the fixation process over short evolutionary timescales, mitigating the expected increase in fixation rates due to CpG hypermutability.

Among the weaknesses above, concern (1) can be addressed with clarification, but concerns (2) and (3) invalidate almost all findings from the data analysis and cannot be easily alleviated with a complete revamp work.

Recommendations for the authors:

Reviewing Editor Comments:

Both reviewers found the manuscript confusing and raised serious concerns. They pointed out a lack of engagement with previous literature on modeling and the presence of ill-defined terms within the model, which obscure understanding. They also noted a significant disconnection between the modeling approach and the biological processes involved. Additionally, the data analysis was deemed problematic due to the failure to consider essential biological and technical factors. One reviewer suggested that the modeling component would be more suitable as a section of the companion theory paper rather than a standalone paper. Please see their individual reviews for their overall assessment.

Reviewer #2 (Recommendations For The Authors):

Beyond my major concerns, I have numerous questions about the interpretation of various findings:

Lines 62-63: Please explain under what circumstance Ne=N/V(K) is biologically nonsensical and why.

Response 18: “Biologically non-sensical” is the term used in (Chen, et al. 2017). We now used the term “biologically untenable” but the message is the same. How does one get V(K) ≠ E(K) in the WF sampling? It is untenable under the WF structure. Kimura may be the first one to introduce V(K) ≠ E(K) into the WF model and subsequent papers use the same sort of modifications that are mathematically valid but biologically dubious. As explained extensively in the companion paper, the modifications add complexities but do not give the WF models powers to explain the paradoxes.

Lines 231-234: The claim about a lower molecular evolution rate (lambda) is inaccurate - under neutrality, the molecular evolution rate is always the same as the mutation rate. It is true that when the species divergence Td is not much greater than fixation time Tf, the observed number of fixed differences would be substantially smaller than 2*mu*Td, but the lower divergence level does not mean that the molecular evolution is slower. In other words, in calculating the divergence level, it is the time term that needs to be adjusted rather than the molecular evolution rate.

Response 19: Thanks, we agree that the original wording was not accurate. It is indeed the substitution rate rather than the molecular evolution rate that is affected when species divergence time Td is not much greater than the fixation time Tf. We have revised the relevant text in the manuscript to correct this and ensure clarity.

Lines 277-279: Hs for rRNA is 5.2x fold than the genome average. This could be roughly translated as Ne*/Ne=5.2. According to Eq 2: (1/Ne*)/(1/Ne)= Vh/C*, it can be drived that mean Ne*/Ne=C*/Vh. Then why do the authors conclude "C*=N*/N~5.2" in line 278? Wouldn't it mean that C*/Vh is roughly 5.2?

Response 20: We apologize for the confusion. To prevent misunderstandings, we have revised Equation 1 and deleted Equation 2 from the manuscript. Please refer to the Response6 for further details.

Lines 291-292: What does "a major role of stage I evolution" mean? How does it lead to lower FIS?

Response 21: We apologize for the lack of clarity in our original description, and we have revised the relevant content to make them more directly.

“In this study, we focus on multi-copy gene systems, where the evolution takes place in two stages: both within (stage I) and between individuals (stage II).”

“FIS for rDNA among 8 human individuals is 0.059 (Table 2), much smaller than 0.142 in M. m. domesticus mice, indicating minimal genetic differences across human individuals and high level of genetic identity in rDNAs between homologous chromosomes among human population. … Correlation of polymorphic sites in IGS region is shown in Supplementary Fig. 1. The results suggest that the genetic drift due to the sampling of chromosomes during sexual reproduction (e.g., segregation and assortment) is augmented substantially by the effects of homogenization process within individual. Like those in mice, the pattern indicates that intra-species polymorphism is mainly preserved within individuals.”

Line 297-300: why does the concentration at very allele frequency indicate rapid homogenization across copies? Suppose there is no inter-copy homogenization, and each copy evolves independently, wouldn't we still expect the SFS to be strongly skewed towards rare variants? It is completely unclear how homogenization processes are expected to affect the SFS.

Response 22: We appreciate the reviewer’s insightful comments and apologize for any confusion in our original explanation. To clarify:

If there is no inter-copy homogenization and each copy evolves independently, it would effectively result in an equivalent population size that is C times larger than that of single-copy genes. However, given the copies are distributed on five chromosomes, if the copies within a chromosome were fully linked, there would be no fixation at any sites. Considering the data presented in Table 4, where the substitution rate in rDNA is higher than in single-copy genes, this suggests that additional forces must be acting to homogenize the copies, even across non-homologous chromosomes.

Regarding the specific data presented in the Figure 3, the allele frequency spectrum is based on human polymorphism sites and is a folded spectrum, as the ancestral state of the alleles was not determined. High levels of homogenization would typically push variant mutations toward the extremes of the SFS, leading to fewer intermediate-frequency alleles and reduced heterozygosity. The statement that "allele frequency spectrum is highly concentrated at very low frequency within individuals" was intended to emphasize the localized distribution of variants and the high identity at each site. However, we recognize that it does not accurately reflect the role of homogenization and this conclusion cannot be directly inferred from the figure as presented. Therefore, we have removed the sentence in the text.

The evidence of gBGC in rRNA genes in great apes does not help explain the observed accelerated evolution of rDNA relative to the rest of the genome. Evidence of gBGC has been clearly demonstrated in a variety of species, including mice. It affects not only rRNA genes but also most parts of the genome, particularly regions with high recombination rates. In addition, gBGC increases the fixation probability of W>S mutations but suppresses the fixation of S>W mutations, so it is not obvious how gBGC will increase or decrease the molecular evolution rate overall.

Response 23: We have thoroughly rewritten the last section of Results. The earlier writing has misplaced the emphasis, raising many questions (as stated above). To answer them, we would have to present a new set of equations thus adding unnecessary complexities to the paper. Here is the streamlined and more logical flow of the new section.

First, Tables 4 and 5 have shown the accelerated evolution of the rRNA genes. We have now shown that rRNA genes do not have higher mutation rates. Below is copied from the revised text:

“We now consider the evolution of rRNA genes between species by analyzing the rate of fixation (or near fixation) of mutations. Polymorphic variants are filtered out in the calculation. Note that Eq. (3) shows that the mutation rate, m, determines the long-term evolutionary rate, l. Since we will compare the l values between rRNA and single-copy genes, we have to compare their mutation rates first by analyzing their long-term evolution. As shown in Table S1 l falls in the range of 50-60 (differences per Kb) for single copy genes and 40 – 70 for the non-functional parts of rRNA genes. The data thus suggest that rRNA and single-copy genes are comparable in mutation rate. Differences between their l values will have to be explained by other means.”

Second, we have shown that the accelerated evolution in mice is likely due to genetic drift, resulting in faster fixation of neutral variants. We also show that this is unlikely to be true in humans and chimpanzees; hence selection is the only possible explanation. The section below is copied from the revised text. It shows the different patterns of gene conversions between mice and apes, in agreement with the results of Tables 4 and 5. In essence, it shows that the GC ratio in apes is shifting to a new equilibrium, which is equivalent to a new adaptive peak. Selection is driving the rDNA genes to move to the new adaptive peak.

Revision - “Thus, the much accelerated evolution of rRNA genes between humans and chimpanzees cannot be entirely attributed to genetic drift. In the next and last section, we will test if selection is operating on rRNA genes by examining the pattern of gene conversion. 

3) Positive selection for rRNA mutations in apes, but not in mice – Evidence from gene conversion patterns

For gene conversion, we examine the patterns of AT-to-GC vs. GC-to-AT changes. While it has been reported that gene conversion would favor AT-to-GC over GC-to-AT conversion (Jeffreys and Neumann 2002; Meunier and Duret 2004) at the site level, we are interested at the gene level by summing up all conversions across sites. We designate the proportion of AT-to-GC conversion as f and the reciprocal, GC-to-AT, as g. Both f and g represent the proportion of fixed mutations between species (see Methods). So defined, f and g are influenced by the molecular mechanisms as well as natural selection. The latter may favor a higher or lower GC ratio at the genic level between species. As the selective pressure is distributed over the length of the gene, each site may experience rather weak pressure.

Let p be the proportion of AT sites and q be the proportion of GC sites in the gene. The flux of AT-to-GC would be pf and the flux in reverse, GC-to-AT, would be qg. At equilibrium, pf = qg. Given f and g, the ratio of p and q would eventually reach p/q \= g/f. We now determine if the fluxes are in equilibrium (pf =qg). If they are not, the genic GC ratio is likely under selection and is moving to a different equilibrium.

In these genic analyses, we first analyze the human lineage (Brown and Jiricny 1989; Galtier and Duret 2007). Using chimpanzees and gorillas as the outgroups, we identified the derived variants that became nearly fixed in humans with frequency > 0.8 (Table 6). The chi-square test shows that the GC variants had a significantly higher fixation probability compared to AT. In addition, this pattern is also found in chimpanzees (p < 0.001). In M. m. domesticus (Table 6), the chi-square test reveals no difference in the fixation probability between GC and AT (p = 0.957). Further details can be found in Supplementary Figure 2. Overall, a higher fixation probability of the GC variants is found in human and chimpanzee, whereas this bias is not observed in mice.

Tables 6-7 here

Based on Table 6, we could calculate the value of p, q, f and g (see Table 7). Shown in the last row of Table 7, the (pf)/(qg) ratio is much larger than 1 in both the human and chimpanzee lineages. Notably, the ratio in mouse is not significantly different from 1. Combining Tables 4 and 7, we conclude that the slight acceleration of fixation in mice can be accounted for by genetic drift, due to gene conversion among rRNA gene copies. In contrast, the different fluxes corroborate the interpretations of Table 5 that selection is operating in both humans and chimpanzees.”

References

Arnheim N, Treco D, Taylor B, Eicher EM. 1982. Distribution of ribosomal gene length variants among mouse chromosomes. Proc Natl Acad Sci U S A 79:4677-4680.

Brown T, Jiricny J. 1989. Repair of base-base mismatches in simian and human cells. Genome / National Research Council Canada = Génome / Conseil national de recherches Canada 31:578-583.

Cannings C. 1974. The latent roots of certain Markov chains arising in genetics: A new approach, I. Haploid models. Advances in Applied Probability 6:260-290.

Chen Y, Tong D, Wu CI. 2017. A New Formulation of Random Genetic Drift and Its Application to the Evolution of Cell Populations. Mol Biol Evol 34:2057-2064.

Chia AB, Watterson GA. 1969. Demographic effects on the rate of genetic evolution I. constant size populations with two genotypes. Journal of Applied Probability 6:231-248.

Crow JF, Kimura M. 2009. An Introduction to Population Genetics Theory: Blackburn Press.

Danecek P, Bonfield JK, Liddle J, Marshall J, Ohan V, Pollard MO, Whitwham A, Keane T, McCarthy SA, Davies RM, et al. 2021. Twelve years of SAMtools and BCFtools. Gigascience 10.

Datson NA, Morsink MC, Atanasova S, Armstrong VW, Zischler H, Schlumbohm C, Dutilh BE, Huynen MA, Waegele B, Ruepp A, et al. 2007. Development of the first marmoset-specific DNA microarray (EUMAMA): a new genetic tool for large-scale expression profiling in a non-human primate. Bmc Genomics 8:190.

Der R, Epstein CL, Plotkin JB. 2011. Generalized population models and the nature of genetic drift. Theoretical Population Biology 80:80-99.

Dover G. 1982. Molecular drive: a cohesive mode of species evolution. Nature 299:111-117.

Eickbush TH, Eickbush DG. 2007. Finely orchestrated movements: evolution of the ribosomal RNA genes. Genetics 175:477-485.

Galtier N, Duret L. 2007. Adaptation or biased gene conversion? Extending the null hypothesis of molecular evolution. Trends in Genetics 23:273-277.

Gibbs RA, Rogers J, Katze MG, Bumgarner R, Weinstock GM, Mardis ER, Remington KA, Strausberg RL, Venter JC, Wilson RK, et al. 2007. Evolutionary and Biomedical Insights from the Rhesus Macaque Genome. Science 316:222-234.

Guarracino A, Buonaiuto S, de Lima LG, Potapova T, Rhie A, Koren S, Rubinstein B, Fischer C, Abel HJ, Antonacci-Fulton LL, et al. 2023. Recombination between heterologous human acrocentric chromosomes. Nature 617:335-343.

Hartl DL, Clark AG, Clark AG. 1997. Principles of population genetics: Sinauer associates Sunderland.

Hori Y, Shimamoto A, Kobayashi T. 2021. The human ribosomal DNA array is composed of highly homogenized tandem clusters. Genome Res 31:1971-1982.

Jeffreys AJ, Neumann R. 2002. Reciprocal crossover asymmetry and meiotic drive in a human recombination hot spot. Nat Genet 31:267-271.

Karlin S, McGregor J. 1964. Direct Product Branching Processes and Related Markov Chains. Proceedings of the National Academy of Sciences 51:598-602.

Keane TM, Goodstadt L, Danecek P, White MA, Wong K, Yalcin B, Heger A, Agam A, Slater G, Goodson M, et al. 2011. Mouse genomic variation and its effect on phenotypes and gene regulation. Nature 477:289-294.

Krystal M, D'Eustachio P, Ruddle FH, Arnheim N. 1981. Human nucleolus organizers on nonhomologous chromosomes can share the same ribosomal gene variants. Proceedings of the National Academy of Sciences of the United States of America 78:5744-5748.

Meunier J, Duret L. 2004. Recombination drives the evolution of GC-content in the human genome. Molecular Biology and Evolution 21:984-990.

Nagylaki T. 1983. Evolution of a large population under gene conversion. Proc Natl Acad Sci U S A 80:5941-5945.

Nurk S, Koren S, Rhie A, Rautiainen M, Bzikadze AV, Mikheenko A, Vollger MR, Altemose N, Uralsky L, Gershman A, et al. 2022. The complete sequence of a human genome. Science 376:44-53.

Ohta T. 1985. A model of duplicative transposition and gene conversion for repetitive DNA families. Genetics 110:513-524.

Ohta T. 1976. Simple model for treating evolution of multigene families. Nature 263:74-76.

Ohta T, Dover GA. 1984. The Cohesive Population Genetics of Molecular Drive. Genetics 108:501-521.

Ohta T, Dover GA. 1983. Population genetics of multigene families that are dispersed into two or more chromosomes. Proc Natl Acad Sci U S A 80:4079-4083.

Ruan Y, Wang X, Hou M, Diao W, Xu S, Wen H, Wu C-I. 2024. Resolving Paradoxes in Molecular Evolution: The Integrated WF-Haldane (WFH) Model of Genetic Drift. bioRxiv:2024.2002.2019.581083.

Smirnov E, Chmúrčiaková N, Liška F, Bažantová P, Cmarko D. 2021. Variability of Human rDNA. Cells 10.

Smith GP. 1976. Evolution of Repeated DNA Sequences by Unequal Crossover. Science 191:528-535.

Smith GP. 1974a. Unequal crossover and the evolution of multigene families. Cold Spring Harbor symposia on quantitative biology 38:507-513.

Smith GP. 1974b. Unequal Crossover and the Evolution of Multigene Families.  38:507-513.

Stults DM, Killen MW, Pierce HH, Pierce AJ. 2008. Genomic architecture and inheritance of human ribosomal RNA gene clusters. Genome Res 18:13-18.

van Sluis M, Gailín M, McCarter JGW, Mangan H, Grob A, McStay B. 2019. Human NORs, comprising rDNA arrays and functionally conserved distal elements, are located within dynamic chromosomal regions. Genes Dev 33:1688-1701.

Wall JD, Frisse LA, Hudson RR, Di Rienzo A. 2003. Comparative linkage-disequilibrium analysis of the beta-globin hotspot in primates. Am J Hum Genet 73:1330-1340.

Author Response

The following is the authors’ response to the current reviews.

Responses to the reviewers

We thank the editor and reviewers for their insightful feedback and valuable suggestions on our revised manuscript. In this reply, we provided further clarifications and made changes accordingly. Reviewers’ comments are in bold, and our responses are immediately below. Changes in the main text are presented in italics, accompanied by the specific line numbers in the revised manuscript where these changes can be found. Below, we respond to each reviewer’s comments in turn.

Reviewer #1 (Public Review):

Ps observed 24 objects and were asked which afforded particular actions (14 action types). Affordances for each object were represented by a 14-item vector, values reflecting the percentage of Ps who agreed on a particular action being afforded by the object. An affordance similarity matrix was generated which reflected similarity in affordances between pairs of objects. Two clusters emerged, reflecting correlations between affordance ratings in objects smaller than body size and larger than body size. These clusters did not correlate themselves. There was a trough in similarity ratings between objects ~105 cm and ~130 cm, arguably reflecting the body size boundary. The authors subsequently provide some evidence that this clear demarcation is not simply an incidental reflection of body size, but likely causally related. This evidence comes in the flavour of requiring Ps to imagine themselves as small as a cat or as large as an elephant and showing a predicted shift in the affordance boundary. The manuscript further demonstrates that ChatGPT (theoretically interesting because it's trained on language alone without sensorimotor information; trained now on words rather than images) showed a similar boundary.

The authors also conducted a small MRI study task where Ps decide whether a probe action was affordable (graspable?) and created a congruency factor according to the answer (yes/no). There was an effect of congruency in posterior fusiform and superior parietal lobule for objects within body size range, but not outside. No effects in LOC or M1.

The major strength of this manuscript in my opinion is the methodological novelty. I felt the correlation matrices were a clever method for demonstrating these demarcations, the imagination manipulation was also exciting, and the ChatGPT analysis provided excellent food for thought. These findings are important for our understanding of the interactions between action and perception, and hence for researchers from a range of domains of cognitive neuroscience.

The major element that limits conclusions is that an MRI study with 12 P in this context can really only provide pilot data. Certainly the effects are not strong enough for 12 P to generate much confidence. The others of my concerns have been addressed in the revision.

Reviewer #1 (Recommendations For The Authors):

I think that the authors need to mention in the abstract that the MRI study constitutes a small pilot.

Response: We appreciate the reviewer’s positive evaluation and constructive suggestions. In response to the concern about the limited number of participants in the fMRI study, we fully acknowledge the implications this has on the generalizability and robustness of our findings related to the congruency effect. To clarity, we have explicitly stated its preliminary nature of the MRI study in the abstract [line 22]: “A subsequent fMRI experiment offered preliminary evidence of affordance processing exclusively for objects within the body size range, but not for those beyond.”

Reviewer #2 (Public Review):

Summary

In this work, the authors seek to test a version of an old idea, which is that our perception of the world and our understanding of the objects in it are deeply influenced by the nature of our bodies and the kinds of behaviours and actions that those objects afford. The studies presented here muster three kinds of evidence for a discontinuity in the encoding of objects, with a mental "border" between objects roughly of human body scale or smaller, which tend to relate to similar kinds of actions that are yet distinct from the kinds of actions implied by human-or-larger scale objects. This is demonstrated through observers' judgments of the kinds of actions different objects afford; through similar questioning of AI large-language models (LLMs); and through a neuroimaging study examining how brain regions implicated in object understanding make distinctions between kinds of objects at human and larger-than-human scales.

Strengths 

The authors address questions of longstanding interest in the cognitive neurosciences -- namely how we encode and interact with the many diverse kinds of objects we see and use in daily life. A key strength of the work lies in the application of multiple approaches. Examining the correlations among kinds of objects, with respect to their suitability for different action kinds, is novel, as are the complementary tests of judgments made by LLMs. The authors include a clever manipulation in which participants are asked to judge action-object pairs, having first adopted the imagined size of either a cat or an elephant, showing that the discontinuity in similarity judgments effectively moved to a new boundary closer to the imagined scale than the veridical human scale. The dynamic nature of the discontinuity hints that action affordances may be computed dynamically, "on the fly", during actual action behaviours with objects in the real world.

Weaknesses 

A limitation of the tests of LLMs may be that it is not always known what kinds of training material was used to build these models, leading to a possible "black box" problem. Further, presuming that those models are largely trained on previous human-written material, it may not necessarily be theoretically telling that the "judgments" of these models about action-object pairs shows human-like discontinuities. Indeed, verbal descriptions of actions are very likely to mainly refer to typical human behaviour, and so the finding that these models demonstrate an affordance discontinuity may simply reflect those statistics, rather than providing independent evidence for affordance boundaries.

The relatively small sample size of the brain imaging experiment, and some design features (such as the task participants performed, and the relatively narrow range of objects tested) provide some limits on the extent to which it can be taken as support for the authors' claims.

Response: We thank the reviewer for the positive evaluation and the constructive comments. We agree that how LLMs work is a “black box”, and thus it is speculative to assume them to possess any human-like ability, because, as the reviewer pointed out, “these models demonstrate an affordance discontinuity may simply reflect those statistics.” Indeed, our manuscript has expressed a similar idea [line 338]: “We speculated that ChatGPT models may have formed the affordance boundary through a human prism ingrained within its linguistic training corpus.” That is, our intention was not to suggest that such information could replace sensorimotor-based interaction or achieve human-level capability, but rather to highlight that embodied interaction is necessary. Additionally, the scope of the present study does not extend to elucidating the mechanisms behind LLMs’ resemblance of affordance boundary, whether through statistical learning or actual comprehension. To clarify this point, in the revised manuscript, we have clarified that the mechanisms underlying the observed affordance boundary in LLMs may be different from human cognitive processes, and advocated future studies to explore this possibility [line 415]: “Nevertheless, caution should be taken when interpreting the capability of LLMs like ChatGPT, which are often considered “black boxes.” That is, our observation indicates that certain sensorimotor information is embedded within human language materials presumably through linguistic statistics, but it is not sufficient to assert that LLMs have developed a human-like ability to represent affordances. Furthermore, such information alone may be insufficient for LLMs to mimic the characteristics of the affordance perception in biological intelligence. Future studies are needed to elucidate such limitation.”

Regarding the concern about the models’ results not “providing independent evidence for affordance boundaries”, our objective in employing LLMs was to explore if an affordance boundary could emerge from conceptual knowledge without direct sensorimotor experience, rather than to validate the existence of the affordance boundary per se.

As for the concern about the limitations imposed by the small sample size and certain design features of our brain imaging experiment, please see our reply to Reviewer #1.

Reviewer #3 (Public Review):

Summary:

Feng et al. test the hypothesis that human body size constrains the perception of object affordances, whereby only objects that are smaller than the body size will be perceived as useful and manipulable parts of the environment, whereas larger objects will be perceived as "less interesting components."

To test this idea, the study employs a multi-method approach consisting of three parts:

In the first part, human observers classify a set of 24 objects that vary systematically in size (e.g., ball, piano, airplane) based on 14 different affordances (e.g., sit, throw, grasp). Based on the average agreement of ratings across participants, the authors compute the similarity of affordance profiles between all object pairs. They report evidence for two homogenous object clusters that are separated based on their size with the boundary between clusters roughly coinciding with the average human body size. In follow-up experiments, the authors show that this boundary is larger/smaller in separate groups of participants who are instructed to imagine themselves as an elephant/cat.

In the second part, the authors ask different large language models (LLMs) to provide ratings for the same set of objects and affordances and conduct equivalent analyses on the obtained data. Some, but not all, of the models produce patterns of ratings that appear to show similar boundary effects, though less pronounced and at a different boundary size than in humans.

In the third part, the authors conduct an fMRI experiment. Human observers are presented with four different objects of different sizes and asked if these objects afford a small set of specific actions. Affordances are either congruent or incongruent with objects. Contrasting brain activity on incongruent trials against brain activity on congruent trials yields significant effects in regions within the ventral and dorsal visual stream, but only for small objects and not for large objects.

The authors interpret their findings as support for their hypothesis that human body size constrains object perception. They further conclude that this effect is cognitively penetrable, and only partly relies on sensorimotor interaction with the environment (and partly on linguistic abilities).

Strengths:

The authors examine an interesting and relevant question and articulate a plausible (though somewhat underspecified) hypothesis that certainly seems worth testing. Providing more detailed insights into how object affordances shape perception would be highly desirable. Their method of analyzing similarity ratings between sets of objects seems useful and the multi-method approach is original and interesting.

Weaknesses:

The study presents several shortcomings that clearly weaken the link between the obtained evidence and the drawn conclusions. Below I outline my concerns in no particular order:

(1) It is not entirely clear to me what the authors are proposing and to what extent the conducted work actually speaks to this. For example, in the introduction, the authors write that they seek to test if body size serves not merely as a reference for object manipulation but also "plays a pivotal role in shaping the representation of objects." This motivation seems rather vague motivation and it is not clear to me how it could be falsified.

Overall, the lack of theoretical precision makes it difficult to judge the appropriateness of the approaches and the persuasiveness of the obtained results. I would strongly suggest clarifying the theoretical rationale and explaining in more detail how the chosen experiments allow them to test falsifiable predictions.

(2) The authors used only a very small set of objects and affordances in their study and they do not describe in sufficient detail how these stimuli were selected. This renders the results rather exploratory and clearly limits their potential to discover general principles of human perception. Much larger sets of objects and affordances and explicit data-driven approaches for their selection would provide a more convincing approach and allow the authors to rule out that their results are just a consequence of the selected set of objects and actions.

(3) Relatedly, the authors could be more thorough in ruling out potential alternative explanations. Object size likely correlates with other variables that could shape human similarity judgments and the estimated boundary is quite broad (depending on the method, either between 80 and 150 cm or between 105 to 130 cm). More precise estimates of the boundary and more rigorous tests of alternative explanations would add a lot to strengthen the authors' interpretation.

(4) While I appreciate the manipulation of imagined body size, as a clever way to solidify the link between body size and affordance perception, I find it unfortunate that it is implemented in a between-subjects design, as this clearly leaves open the possibility of pre-existing differences between groups. I certainly disagree with the authors' statement that their findings suggest "a causal link between body size and affordance perception."

(5) The use of LLMs in the current study is not clearly motivated and I find it hard to understand what exactly the authors are trying to test through their inclusion. As it currently stands, I find it hard to discern how the presence of perceptual boundaries in LLMs could constitute evidence for affordance-based perception.

(6) Along the same lines, the fMRI study also provides little evidence to support the authors' claims. The use of congruency effects as a way of probing affordance perception is not well motivated. Importantly (and related to comment 2 above), the very small set of objects and affordances in this experiment heavily complicates any conclusions about object size being the crucial variable determining the occurrence of congruency effects.

Overall, I consider the main conclusions of the paper to be far beyond the reported data. Articulating a clearer theoretical framework with more specific hypotheses as well as conducting more principled analyses on more comprehensive data sets could help the authors obtain stronger tests of their ideas.

Response: We appreciate the insightful inquiries regarding our manuscript. Below, we explained the theoretical motivation and rationale of each part of our experiments.

In response to the reviewer’s insights, we have modified the expression “plays a pivotal role in shaping the representation of objects” in the revised manuscript and have restated the general question of our study in the introduction. Our motivation is on the long-lasting debate over the representation versus direct perception of affordance, specifically examining the “representationalization” of affordance. That is, we tested whether object affordance simply covaried directly with continuous constraints such as object size, a perspective aligned with the representation-free (direct perception) view, or whether affordance became representationalized, adhering to the representation-based view, constrained by body size. Such representationalization would generate a categorization between objects that are affordable and the environment that exceeds affordance.

To test these hypotheses, we first delineated the affordance of various objects. We agree with the reviewer that in this step a broader selection of objects and actions could mitigate the risk of our results being influenced by the specific selection of objects and actions. However, our results are unlikely to be biased, because our selection was guided by two key criteria, rather than being arbitrary. First, the objects were selected from the dataset in Konkle and Oliva's study (2011), which systematically investigated object size’ impact on object recognition, thus providing a well-calibrated range of sizes (i.e., from 14 cm to 7,618 cm) reflective of real-world objects. Second, the selected actions covered a wide range of daily humans-objects/environments interactions, from single-point movements (e.g., hand, foot) to whole-body movements (e.g., lying, standing) based on the kinetics human action video dataset (Kay et al., 2017). Thus, this set of objects and actions is a representative sampling of typical human experiences.

Upon demonstrating a trough in perceived affordance similarity, we recognized the location of the affordance boundary coincidentally fell within the range of human body size. We agree with the reviewer that this observation of the coincidence between body size and the location of boundary alone is not sufficient for a mechanistic explanation, because variables co-varying with object sizes might also generate this coincidence. The identification of a more precise location for the boundary unlikely rules out alternative explanations of this kind. To establish a causal link between body size and the affordance boundary, we opted for a direct manipulation of body sizes through imagination, while keeping all other variables constant across conditions. This approach allowed us to examine whether and how the affordance boundary shifts in response to body size changes.

Regarding the between-subjects design of the imagination experiment, we wish to clarify that this design aimed to prevent carryover effects. Although a within-subjects design indeed is more sensitive in detecting manipulation effects by accounting for subject variability, it risks contamination across conditions. Specifically, transitioning immediately between different imagined body sizes poses a challenge, and sequential participation could induce undesirable response strategies, such as deliberately altering responses to the same objects in different conditions. The between-subjects design, which susceptible to participant variability (e.g., “pre-existing differences between groups” suggested by the reviewer), avoids such contamination. In addition, we employed random assignment of participants to different conditions (cat-size versus elephant-size).

The body imagination experiment provided causal evidence of an embodied discontinuity, suggesting the boundary is tied to the agent’s motor capacity, rather than amodal sources. The LLMs experiment then sought to test a prediction from the embodied theories of cognition: the supramodality of object perception. Especially, we asked whether the embodied discontinuity is supramodally accessible, using LLMs to assess whether affordance perception discretization is supramodally accessible beyond the sensorimotor domain through linguistic understanding. From this perspective, our LLM experiment was employed not to affirm affordance-based perception but to examine and support a prediction by the embodied theories of cognition.

Finally, our preliminary fMRI study aimed to conceptually replicate the perceptual discontinuity and explore it neural correlates using a subset of objects and actions from the behaviour experiments. This approach was chosen to achieve stable neural responses and enhance study power, employing the congruent effect (congruent - incongruent) as a metric for affordance processing (e.g., Kourtis et al., 2018), which reflects facilitated responses when congruent with objects’ affordances (e.g., Ellis & Tucker, 2000). Nevertheless, we recognize the limitation of a relatively small sample sizes, for details please see our reply to the reviewer #1.

In summary, our findings contribute to the discourse on computationalism’s representation concept and influence of these representations, post-discretization, on processes beyond the sensorimotor domain. We hope that these additional explanations and revisions effectively address the concerns raised and demonstrate our commitment to enhancing the quality of our work in light of your valuable feedback. By acknowledging these limitations and directions for future research, we hope to further the discourse on affordance perception and embodied cognition.

References

Ellis, R., & Tucker, M. (2000). Micro‐affordance: The potentiation of components of action by seen objects. British Journal of Psychology, 91(4), 451-471.

Kay, W., Carreira, J., Simonyan, K., Zhang, B., Hillier, C., Vijayanarasimhan, S., ... & Zisserman, A. (2017). The kinetics human action video dataset. arXiv preprint arXiv:1705.06950.

Konkle, T., & Oliva, A. (2011). Canonical visual size for real-world objects. Journal of Experimental Psychology: human perception and performance, 37(1), 23.

Kourtis, D., Vandemaele, P., & Vingerhoets, G. (2018). Concurrent cortical representations of function-and size-related object affordances: an fMRI study. Cognitive, Affective, & Behavioral Neuroscience, 18, 1221-1232.

The following is the authors’ response to the original reviews.

Responses to the reviewers

We deeply appreciate the reviewers’ comments. In response to the concerns raised, we have revised the manuscript accordingly. Below we address each of the reviewers’ comments in turn. Reviewers’ comments are in bold, and our responses are immediately below. Changes in the main text are presented in italics, followed by corresponding page and line numbers in the revised manuscript. We also highlighted tracks of change in the revised manuscript.

Reviewer #1 (Public Review):

(1) The main behavioural work appears well-powered (>500 Ps). This sample reduces to 100 for the imagination study, after removing Ps whose imagined heights fell within the human range (100-200 cm). Why 100-200 cm? 100 cm is pretty short for an adult. Removing 80% of data feels like conclusions from the imagination study should be made with caution.

R1: Sorry for the confusion. We did not remove 80% of the participants; instead, a separate sample of participants was recruited in the imagination experiment. The size of this sample (100 participants) was indeed smaller than the first experiment (528 participants), because the first experiment was set for exploratory purposes and was designed to be over-powered. Besides, inspection of the data of the first sample showed that the affordance pattern became stable after the first 50 participants. We explained this consideration in the revised manuscript:

(p 21, ln 490) “…, another one hundred and thirty-nine participants from the same population were recruited from the same platform. We chose a smaller sample size for the imagination experiment compared to that for the object-action relation judgement task, because inspection of the data of the first sample showed that the affordance pattern became stable after the first 50 participants.”

The average adult human height ranges from 140-170 cm for women and 150180 cm for men (NCD-RisC, 2016). Accordingly, the criterion of 100-200 cm covered this range and was set to ensure that participants unambiguously imagined a body schema different from that of human, as the tallest domestic cat below 100 cm according to the Guinness World Records and an elephant above 200 cm according to Crawley et al. (2017). We clarified these considerations in the revised manuscript:

(p 21, ln 494) “To maximize the validity of the manipulation, data from participants whose imagined height fell within the average human size range (100cm - 200cm) were excluded from further analysis. Consequently, 100 participants (49 males, aged from 17 to 39 years, mean age = 23.2 years) remained in the analysis. This exclusion criterion was broader than the standard adult human height range of 140cm to 180cm (NCD-RisC, 2016). This approach ensured that our analysis focused on participants who unambiguously imagined a body schema different from humans, yet within the known height range of cats and elephants.”

In addition, we also reanalysed the data with a more conservative criterion of 140cm to 180cm, and the results remained.

(2) There are only 12 Ps in the MRI study, which I think should mean the null effects are not interpreted. I would not interpret these data as demonstrating a difference between SPL and LOC/M1, but rather that some analyses happened to fall over the significance threshold and others did not.

R2: We would like to clarify that the null hypothesis of this fMRI study is the lack of two-way interaction between object size and object-action congruency, which was rejected by the observed significant interaction. That is, the interpretation of the present study did not rely on accepting any null effect.

Having said this, we admit that the fMRI experiment is exploratory and the sample size is small (12 participants), which might lead to low power in estimating the affordance effect. In the revision, we acknowledge this issue explicitly:

(p 16, ln 354) “…, supporting the idea that affordance is typically represented only for objects within the body size range. While it is acknowledged that the sample size of the fMRI study was small (12 participants), necessitating cautious interpretation of its results, the observed neural-level affordance discontinuity is notable. That is, qualitative differences in neural activity between objects within the affordance boundary and those beyond replicated our behavioral findings. This convergent evidence reinforced our claim that objects were discretized into two broad categories along the continuous size axis, with affordance only being manifested for objects within the boundary.”

(3) I found the MRI ROI selection and definition a little arbitrary and not really justified, which rendered me even more cautious of the results. Why these particular sensory and motor regions? Why M1 and not PMC or SMA? Why SPL and not other parietal regions? Relatedly, ROIs were defined by thresholding pF and LOC at "around 70%" and SPL and M1 "around 80%", and it is unclear how and why these (different) thresholds were determined.

R3: Our selection of these specific sensory and motor regions was based on prior literature reporting their distinct contribution to affordance perception (e.g., Borghi, 2005; Sakreida et al., 2016). The pFs was chosen as a representative region of the ventral visual stream, involved in object identification and classification, and the SPL was chosen as a representative region of the dorsal visual stream, involved in object perception and manipulation. The primary motor cortex (M1) has also been reported involved in affordance processing (e.g., McDannald et al., 2018), and we chose this region to probe the affordance congruency effect in the motor execution stage of the sense-think-act pathway. We did not choose the premotor cortex (PMC) and the supplementary motor area (SMA) because they were proposedly also involved in processes beyond motor execution (e.g., Hertrich et al., 2016; Kantak et al., 2012), and if any effect was observed, one cannot exclusively attribute the effect to motor execution. As for the parietal regions, our choice of the SPL not IPL/IPS is based on the meta-analysis of affordance processing areas where only the SPL shows consistent activation for both stable and variable affordances (Sakreida et al., 2016). We chose the SPL to capture effects on either type of affordances. In revision, we explained these considerations in the revised manuscript:

(p 14, ln 280) “In addition to the pFs and SPL, we also examined the congruency effect in the lateral occipital cortex (LO), which is involved in object representation (e.g., Grill-Spector et al., 2000; Konkle & Caramazza, 2013) and provides inputs to both the pFs and SPL (Hebart et al., 2018). Meanwhile, the primary motor cortex (M1), which receives inputs from the dorsal stream (Vainio & Ellis, 2020), is involved in affordance processing (e.g., McDannald et al., 2018) and action executions (Binkofski et al., 2002).”

(p 29, ln 684) “We chose the pFs, LO, SPL, and M1 as ROIs based on existing literature highlighting their distinct contributions to affordance perception (Borghi, 2005; Sakreida et al., 2016).”

Regarding ROI thresholding, we apologize for the lack of clarity in reporting the thresholds in the original manuscript. The thresholds were different between ventral regions (from Zhen et al., 2015) and dorsal regions (from Fan et al., 2016) because they are from two different atlases. The former was constructed by probability maps of task-state fMRI activity during localizer contrast with stationary images and the latter by a parcellation of the brain's functional connectivity; therefore, the numerical values in these two atlases are not comparable. To extract ROIs with comparable sizes, we selected a threshold of 55% for the pFs, 90% for the LO, 78% for the SPL, and 94% for the M1 in the original manuscript.

To rule out the possibility that the results were distorted by the specific choice of thresholds, we re-ran the analysis with a threshold 80% for all ROIs (resulting in 456 voxels in the lpFs, 427 voxels in the rpFs, 1667 voxels in the lLO, 999 voxels in the rLO, 661 voxels in the lSPL, 310 voxels in the rSPL, 231 voxels in the lM1, and 327 voxels in the rM1) with the 2-by-2 repeated-measures ANOVA. Our results remained the same qualitatively. A significant interaction between object type and congruency was observed in the pFs (F(1,11) = 24.87, p <.001, 𝜂2=.69) and SPL (F(1,11) = 14.62, p =.003, 𝜂2=.57). The simple effect analysis revealed the congruency effect solely for objects within body size range (pFs: p =.003; SPL: p <.001), not for objects beyond (ps >.30). For the M1 and LO, neither significant main effects (ps >.11) nor interactions were found (ps >.20).

We clarified our choice of thresholds in the methods section in the revised manuscript:

(p 29, ln 686) “Eight ROIs depicted in Fig. 3b were constructed based on the overlap between the whole-brain map activated by both objects within and beyond and corresponding functional atlases (the pFs and LO from Zhen et al., 2015; the SPL and M1 from Fan et al., 2016). To achieve ROIs of similar sizes, we applied varying thresholds to each cortical area: for the pFs and LO, the atlases were thresholded at 55% and 90%, resulting in 266 voxels in the lpFs, 427 in the rpFs, 254 in the lLO and 347 in the rLO; for the SPL and M1, the atlases were thresholded at 78% and 94%, resulting in 661 voxels in the lSPL, 455 in the rSPL, 378 in the lM1, and 449 in the rM1. In the subsequent analysis, homologous areas spanning both cortical hemispheres were merged.”

(4) Discussion and theoretical implications. The authors discuss that the MRI results are consistent with the idea we only represent affordances within body size range. But the interpretation of the behavioural correlation matrices was that there was this similarity also for objects larger than body size, but forming a distinct cluster. I therefore found the interpretation of the MRI data inconsistent with the behavioural findings.

R4: We speculated that the similarity in action perception among objects beyond the body size range may be due to these objects being similarly conceptualized as ‘environment’, in contrast to the objects within the body size range, which are categorized differently, namely as the ‘objects for the animal.’ Accordingly, in cortical regions involved in object processing, objects conceptualized as ‘environment’ unlikely showed the congruency effect, distinct from objects within the body size range. We have explained this point in the revised manuscript:

(p 17, ln 370) “…which resonates the embodied influence on the formation of abstract concepts (e.g., Barsalou, 1999; Lakoff & Johnson, 1980) of objects and environment. Consistently, our fMRI data did not show the congruency effect for objects beyond the body size range, distinct from objects within this range, suggesting a categorization influenced by objects’ relative size to the human body.”

(5) In the discussion, the authors outline how this work is consistent with the idea that conceptual and linguistic knowledge is grounded in sensorimotor systems. But then reference Barsalou. My understanding of Barsalou is the proposition of a connectionist architecture for conceptual representation. I did not think sensorimotor representation was privileged, but rather that all information communicates with all other to constitute a concept.

R5: We are sorry for the confusion. We do not intend to argue that the sensorimotor representation is privileged. Instead, we would like to simply emphasize their engagement in concept. According to our understanding, Barsalou’s Perceptual Symbol Theory proposes that grounded concepts include sensorimotor information, and conceptual knowledge is grounded in the same neural system that supports action (Barsalou, 1999). This is consistent with our proposal that the affordance boundary locked to an animal’s sensorimotor capacity might give rise to a conceptual-ish representation of object-ness specific to the very animal. We have clarified this point in the introduction and discussion on the conceptual knowledge and sensorimotor information:

In the introduction (p 2, ln 59) “…, and the body may serve as a metric that facilitates meaningful engagement with the environment by differentiating objects that are accessible for interactions from those not. Further, grounded cognition theory (see Barsalou, 2008 for a review) suggests that the outputs of such differentiation might transcend sensorimotor processes and integrate into supramodal concepts and language. From this perspective, we proposed two hypotheses...”

In the discussion (p 18, ln 392) “Indeed, it has been proposed that conceptual knowledge is grounded in the same neural system that supports action (Barsalou, 1999; Glenberg et al., 2013; Wilson & Golonka, 2013), thereby suggesting that sensorimotor information, along with other modal inputs, may be embedded in language (e.g., Casasanto, 2011; Glenberg & Gallese, 2012; Stanfield & Zwaan, 2001), as the grounded theory proposed (see Barsalou, 2008 for a review).”

(6) More generally, I believe that the impact and implications of this study would be clearer for the reader if the authors could properly entertain an alternative concerning how objects may be represented. Of course, the authors were going to demonstrate that objects more similar in size afforded more similar actions. It was impossible that Ps would ever have responded that aeroplanes afford grasping and balls afford sitting, for instance. What do the authors now believe about object representation that they did not believe before they conducted the study? Which accounts of object representation are now less likely?

R6: We thank the reviewer for this suggestion. The theoretical motivation of the present study is to explore whether, for continuous action-related physical features (such as object size relative to the agents), affordance perception introduces discontinuity and qualitative dissociation, i.e., to allow the sensorimotor input to be assigned into discrete states/kinds, as representations envisioned by the computationalists; alternatively, whether the activity may directly mirror the input, free from discretization/categorization/abstraction, as proposed by the Replacement proposal of some embodied theories on cognition.

By addressing this debate, we hoped to shed light on the nature of representation in, and resulted from, the vision-for-action processing. Our finding of affordance discontinuity suggests that sensorimotor input undergoes discretization implied in the computationalism idea of representation. Further, not contradictory to the claims of the embodied theories, these representations do shape processes out of the sensorimotor domain, but after discretization.

We have now explained our hypotheses and alternatives explicitly in the revised introduction and discussion:

In the introduction (p 2, ln 45) “However, the question of how object perception is influenced by the relative size of objects in relation to the human body remains open. Specifically, it is unclear whether this relative size simply acts as a continuous variable for locomotion reference, or if it affects differentiating and organizing object representation based on their ensued affordances.”

In the discussion (p 14, ln 295) “One long-lasting debate on affordance centers on the distinction between representational and direct perception of affordance. An outstanding theme shared by many embodied theories of cognition is the replacement hypothesis (e.g., Van Gelder, 1998), which challenges the necessity of representation as posited by computationalism’s cognitive theories (e.g., Fodor, 1975). This hypothesis suggests that input is discretized/categorized and subjected to abstraction or symbolization, creating discrete stand-ins for the input (e.g., representations/states). Such representationalization would lead to a categorization between the affordable (the objects) and those beyond affordance (the environment), in contrast to the perspective offered by embodied theories. The present study probed this ‘representationalization’ of affordance by examining whether affordance perception introduces discontinuity and qualitative dissociation in response to continuous action-related physical features (such as object size relative to the agents), which allows sensorimotor input to be assigned into discrete states/kinds, in line with the representation-based view under the constraints of body size. Alternatively, it assessed whether activity directly mirrors the input, free from discretization/categorization/abstraction, in line with the representation-free view.

First, our study found evidence demonstrating discretization in affordance perception. Then, through the body imagination experiment, we provided causal evidence suggesting that this discretization originates from sensorimotor interactions with objects rather than amodal sources, such as abstract object concepts independent of agent motor capability. Finally, we demonstrated the supramodality of this embodied discontinuity by leveraging the recent advances in AI. We showed that the discretization in affordance perception is supramodally accessible to disembodied agents such as large language models (LLMs), which lack sensorimotor input but can access linguistic materials built upon discretized representations. These results collectively suggest that sensorimotor input undergoes discretization, as implied in the computationalism’s idea of representation. Note that, these results are not contradictory to the claim of the embodied theories, as these representations do shape processes beyond the sensorimotor domain but after discretization.

This observed boundary in affordance perception extends the understanding of the discontinuity in perception in response to the continuity of physical inputs (Harnad, 1987; Young et al., 1997).”

Reviewer #1 (Recommendations For The Authors):

a) I would recommend providing further justification for why 100-200 cm were used as the cut-offs reflecting acceptable imagined body size. Were these decisions preregistered anywhere? If so, please state.

Ra: Please see R1.

b) I would encourage the authors to call the MRI a small pilot study throughout, including in the abstract.

Rb: We completely agree and have indicated the preliminary nature of this study in the revised version:

(p 11, ln 236) “To test this speculation, we ran an fMRI experiment with a small number of participants to preliminarily investigate the neural basis of the affordance boundary in the brain by measuring neural activity in the dorsal and ventral visual streams when participants were instructed to evaluate whether an action was affordable by an object (Fig. 3a).”

c) Please provide much further justification of ROI selection, why these thresholds were chosen, and therefore why they are different across regions.

Rc: Please see R3.

d) Further elucidation in the discussion would help the reader interpret the MRI data, which should always be interpreted also in light of the behavioural findings.

Rd: Please see R4.

e) The authors may wish to outline precisely what they claim concerning the nature of conceptual/linguistic representation. Is sensorimotor information privileged or just part of the distributed representation of concepts?

Re: This is a great point. For details of corresponding revision, please see R5.

f) There are some nods to alternative manners in which we plausibly represent objects (e.g. about what the imagination study tells us) but I think this theoretical progression should be more prominent.

Rf: We thank the reviewer for this suggestion. For details of corresponding revision, please see R6.

Reviewer #2 (Public Review):

(1) A limitation of the tests of LLMs may be that it is not always known what kinds of training material was used to build these models, leading to a possible "black box" problem. Further, presuming that those models are largely trained on previous human-written material, it may not necessarily be theoretically telling that the "judgments" of these models about action-object pairs show human-like discontinuities. Indeed, verbal descriptions of actions are very likely to mainly refer to typical human behaviour, and so the finding that these models demonstrate an affordance discontinuity may simply reflect those statistics, rather than evidence that affordance boundaries can arise independently even without "organism-environment interactions" as the authors claim here.

R1: We agree that how LLMs work is a “black box”, and thus it is speculative to assume them to possess any human-like ability, because, as the reviewer pointed out, “these models demonstrate an affordance discontinuity may simply reflect those statistics.” Indeed, our manuscript has expressed a similar idea: “We speculated that ChatGPT models may have formed the affordance boundary through a human prism ingrained within its linguistic training corpus. (p 16 ln 338)”. That is, we did not intend to claim that such information is sufficient to replace sensorimotor-based interaction, or to restore human-level capability, for which we indeed speculated that embodied interaction is necessary. In the revised manuscript, we have clarified our stand that the mechanism generating the observed affordance boundary in LLMs might be different from that in human cognition, and urged future studies to explore this possibility:

(p 18, ln 413) “…, as well as alignment methods used in fine-tuning the model (Ouyang et al., 2022). Nevertheless, caution should be taken when interpreting the capabilities of LLMs like ChatGPT, which are often considered “black boxes.” That is, our observation indicates that some degree of sensorimotor information is embedded within human language materials presumably through linguistic statistics, but it is not sufficient to assert that LLMs have developed a human-like ability to represent affordances. Furthermore, such information alone may be insufficient for LLMs to mimic the characteristics of the affordance perception in biological intelligence. Future studies are needed to elucidate such limitation.”

Indeed, because of this potential dissociation, our LLM study might bear novel implications for the development of AI agents. We elaborated on them in the revised discussion on LLMs:

(p 19, ln 427) “…, represents a crucial human cognitive achievement that remains elusive for AI systems. Traditional AI (i.e., task-specific AI) has been confined with narrowly defined tasks, with substantial limitations in adaptability and autonomy. Accordingly, these systems have served primarily as tools for humans to achieve specific outcomes, rather than as autonomous agents capable of independently formulating goals and translating them into actionable plans. In recent years, significant efforts have been directed towards evolving traditional AI into more agent-like entities, especially in domains like navigation, object manipulation, and other interactions with the physical world. Despite these advancements, the capabilities of AI still fall behind human-level intelligence. On the other hand, embodied cognition theories suggest that sensorimotor interactions with the environment are foundational for various cognitive domains. From this point of view, endowing AI with human-level abilities in physical agent-environment interactions might provide an unreplaceable missing piece for achieving Artificial General Intelligence (AGI). This development would significantly facilitate AI’s role in robotics, particularly in actions essential for survival and goal accomplishment, a promising direction for the next breakthrough in AI (Gupta et al., 2021; Smith & Gasser, 2005).

However, equipping a disembodied AI with the ability for embodied interaction planning within a specific environment remains a complex challenge. By testing the potential representationalization of action possibilities (affordances) in both humans and LLMs, the present study suggests a new approach to enhancing AI’s interaction ability with the environment. For instance, our finding of supramodal affordance representation may indicate a possible pathway for disembodied LLMs to engage in embodied physical interactions with their surroundings. From an optimistic view, these results suggest that LLM-based agents, if appropriately designed, may leverage affordance representations embedded in language to interact with the physical world. Indeed, by clarifying and aligning such representations with the physical constitutes of LLM-based agents, and even by explicitly constructing an agent-specific object space, we may foster the sensorimotor interaction abilities of LLM-based agents. This progression could lead to achieving animal-level interaction abilities with the world, potentially sparking new developments in the field of embodied cognition theories.”

(2) The authors include a clever manipulation in which participants are asked to judge action-object pairs, having first adopted the imagined size of either a cat or an elephant, showing that the discontinuity in similarity judgments effectively moved to a new boundary closer to the imagined scale than the veridical human scale. The dynamic nature of the discontinuity suggests a different interpretation of the authors' main findings. It may be that action affordance is not a dimension that stably characterises the long-term representation of object kinds, as suggested by the authors' interpretation of their brain findings, for example. Rather these may be computed more dynamically, "on the fly" in response to direct questions (as here) or perhaps during actual action behaviours with objects in the real world.

R2: We thank the reviewer for pointing out the dynamic nature of affordance perception in our study. This feature indeed reinforced our attribution of the boundary into an affordance-based process instead of a conceptual or semantic process, the latter of which would predict the action possibilities being a fixed belief about the objects, instead of being dynamically determined according to the feature of the agent-object dyads. In addition, this dynamic does not contradict with our interpretation of the observed boundary in affordance perception. With this observation, we speculated that continuous input was abstracted or representationalized into discontinued categories, and the boundary between these categories was drawn according to the motor capacity of the agent. The finding of the boundary adapting to manipulation on body schema suggests that the abstraction/representationalization dynamically updates according to the current belief of motor capacity and body schema of the animal. In addition, we agree that future studies are needed to examine the dynamics of the abstraction/representationalization of affordance, probably by investigating the evolvement of affordance representation during ongoing actual interactions with novel objects or manipulated motor capability. These points are now addressed in the revision:

(p 17, ln 380) “Therefore, this finding suggests that the affordance boundary is cognitively penetrable, arguing against the directness of affordance perception (e.g., Gibson, 1979; Greeno, 1994; Prindle et al., 1980) or the exclusive sensorimotor origin of affordances (e.g., Gallagher, 2017; Thompson, 2010; Hutto & Myin, 2012; Chemero, 2013). Further, this finding that the boundary adapted to manipulation on body schema suggests that the abstraction/representationalization may be dynamically updated in response to the current motor capacity and body schema of the agent, suggesting that the affordance-based process is probably determined dynamically by the nature of the agent-object dyads, rather than being a fixed belief about objects. Future studies could explore the dynamics of affordance representationalization, probably by investigating how affordance representations evolve during active interactions with novel objects or under conditions of altered motor capabilities. Finally, our findings also suggest that disembodied conceptual knowledge pertinent to action likely modulates affordance perception.”

Reviewer #2 (Recommendations For The Authors):

a) As described, I think the authors could improve their discussion of the LLM work and consider more deeply possible different interpretations of their findings with those models. Are they really providing an independent data point about how objects may be represented, or instead is this a different, indirect way of asking humans the same questions (given the way in which these models are trained)?

Ra: Please see R1.

b) Some of the decisions behind the design of the fMRI experiment, and some of the logic of its interpretation, could be made clearer. Why those four objects per se? What kinds of confounds, such as familiarity, or the range of possible relevant actions per object, might need to be considered? Is there the possibility that relative performance on the in-scanner behavioural task may be in part responsible for the findings? Why were those specific regions of interest chosen and not others? The authors find that the dorsal and ventral regions make a univariate distinction between congruent and incongruent trials, but only for human-scale objects, but it was not clear from the framework that the authors adopted why that distinction should go in that direction (e.g. congruent > incongruent) nor why there shouldn't also be a distinction for the "beyond" objects? Finally, might some of these brain questions better be approached with an RSA or similar approach, as that would seem to better map onto the behavioural studies?

Rb: We thank the reviewer for the detailed suggestions.

Regarding the fMRI study, we have provided further justification on its rationale in the revised manuscript:

(p 11, ln 231) “The distinct categories of reported affordances demarcated by the boundary imply that the objects on either side of the boundary may be represented differently in the brain. We thus speculated that the observed behavioral discontinuity is likely underpinned by distinct neural activities, which give rise to these discrete ‘representations’ separated by the boundary.”

The objects used in the fMRI study were selected by taking into account the objective of the fMRI study, which was to provide the neural basis for the affordance discontinuity found in behaviour experiments. In other words, the fMRI study is not an exploratory experiment, but a validation experiment. To this end, we deliberately selected a small range of common objects to ensure that participants were sufficiently familiar with them, as confirmed through their oral reports. Furthermore, to ensure a fair comparison between the two categories of objects in terms of action possibility range, we predetermined an equal number of congruent and incongruent actions for each category. This arrangement was intended to eliminate any bias that might arise from different amount of action choices associated with each category. Therefore, the present object and action sets in the fMRI study, which were based on the behavior experiments, are sufficient for its purpose.

Regarding the possibility that the performance of the in-scanner behavioural task may be in part responsible for the findings, we analysed participants’ performance. Not surprisingly, participants demonstrated high consistency and accuracy in their responses:

𝑀𝑒𝑎𝑛𝐶𝑜𝑛𝑔𝑟𝑢𝑒𝑛𝑡_𝑂𝑏𝑗𝑒𝑐𝑡𝑊𝑖𝑡ℎ𝑖𝑛 = 0.991, SD = 0.018;

𝑀𝑒𝑎𝑛𝐼𝑛𝑐𝑜𝑛𝑔𝑟𝑢𝑒𝑛𝑡_𝑂𝑏𝑗𝑒𝑐𝑡𝑊𝑖𝑡ℎ𝑖𝑛 = 0.996, SD = 0.007;

𝑀𝑒𝑎𝑛𝐶𝑜𝑛𝑔𝑟𝑢𝑒𝑛𝑡_𝑂𝑏𝑗𝑒𝑐𝑡𝐵𝑒𝑦𝑜𝑛𝑑 = 0.996, SD = 0.004;

𝑀𝑒𝑎𝑛𝐼𝑛𝑐𝑜𝑛𝑔𝑟𝑢𝑒𝑛𝑡𝑂𝑏𝑗𝑒𝑐𝑡𝐵𝑒𝑦𝑜𝑛𝑑 = 0.998, SD = 0.002

in all conditions, suggesting constant active engagement with the task. Thus, the inscanner behaviour unlikely resulted in the lack of congruency effect for the ‘beyond’ objects observed in the brain.

Regarding the selection of ROIs, our decision to focus on these specific sensory and motor regions was based on existing literature highlighting their distinct contribution to affordance perception (Borghi, 2005; Sakreida et al., 2016). The pFs was chosen for its role in object identification and classification, while the SPL was chosen for its involvement in object manipulation. Additionally, the primary motor cortex (M1) is known to be engaged in affordance processing (e.g., McDannald et al., 2018), which was included to investigate the affordance congruency effect during the motor execution stage of the sense-think-act pathway. These considerations are detailed in the revised manuscript:

(p 14, ln 280) “In addition to the pFs and SPL, we also examined the congruency effect in the lateral occipital cortex (LO), which is involved in object representation (e.g., Grill-Spector et al., 2000; Konkle & Caramazza, 2013) and provides inputs to both the pFs and SPL (Hebart et al., 2018). Meanwhile, the primary motor cortex (M1), which receives inputs from the dorsal stream (Vainio & Ellis, 2020), is involved in affordance processing (e.g., McDannald et al., 2018) and action executions (Binkofski et al., 2002).”

(p 29, ln 684) “We chose the pFs, LO, SPL, and M1 as ROIs based on existing literature highlighting their distinct contributions to affordance perception (Borghi, 2005; Sakreida et al., 2016).”

Regarding the congruency effect, in our study, we followed the established fMRI research paradigm of employing the congruent effect as a measure of affordance processing (e.g., Kourtis et al., 2018), and the rationale behind the directionality of the distinction in our framework (congruent > incongruent) is grounded in the concept of affordance, in which the mere perception of a graspable object facilitates motor responses that are congruent with certain qualities of the object (e.g., Ellis & Tucker, 2000). From the interaction of congruency by object type, we observed only congruency effect for objects within rather than objects beyond. We speculate that the objects beyond the affordance boundary is generally beyond the motor capacities of the very animal, being too large for the animal to manipulate, thus no congruency effect was found. We have added these clarifications in the revised manuscript:

(p 11, ln 244) “The congruency effect, derived from the contrast of Congruent versus Incongruent conditions, is a well-established measure of affordance processing (e.g., Kourtis et al., 2018).”

(p 16, ln 340) “In contrast, objects larger than that range typically surpass the animal’s motor capabilities, rendering them too cumbersome for effective manipulation. Consequently, these larger objects are less likely to be considered as typical targets for manipulation by the animal, as opposed to the smaller objects. That is, they are perceived not as the “objects” in the animal’s eye, but as part of the background environment, due to their impracticality for direct interactions.”

Regarding the RSA analysis, we agree with the reviewer that RSA may offer a more direct comparison with similarities among objects. However, our primary objective in this fMRI study was to explore the neural basis of the affordance boundary observed in the behavioural study, rather than explaining the similarities in neural responses between different objects. For this reason, we did not conduct RSA analysis.

c) Page 4 Re statistical evaluation of the discontinuity in judgments, the authors might consider a Bayesian approach, which would be stronger than using "all ps > 0.05" to argue that within-boundary similarities are consistent and high.

Rc: We thank the reviewer for the suggestion on the Bayesian approach for significance tests, which has been now added in the revised manuscript:

In the results (p 4, ln 105) “This trough suggested an affordance boundary between size rank 4 and 5, while affordance similarities between neighboring ranks remained high (rs > 0.45) and did not significantly differ from each other (ps > 0.05, all 𝐵𝐹10 < 10) on either side of the boundary (Fig. 1d, left panel, green lines).”

In the methods (p 25, ln 597) “Pearson and Filon’s (1898) Z, implemented in R package “cocor” (Diedenhofen & Musch, 2015) was used to evaluate the significance of these similarities (alpha level = .05, one-tail test). For significance tests, Bayesian statistical analyses were conducted using the web version of the “bayesplay” R package (Colling, 2021). Specifically, the data (likelihood) model was specified as a normal distribution, where the correlation coefficients were transformed to Fisher’s z. The null hypothesis was specified as a standard normal distribution centred at zero. Conversely, the alternative hypothesis was specified as a normal distribution centred at 2. Bayes factors (BF10) were calculated and interpreted using the classification scheme suggested by Wagenmakers et al. (2011), wherein a Bayes factor greater than 10 is considered strong evidence for accepting H1 over H0.”

d) Page 4 One question I had about the big objects is whether their internal similarity and dissimilarity to smaller objects, might largely arise if most of the answers about actions for those larger objects are just "no"? This depends on the set of possible actions that were considered: the authors chose 14 from a previous study but did not describe these further or consider possible strengths/limitations of this selection. This is a very important point that needs addressing - to what extent are these findings "fragile" in that they relate only to that specific selection of 14 action kinds?

Rd: The action judgements for objects beyond body size were not mostly “no”; in fact, there was no significant difference between average action possibilities related to objects beyond (25%) and within (26%). Rather, the dissimilarity between objects within and those beyond likely arose from the difference in most-plausible action set they related. For example, the top three actions related to objects within are “grasp”, “hold” and “throw”, while those related to objects beyond are “sit”, “lift” and “stand”, as stated in our original manuscript: “A further analysis on the affordances separated by the boundary revealed that objects within human body size range were primarily subjected to hand-related actions such as grasping, holding and throwing. These affordances typically involve object manipulation with humans’ effectors. In contrast, objects beyond the size range of human body predominantly afforded actions such as sitting and standing, which typically require locomotion or posture change of the whole body around or within the objects (p 11 ln 229)”.

Regarding the validity of action selection, the selection of the objects and affordances in this study was guided by two key criteria. First, the objects were selected from the dataset published in Konkle and Oliva's study (2011), which systematically investigates the effect of object size on object recognition. Therefore, the range of object sizes, from 14 cm to 7,618 cm, is well-calibrated and represents a typical array of object sizes found in the real world. Second, the actions were selected to cover a wide range of daily humans-objects/environments interactions, from singlepoint movements (e.g., hand, foot) to whole-body movements (e.g., lying, standing), based on the kinetics human action video dataset (Kay et al., 2017). Thus, this set of objects and actions is a sufficiently representative of typic human experiences. In revision, we have clarified these two criteria in the methods section:

(p 22, ln 517) “The full list of objects, their diagonal size, and size rankings were provided in Supplementary Table S6. The objects were selected from the dataset in Konkle and Oliva’s study (2011) to cover typic object sizes in the world (ranging from 14 cm to 7,618 cm), and actions related to these objects were selected to span a spectrum of daily humans-objects/environments interactions, from single-point movements (e.g., hand, foot) to whole-body movements (e.g., lying, standing), based on the Kinetics Human Action Video Dataset (Kay et al., 2017).”

Having said this, we agree with reviewer that a larger set of objects and actions will facilitate finer localization of the representational discontinuity, which can be addressed in future studies

(p 16, ln 344): “…, due to their impracticality for direct interactions. Future studies should incorporate a broader range of objects and a more comprehensive set of affordances for finer delineation of the representational discontinuity between objects and the environment.”

e) Page 12 "no region showed the congruency effect for objects beyond the body size" in a whole brain analysis. What about a similar analysis for the humanscale objects? We must also keep in mind that with N=12 there may be relatively little power to detect such effects at the random-effects level, so this null finding may not be very informative.

Re: We thank the reviewer for this advice. The whole brain analysis on the congruency effect for human-scale objects (objects within) has now been included in the supplementary materials (please see Author response figure 1d (New Supplementary Fig. S4d) and Author response table 1 (New Supplementary Table S5) below).

Author response image 1.

Significant brain activations of different contrasts in the whole-brain level analysis. a, the effect of object type, positive values (warm color) indicated higher activation for objects within than objects beyond and negative values (cold color) indicated the opposite. b, the effect of congruency, positive values indicated higher activation in congruent than incongruent condition. c, the effect of interaction between object type and congruency, positive values indicated the larger congruency effect for objects within than beyond. d, the congruency effect for objects within. All contrasts were corrected with cluster-level correction at p < .05. The detailed cluster-level results for each contrast map can be found in Supplementary Table S2 to S5.

Author response table 1.

Cortical regions showing significant congruency effect (congruent versus incongruent) for objects within, whole-brain analysis (R = right hemisphere, L = left hemisphere; Z > 2.3, p = 0.05, cluster corrected)

Regarding the power of the fMRI study, we would like to clarify that, the critical test of this fMRI study is the two-way interaction of congruency effect by object size instead of the (null) congruency effect for the object beyond. Having said this, we agree that the sample size is small which might lead to lack of power in the fMRI study. In the revision we have now acknowledged this issue explicitly:

(p 16, ln 354) “…supporting the idea that affordance is typically represented only for objects within the body size range. While it is acknowledged that the sample size of the fMRI study was small (12 participants), necessitating cautious interpretation of its results, the observed neural-level affordance discontinuity is notable. That is, qualitative differences in neural activity between objects within the affordance boundary and those beyond replicated our behavior findings. This convergent evidence reinforced our claim that objects were discretized into two broad categories along the continuous size axis, with affordance only being manifested for objects within the boundary.”

f) Page 14 [the fMRI findings] "suggest that affordance perception likely requires perceptual processing and is not necessarily reflected in motor execution". This seems a large leap to make from a relatively basic experiment that tests only a small set of (arbitrarily chosen) objects and actions. It's important to keep in mind too that none of the studies here actually asked participants to interact with objects; that objects were shown as 2D images; and that the differences between real-world sizes of objects were greatly condensed by the way they are scaled for presentation on a computer screen (and such scaling is probably greater for the larger-than-human objects).

Rf: The action-congruency judgement task is widely used in the studies of affordance processing (e.g., Kourtis et al., 2018; Peelen & Caramazza, 2012), so does the practice of not including actual interaction with the objects and using 2D instead of 3D objects (e.g., Peelen & Caramazza, 2012; Matić et al., 2020). However, we are aware that alternative practice exists in the field and we agree that it would be interesting for future studies to test whether actual interactions and 3D objects presentation may bring any change on the affordance boundary observed in our study.

Our inference “affordance perception likely requires perceptual processing and is not necessarily reflected in motor execution” was based on the fMRI finding that the congruency effect only in cortical regions proposedly engaged in perceptual processing, but not in the M1 which is associated with motor execution. This significant two-way interaction pointed to a possibility that affordance processing may not necessarily manifest in motor execution.

We acknowledge the scaling issue inherent in all laboratory experiments, but we doubt that it significantly influenced our results. In fact, it is a common practice in studies on object size to present objects of different physical sizes as constantly sized images on a screen (e.g., Konkle & Oliva, 2012; Huang et al., 2022). Moreover, scaling does not change the smoothness of object sizes, whereas the affordance boundary represents a singularity point that disrupts this smoothness. Finally, regarding the limited variety of objects and actions, please see Rd.

g) Page 15 Why are larger objects "less interesting"? They have important implications for navigation, for example?

Rg: We are sorry for the confusion. Our intention was to express that objects beyond the affordance boundary are generally beyond motor capacities of the animal in question. As such, compared to smaller objects within the environment, these larger objects may not typically be considered as potential targets for manipulation. We have now corrected the wording in the revised text:

(p 16, ln 340) “In contrast, objects larger than that range typically surpass the animal’s motor capabilities, rendering them too cumbersome for effective manipulation. Consequently, these larger objects are less likely to be considered as typical targets for manipulation by the animal, as opposed to smaller objects in the environment. That is, they are perceived not as the “objects” in the animal’s eye, but as part of the background environment, due to their impracticality for direct interactions.”

h) Page 15 At several places I wondered whether the authors were arguing against a straw man. E.g. "existing psychological studies...define objects in a disembodied manner..." but no citations are given on this point, nor do the authors describe previous theoretical positions that would make a strong counter-claim to the one advocated here.

Rh: We are sorry for not presenting our argument clearly. Previous studies often define the object space based on object features alone, such as absolute size or function, without reference to the knowledge and the abilities of the agent (e.g., de Beeck et al., 2008; Konkle & Oliva, 2011). This perspective overlooks the importance of the features of the animal-object pairs. Gibson (1979) highlighted that an object’s affordance, which includes all action possibilities it offers to an animal, is determined by the object’s size relative to the animal’s size, rather than its real-world size. Under this embodied view, we argue that the object space is better defined by the features of the agent-object system, and this is the primary assumption and motivation of the present study. We have now clarified this point and added the references in the revision:

(p 2, ln 35) “A contemporary interpretation of this statement is the embodied theory of cognition (e.g., Chemero, 2013; Gallagher, 2017; Gibbs, 2005; Wilson, 2002; Varela et al., 2017), which, diverging from the belief that size and shape are inherent object features (e.g., de Beeck et al., 2008; Konkle & Oliva, 2011), posits that human body scale (e.g., size) constrains the perception of objects and the generation of motor responses.”

(p 17, ln 365) “Existing psychological studies, especially in the field of vision, define objects in a disembodied manner, primarily relying on their physical properties such as shape (e.g., de Beeck et al., 2008) and absolute size (e.g., Konkle & Oliva, 2011).”

Reviewer #3 (Public Review):

(1) Even after several readings, it is not entirely clear to me what the authors are proposing and to what extent the conducted work actually speaks to this. In the introduction, the authors write that they seek to test if body size serves not merely as a reference for object manipulation but also "plays a pivotal role in shaping the representation of objects." This motivation seems rather vague motivation and it is not clear to me how it could be falsified.

Similarly, in the discussion, the authors write that large objects do not receive "proper affordance representation," and are "not the range of objects with which the animal is intrinsically inclined to interact, but probably considered a less interesting component of the environment." This statement seems similarly vague and completely beyond the collected data, which did not assess object discriminability or motivational values.

Overall, the lack of theoretical precision makes it difficult to judge the appropriateness of the approaches and the persuasiveness of the obtained results. This is partly due to the fact that the authors do not spell out all of their theoretical assumptions in the introduction but insert new "speculations" to motivate the corresponding parts of the results section. I would strongly suggest clarifying the theoretical rationale and explaining in more detail how the chosen experiments allow them to test falsifiable predictions.

R1: We are sorry for the confusion about the theoretical motivation and rationale. Our motivation is on the long-lasting debate regarding the representation versus direct perception of affordance. That is, we tested whether object affordance would simply covary with its continuous constraints such as object size, in line with the representation-free view, or, whether affordance would be ‘representationalized’, in line with the representation-based view, under the constrain of body size. In revision, we have clarified the motivation and its relation to our approach:

In the introduction (p 2, ln 45): “However, the question of how object perception is influenced by the relative size of objects in relation to the human body remains open. Specifically, it is unclear whether this relative size simply acts as a continuous variable for locomotion reference, or if it affects differentiating and organizing object representations based on their ensued affordances.”

In the discussion (p 14, ln 295): “One long-lasting debate on affordance centers on the distinction between representational and direct perception of affordance. An outstanding theme shared by many embodied theories of cognition is the replacement hypothesis (e.g., Van Gelder, 1998), which challenges the necessity of representation as posited by computationalism’s cognitive theories (e.g., Fodor, 1975). This hypothesis suggests that input is discretized/categorized and subjected to abstraction or symbolization, creating discrete stand-ins for the input (e.g., representations/states). Such representationalization would lead to a categorization between the affordable (the objects) and those beyond affordance (the environment). Accordingly, computational theories propose the emergence of affordance perception, in contrast to the perspective offered by embodied theories. The present study probed this ‘representationalization’ of affordance by examining whether affordance perception introduces discontinuity and qualitative dissociation in response to continuous action-related physical features (such as object size relative to the agents), which allows sensorimotor input to be assigned into discrete states/kinds, in line with the representation-based view under the constraints of body size. Alternatively, it assessed whether activity directly mirrors the input, free from discretization/categorization/abstraction, in line with the representation-free view.

First, our study found evidence demonstrating discretization in affordance perception. Then, through the body imagination experiment, we provided causal evidence suggesting that this discretization originates from sensorimotor interactions with objects rather than amodal sources, such as abstract object concepts independent of agent motor capability. Finally, we demonstrated the supramodality of this embodied discontinuity by leveraging the recent advances in AI. We showed that the discretization in affordance perception is supramodally accessible to disembodied agents such as large language models (LLMs), which lack sensorimotor input but can access linguistic materials built upon discretized representations. These results collectively suggest that sensorimotor input undergoes discretization, as implied in the computationalism’s idea of representation. Note that, these results are not contradictory to the claim of the embodied theories, as these representations do shape processes beyond the sensorimotor domain but after discretization.

The observed boundary in affordance perception extends the understanding of the discontinuity in perception in response to the continuity of physical inputs (Harnad, 1987; Young et al., 1997).”

We are also sorry for the confusion about the expression “proper affordance representation”. We intended to express that the neural responses to objects beyond the boundary in the whole brain failed to reflect affordance congruency, and therefore did not show evidence of affordance processing. We have clarified this expression in the revised manuscript:

(p 12, ln 265) “Taken together, the affordance boundary not only separated the objects into two categories based on their relative size to human body, but also delineated the range of objects that evoked neural representations associated with affordance processing.”

Finally, we agree with the reviewer that the expressions, such as “not…inclined to interact” and “probably considered a less interesting component of the environment”, may be misleading. Rather, we intended to express that the objects beyond the affordance boundary is generally beyond the motor capacities of the very animal, being too large for the very animal to manipulated, as comparing to the smaller objects in the environment, may not be a typical target object for manipulation for the animal. We have revised these expressions in the manuscript and clarified their speculative nature:

(p 16, ln 340) “In contrast, objects larger than that range typically surpass the animal’s motor capabilities, rendering them too cumbersome for effective manipulation. Consequently, these larger objects are less likely to be considered as typical targets for manipulation by the animal, as opposed to the smaller objects. That is, they are perceived not as the “objects” in the animal’s eye, but as part of the background environment, due to their impracticality for direct interactions.”

(2) The authors used only a very small set of objects and affordances in their study and they do not describe in sufficient detail how these stimuli were selected. This renders the results rather exploratory and clearly limits their potential to discover general principles of human perception. Much larger sets of objects and affordances and explicit data-driven approaches for their selection would provide a far more convincing approach and allow the authors to rule out that their results are just a consequence of the selected set of objects and actions.

R2: The selection of the objects and affordances in this study was guided by two key criteria. First, the objects were selected from the dataset published in Konkle and Oliva's study (2011), which systematically investigates the effect of object size on object recognition. Therefore, the range of object sizes, from 14 cm to 7,618 cm, is well-calibrated and represents a typical array of object sizes found in the real world. Second, the actions were selected to cover a wide range of daily humans objects/environments interactions, from single-point movements (e.g., hand, foot) to whole-body movements (e.g., lying, standing), based on the kinetics human action video dataset (Kay et al., 2017). Thus, this set of objects and actions is a sufficiently representative of typic human experiences. In revision, we have clarified these two criteria in the methods section:

(p 22, ln 517) “The full list of objects, their diagonal sizes, and size rankings were provided in Supplementary Table S6. The objects were selected from the dataset in Konkle and Oliva’s study (2011) to cover typic object sizes in the world (ranging from 14 cm to 7,618 cm), and actions related to these objects were selected to span a spectrum of daily humans-objects/environments interactions, from single-point movements (e.g., hand, foot) to whole-body movements (e.g., lying, standing), based on the Kinetics Human Action Video Dataset (Kay et al., 2017).”

Having said this, we agree with reviewer that a larger set of objects and actions will facilitate finer localization of the representational discontinuity, which can be addressed in future studies

(p 16, ln 344): “…, due to their impracticality for direct interactions. Future studies should incorporate a broader range of objects and a more comprehensive set of affordances for finer delineation of the representational discontinuity between objects and the environment.”

(3) Relatedly, the authors could be more thorough in ruling out potential alternative explanations. Object size likely correlates with other variables that could shape human similarity judgments and the estimated boundary is quite broad (depending on the method, either between 80 and 150 cm or between 105 to 130 cm). More precise estimates of the boundary and more rigorous tests of alternative explanations would add a lot to strengthen the authors' interpretation.

R3: We agree with the reviewer that correlation analyses alone cannot rule out alternative explanations, as any variable co-varying with object sizes might also affect affordance perception. Therefore, our study experimentally manipulated the imagined body sizes, while keeping other variable constant across conditions. This approach provided evidence of a causal connection between body size and affordance perception, effectively ruling out alternative explanations. In revision, the rationale of experimentally manipulation of imagined body sizes has been clarified

(p 7, ln 152): “One may argue that the location of the affordance boundary coincidentally fell within the range of human body size, rather than being directly influenced by it. To rule out this possibility, we directly manipulated participants’ body schema, referring to an experiential and dynamic functioning of the living body within its environment (Merleau-Ponty & Smith, 1962). This allowed us to examine whether the affordance boundary would shift in response to changes in the imagined body size. This experimental approach was able to establish a causal link between body size and affordance boundary, as other potential factors remained constant. Specifically, we instructed a new group of participants to imagine themselves as small as a cat (typical diagonal size: 77cm, size rank 4, referred to as the “cat condition”), and another new group to envision themselves as large as an elephant (typical diagonal size: 577 cm, size rank 7, referred to as the “elephant condition”) throughout the task (Fig. 2a).”

Meanwhile, with correlational analysis, precise location of the boundary cannot help ruling out alternative explanation. However, we agree that future studies are needed to incorporate a broader range of objects and a more comprehensive set of affordances. For details, please see R2.

(4) Even though the division of the set of objects into two homogenous clusters appears defensible, based on visual inspection of the results, the authors should consider using more formal analysis to justify their interpretation of the data. A variety of metrics exist for cluster analysis (e.g., variation of information, silhouette values) and solutions are typically justified by convergent evidence across different metrics. I would recommend the authors consider using a more formal approach to their cluster definition using some of those metrics.

R4: We thank the reviewer for the suggestion. We performed three analyses on this point, all of which consistently indicated the division of objects into two distinct groups along the object size axis.

First, a hierarchical clustering analysis of the heatmaps revealed a two-maincluster structure, which is now detailed in the revised methods section (p 25, ln 589) “A hierarchical clustering analysis was performed, employing the seaborn clustermap method with Euclidean distance and Complete linkage (Waskom, 2021).”

Second, the similarity in affordances between neighbouring size ranks revealed the same two-main-cluster structure. In this analysis, each object was assigned a realworld size rank, and then Pearson’s correlation was calculated as the affordance similarity index for each pair of neighbouring size ranks to assess how similar the perceived affordances were between these ranks. Our results showed a clear trough in affordance similarity, with the lowest point approaching zero, while affordance similarities between neighbouring ranks on either side of the boundary remained high, confirming the observation that objects formed two groups based on affordance similarity.

Finally, we analysed silhouette values for this clustering analysis, where 𝑎𝑖 represents the mean intra-cluster distance, and 𝑏𝑖 represents the mean nearest-cluster distance for each data point i. The silhouette coefficient is calculated as (Rousseeuw, 1987):

The silhouette analysis revealed that the maximum silhouette value coefficient corresponded to a cluster number of two, further confirming the two-cluster structure (please see Author response table 2 below).

Author response table 2.

The silhouette values of a k-means clustering when k (number of clusters) = 2 to 10

(5) While I appreciate the manipulation of imagined body size, as a way to solidify the link between body size and affordance perception, I find it unfortunate that this is implemented in a between-subjects design, as this clearly leaves open the possibility of pre-existing differences between groups. I certainly disagree with the authors' statement that their findings suggest "a causal link between body size and affordance perception."

R5: The between-subjects design in the imagination experiment was employed to prevent contamination between conditions. Specifically, after imagining oneself as a particular size, it can be challenging to immediately transition to envisioning a different body size. In addition, participating sequentially participate in two conditions that only differ in imagined body sizes may lead to undesirable response strategies, such as deliberately altering responses to the same objects in the different conditions. The reason of employing the between-subjects design is now clarified in the revised text (p 7, ln 161): “A between-subject design was adopted to minimize contamination between conditions. This manipulation was effective, as evidenced by the participants’ reported imagined heights in the cat condition being 42 cm (SD = 25.6) and 450 cm (SD = 426.8) in the elephant condition on average, respectively, when debriefed at the end of the task.”

Further, to address the concern that “pre-existing differences between groups” would generate this very result, we adhered to standard protocols such as random assignment of participants to different conditions (cat-size versus elephant-size). Moreover, experimentally manipulating one variable (i.e., body schema) to observe its effect on another variable (i.e., affordance boundary) is the standard method for establishing causal relationships between variables. We could not think of other better ways for this objective.

(6) The use of LLMs in the current study is not clearly motivated and I find it hard to understand what exactly the authors are trying to test through their inclusion. As noted above, I think that the authors should discuss the putative roles of conceptual knowledge, language, and sensorimotor experience already in the introduction to avoid ambiguity about the derived predictions and the chosen methodology. As it currently stands, I find it hard to discern how the presence of perceptual boundaries in LLMs could constitute evidence for affordance-based perception.

R6: The motivation of LLMs is to test the supramodality of this embodied discontinuity found in behavioral experiments: whether this discontinuity is accessible beyond the sensorimotor domain. To do this, we leveraged the recent advance in AI and tested whether the discretization observed in affordance perception is supramodally accessible to disembodied agents which lack access to sensorimotor input but only have access to the linguistic materials built upon discretized representations, such as large language models (LLM). The theoretical motivation and rationale regarding the LLM study are now included in the introduction and discussion:

In the introduction (p 2, ln 59) “…, and the body may serve as a metric that facilitates meaningful engagement with the environment by differentiating objects that are accessible for interactions from those not. Further, grounded cognition theory (see Barsalou, 2008 for a review) suggests that the outputs of such differentiation might transcend sensorimotor processes and integrate into supramodal concepts and language. From this perspective, we proposed two hypotheses...”

In the introduction (p 3, ln 70) “Notably, the affordance boundary varied in response to the imagined body sizes and showed supramodality. It could also be attained solely through language, as evidenced by the large language model (LLM), ChatGPT (OpenAI, 2022).”

For details in the discussion, please see R1.

(7) Along the same lines, the fMRI study also provides very limited evidence to support the authors' claims. The use of congruency effects as a way of probing affordance perception is not well motivated. What exactly can we infer from the fact a region may be more active when an object is paired with an activity that the object doesn't afford? The claim that "only the affordances of objects within the range of body size were represented in the brain" certainly seems far beyond the data.

R7: In our study, we followed the established fMRI research paradigm of employing the congruent effect as a measure of affordance processing (e.g., Kourtis et al., 2018). The choice of this paradigm has now been clarified in the revised manuscript (p 11, ln 244): “The congruency effect, derived from the contrast of Congruent versus Incongruent conditions, is a well-established measure of affordance processing (e.g., Kourtis et al., 2018).”

The statement that “only the affordances of objects within the range of body size were represented in the brain” is based on the observed interaction of congruency by object size. In the revised text, we have weakened this statement to better align with the direct implications of the interaction effect (p 1 ln 22): “A subsequent fMRI experiment revealed evidence of affordance processing exclusively for objects within the body size range, but not for those beyond. This suggests that only objects capable of being manipulated are the objects capable of offering affordance in the eyes of an organism.”

(8) Importantly (related to my comments under 2) above), the very small set of objects and affordances in this experiment heavily complicates any conclusions about object size being the crucial variable determining the occurrence of congruency effects.

R8: The objective of the fMRI study was to provide the neural basis for the affordance discontinuity found in behaviour experiments. In other words, the fMRI study is not an exploratory experiment, and therefore, the present object and action sets, which are based on the behaviour experiments, are sufficient.

(9) I would also suggest providing a more comprehensive illustration of the results (including the effects of CONGRUENCY, OBJECT SIZE, and their interaction at the whole-brain level).

R9: We agree and in revision, we have now included these analyses in the supplementary material (p 30, ln 711): “For the whole-brain analyses on the congruency effect, the object size effect, and their interaction, see Supplementary Fig. S4 and Table S2 to S5.” Please see Author response image 2 (New Supplementary Fig. S4) and Author responses tables 3 to 5 (New Supplementary Table S2 to S4) below.

Author response image 2.

Significant brain activations of different contrasts in the whole-brain level analysis. a, the effect of object type, positive values (warm color) indicated higher activation for objects within than objects beyond and negative values (cold color) indicated the opposite. b, the effect of congruency, positive values indicated higher activation in congruent than incongruent condition. c, the effect of interaction between object type and congruency, positive values indicated the larger congruency effect for objects within than beyond. d, the congruency effect for objects within. All contrasts were corrected with cluster-level correction at p < .05. The detailed cluster-level results for each contrast map can be found in Supplementary Table S2 to S5.

Author response table 3.

Cortical regions reaching significance in the contrasts of (A) objects within versus object beyond and (B) objects beyond versus objects within, whole-brain analysis (R = right hemisphere, L = left hemisphere; Z > 2.3, p = 0.05, cluster corrected).

Author response table 4.

Cortical regions reaching significance in contrasts of (A) congruent versus incongruent and (B) incongruent versus congruent, whole-brain analysis (R = right hemisphere, L = left hemisphere; Z > 2.3, p = 0.05, cluster corrected).

Author response table 5.

Review Table 5 (New Supplementary Table S4). Cortical regions showing significant interaction between object type and congruency, whole-brain analysis (OW = Objects within, OB = Objects beyond; R = right hemisphere, L = left hemisphere; Z > 2.3, p = 0.05, cluster corrected)

Reviewer #3 (Recommendations For The Authors):

a. >a) Clarify all theoretical assumptions already within the introduction and specify how the predictions are tested (and how they could be falsified).

Ra: Please see R1.

b. >b) Explain how the chosen experimental approach relates to the theoretical questions under investigation (e.g., it is not clear to me how affordance similarity ratings can inform inference about which part of the environment is perceived as more or less manipulable).

Rb: We thank the reviewer for the suggestion, and the theoretical motivation and rationale are now clarified. For details, please see R1.

c. >c) Include a much larger set of objects and affordances in the behavioural experiments (that is more generalizable and also permits a more precise estimation of the boundary), and use a more rigorous methodology to justify a particular cluster solution.

Rc: Please see R2 for the limited variance of objects and actions, and R4 for more analyses on the boundary.

d. >d) Clearly motivate what the use of LLMs can contribute to the study of affordance perception.

Rd: Please see R6.

e) Clearly motivate why congruency effects are thought to index "affordance representation in the brain" Re: Please see R7.

e) Include a much larger set of objects and affordances in the fMRI study.

Re: Please see R7.

f) Consider toning down the main conclusions based on the limitations outlined above.

Rf: We have toned down the main conclusions accordingly.

We are profoundly grateful for the insightful comments and suggestions provided by the three reviewers, which have greatly improved the quality of this manuscript.   References

Barsalou, L. W. (1999). Perceptual symbol systems. Behavioral and Brain Sciences, 22(4), 637-660.

de Beeck, H. P. O., Torfs, K., & Wagemans, J. (2008). Perceived shape similarity among unfamiliar objects and the organization of the human object vision pathway. Journal of Neuroscience, 28(40), 10111-10123.

Borghi, A. M. (2005). Object concepts and action. Grounding cognition: The role of perception and action in memory, language, and thinking, 8-34.

Colling, L.J. (2021). ljcolling/go-bayesfactor: (Version v0.9.0).Zenodo. doi: 10.5281/zenodo.4642331

Crawley, J. A. H., Mumby, H. S., Chapman, S. N., Lahdenperä, M., Mar, K. U., Htut, W., ... & Lummaa, V. (2017). Is bigger better? The relationship between size and reproduction in female Asian elephants. Journal of Evolutionary Biology, 30(10), 1836-1845.

Ellis, R., & Tucker, M. (2000). Micro‐affordance: The potentiation of components of action by seen objects. British Journal of Psychology, 91(4), 451-471.

Fan, L., Li, H., Zhuo, J., Zhang, Y., Wang, J., Chen, L., ... & Jiang, T. (2016). The human brainnetome atlas: a new brain atlas based on connectional architecture. Cerebral Cortex, 26(8), 3508-3526.

Fodor, J. A. (1975). The Language of Thought (Vol. 5). Harvard University Press.

Gibson, J. J. (1979). The ecological approach to visual perception: Classic edition.

Hertrich, I., Dietrich, S., & Ackermann, H. (2016). The role of the supplementary motor area for speech and language processing. Neuroscience & Biobehavioral Reviews, 68, 602-610.

Huang, T., Song, Y., & Liu, J. (2022). Real-world size of objects serves as an axis of object space. Communications Biology, 5(1), 1-12.

Kantak, S. S., Stinear, J. W., Buch, E. R., & Cohen, L. G. (2012). Rewiring the brain: potential role of the premotor cortex in motor control, learning, and recovery of function following brain injury. Neurorehabilitation and Neural Repair, 26(3), 282-292.

Kay, W., Carreira, J., Simonyan, K., Zhang, B., Hillier, C., Vijayanarasimhan, S., ... & Zisserman, A. (2017). The kinetics human action video dataset. arXiv preprint arXiv:1705.06950.

Konkle, T., & Oliva, A. (2011). Canonical visual size for real-world objects. Journal of Experimental Psychology: human perception and performance, 37(1), 23.

Kourtis, D., Vandemaele, P., & Vingerhoets, G. (2018). Concurrent cortical representations of function-and size-related object affordances: an fMRI study. Cognitive, Affective, & Behavioral Neuroscience, 18, 1221-1232.

Matić, K., de Beeck, H. O., & Bracci, S. (2020). It's not all about looks: The role of object shape in parietal representations of manual tools. Cortex, 133, 358-370.

McDannald, D. W., Mansour, M., Rydalch, G., & Bolton, D. A. (2018). Motor affordance for grasping a safety handle. Neuroscience Letters, 683, 131-137.

NCD Risk Factor Collaboration (NCD-RisC). (2016). A century of trends in adult human height. Elife, 5, e13410.

Peelen, M. V., & Caramazza, A. (2012). Conceptual object representations in human anterior temporal cortex. Journal of Neuroscience, 32(45), 15728-15736.

Rousseeuw, P. J. (1987). Silhouettes: a graphical aid to the interpretation and validation of cluster analysis. Journal of Computational and Applied Mathematics, 20, 53-65.

Sakreida, K., Effnert, I., Thill, S., Menz, M. M., Jirak, D., Eickhoff, C. R., ... & Binkofski, F. (2016). Affordance processing in segregated parieto-frontal dorsal stream sub-pathways. Neuroscience & Biobehavioral Reviews, 69, 89-112.

Van Gelder, T. (1998). The dynamical hypothesis in cognitive science. Behavioral and Brain Sciences, 21(5), 615-628.

Wagenmakers, E.-J., Wetzels, R., Borsboom, D. & van der Maas, H. L. J. Why psychologists must change the way they analyze their data: the case of psi: Comment on Bem (2011). Journal of Personality and Social Psychology, 100(3), 426–432.

Zhen, Z., Yang, Z., Huang, L., Kong, X. Z., Wang, X., Dang, X., ... & Liu, J. (2015). Quantifying interindividual variability and asymmetry of face-selective regions: a probabilistic functional atlas. NeuroImage, 113, 13-25.

Author Response

The following is the authors’ response to the original reviews.

We sincerely thank the reviewers for their in-depth consideration of our manuscript and their helpful reviews. Their efforts have made the paper much better. We have responded to each point. The previously provided public responses have been updated they are included after the private response for convenience.

Reviewer #1 (Recommendations For The Authors):

1. In general, the manuscript will benefit from copy editing and proof reading. Some obvious edits;

2. Page 6 line 140. Do the authors mean Cholera toxin B?

Response: We corrected this error and went through the entire paper carefully correcting for grammar and increased clarity.

• Page 8 line 173. Methylbetacyclodextrin is misspelled.

Response: Yes, corrected.

• Figure 4c is missing representative traces for electrophysiology data.

• Figure 4. Please check labeling ordering in figure legend as it does not match the panels in the figure.

Thank you for the correction and we apologize for the confusion in figure 4. We uploaded an incomplete figure legend, and the old panel ‘e’ was not from an experiment that was still in the figure. It was removed and the figure legends are now corrected.

• Please mention the statistical analysis used in all figure legends.

Response: Thank you for pointing out this omission, statistics have been added.

• Although the schematics in each figure helps guide readers, they are very inconsistent and sometimes confusing. For example, in Figure 5 the gating model is far-reaching without conclusive evidence, whereas in Figure 6 it is over simplified and unclear what the image is truly representing (granted that the downstream signaling mechanism and channel is not known).

Response: Figure 5d is the summary figure for the entire paper. We have made this clearer in the figure legend and we deleted the title above the figure that gave the appearance that the panel relates to swell only. It is the proposed model based on what we show in the paper and what is known about the activation mechanism of TREK-1.

Figure 6 is supposed to be simple. It is to help the reader understand that when PA is low mechanical sensitivity is high. Without the graphic, previous reviewers got confused about threshold going down and mechanosensitivity going up and how the levels of PA relate. Low PA= high sensitivity. We’ve added a downstream effector to the right side of the panel to avoid any biased to a putative downstream channel effector. The purpose of the experiment is to show PLD has a mechanosensitive phenotype in vivo.

Reviewer #2 (Recommendations For The Authors):

This manuscript outlines some really interesting findings demonstrating a mechanism by which mechanically driven alterations in molecular distributions can influence a) the activity of the PLD2 molecule and subsequently b) the activation of TREK-1 when mechanical inputs are applied to a cell or cell membrane.

The results presented here suggest that this redistribution of molecules represents a modulatory mechanism that alters either the amplitude or the sensitivity of TREK-1 mediated currents evoked by membrane stretch. While the authors do present values for the pressure required to activate 50% of channels (P50), the data presented provides incomplete evidence to conclude a shift in threshold of the currents, given that many of the current traces provided in the supplemental material do not saturate within the stimulus range, thus limiting the application of a Boltzmann fit to determine the P50. I suggest adding additional context to enable readers to better assess the limitations of this use of the Boltzmann fit to generate a P50, or alternately repeating the experiments to apply stimuli up to lytic pressures to saturate the mechanically evoked currents, enabling use of the Boltzmann function to fit the data.

Response: We thank the reviewer for pointing this out. We agree the currents did not reach saturation. Hence the term P50 could be misleading, so we have removed it from the paper. We now say “half maximal” current measured from non-saturating pressures of 0-60 mmHg. We also deleted the xPLD data in supplemental figure 3C since there is insufficient current to realistically estimate a half maximal response.

In my opinion, the conclusions presented in this manuscript would be strengthened by an assessment of the amount of TREK-1 in the plasma membrane pre and post application of shear. While the authors do present imaging data in the supplementary materials, these data are insufficiently precise to comment on expression levels in the membrane. To strengthen this conclusion the authors could conduct cell surface biotinylation assays, as a more sensitive and quantitative measure of membrane localisation of the proteins of interest.

1. Response: as mentioned previously, we do not have an antibody to the extracellular domain. Nonetheless to better address this concern we directly compared the levels of TREK-1, PIP2, and GM1; in xPLD2, mPLD2, enPLD2 with and without shear. The results are in supplemental figure 2. PLD2 is known to increase endocytosis1 and xPLD2 is known to block both agonist induced and constitutive endocytosis of µ-opioid receptor2. The receptor is trapped on the surface. This is true of many proteins including Rho3, ARF4, and ACE21 among others. In agreement with this mechanism, in Figure S2C,G we show that TREK increases with xPLD and the localization can clearly be seen at the plasma membrane just like in all of the other publications with xPLD overexpression. xPLD2 would be expected to inhibit the basal current but we presume the increased expression likely has compensated and there is sufficient PA and PG from other sources to allow for the basal current. It is in this state that we then conduct our ephys and monitor with a millisecond time resolution and see no activation. We are deriving conclusion from a very clear response—Figure 1b shows almost no current, even at 1-10 ms after applying pressure. There is little pressure current when we know the channel is present and capable of conducting ion (Figure 1d red bar). After shear there is a strong decrease in TREK-1 currents on the membrane in the presence of xPLD2. But it is not less than TREK-1 expression with mPLD2. And since mouse PLD2 has the highest basal current and pressure activation current. The amount of TREK-1 present is sufficient to conduct large current. To have almost no detective current would require at least a 10 fold reduction compared to mPLD2 levels before we would lack the sensitivity to see a channel open. Lasty endocytosis typically in on the order of seconds to minutes, no milliseconds.

2. We have shown an addition 2 independent ways that TREK-1 is on the membrane during our stretch experiments. Figure 1d shows the current immediately prior to applying pressure for wt TREK-1. When catalytically dead PLD is present (xPLD2) there is almost normal basal current. The channel is clearly present. And then in figure 1a we show within a millisecond there is no pressure current. As a control we added a functionally dead TREK-1 truncation (xTREK). Compared to xPLD2 there is clearly normal basal current. If this is not strong evidence the channel was available on the surface for mechanical activation please help us understand why. And if you think within 2.1 ms 100% of the channel is gone by endocytosis please provide some evidence that this is possible so we can reconsider.

3. We have TIRF super resolution imaging with ~20 nm x-y resolution and ~ 100nm z resolution and Figure 2b clearly shows the channel on the membrane. When we apply pressure in 1b, the channel is present.

4. Lastly, In our previous studies we showed activation of PLD2 by anesthetics was responsible for all of TREK-1’s anesthetic sensitivity and this was through PLD2 binding to the C-terminus of TREK-15. We showed this was the case by transferring anesthetic sensitivity to an anesthetic insensitive homolog TRAAK. This established conclusively the basic premise of our mechanism. Here we show the same C-terminal region and PLD2 are responsible for the mechanical current observed by TREK-1. TRAAK is already mechanosensitive so the same chimera will not work for our purposes here. But anesthetic activation and mechanical activation are dramatically different stimuli, and the fact that the role of PLD is robustly observed in both should be considered.

The authors discuss that the endogenous levels of TREK-1 and PLD2 are "well correlated: in C2C12 cells, that TREK-1 displayed little pair correlation with GM1 and that a "small amount of TREK-1 trafficked to PIP2". As such, these data suggest that the data outlined for HEK293T cells may be hampered by artefacts arising from overexpression. Can TREK-1 currents be activated by membrane stretch in these cells C2C12 cells and are they negatively impacted by the presence of xPLD2? Answering this question would provide more insight into the proposed mechanism of action of PLD2 outlined by the authors in this manuscript. If no differences are noted, the model would be called into question. It could be that there are additional cell-specific factors that further regulate this process.

Response: The low pair correlation of TREK-1 and GM1 in C2C12 cells was due to insufficient levels of cholesterol in the cell membrane to allow for robust domain formation. In Figure 4b we loaded C2C12 cells with cholesterol using the endogenous cholesterol transport protein apoE and serum (an endogenous source of cholesterol). As can be seen in Fig. 4b, the pair correlation dramatically increased (purple line). This was also true in neuronal cells (N2a) (Fig 4d, purple bar). And shear (3 dynes/cm2) caused the TREK-1 that was in the GM1 domains to leave (red bar) reversing the effect of high cholesterol. This demonstrates our proposed mechanism is working as we expect with endogenously expressed proteins.

There are many channels in C2C12 cells, it would be difficult to isolate TREK-1 currents, which is why we replicated the entire system (ephys and dSTORM) in HEK cells. Note, in figure 4c we also show that adding cholesterol inhibits TREK-1 whole cell currents in HEK293cells.

As mentioned in the public review, the behavioural experiments in D. melanogaster can not solely be attributed to a change in threshold. While there may be a change in the threshold to drive a different behaviour, the writing is insufficiently precise to make clear that conclusions cannot be drawn from these experiments regarding the functional underpinnings of this outcome. Are there changes in resting membrane potential in the mutant flys? Alterations in Nav activity? Without controlling for these alternate explanations it is difficult to see what this last piece of data adds to the manuscript, particularly given the lack of TREK-1 in this organism. At the very least, some editing of the text to more clearly indicate that these data can only be used to draw conclusions on the change in threshold for driving the behaviour not the change in threshold of the actual mechanotransduction event (i.e. conversion of the mechanical stimulus into an electrochemical signal).

Response: We agree; features other than PLDs direct mechanosensitivity are likely contributing. This was shown in figure 6g left side. We have an arrow going to ion channel and to other downstream effectors. We’ve added the putative alteration to downstream effectors to the right side of the panel. This should make it clear that we no more speculate the involvement of a channel than any of the other many potential downstream effectors. As mentioned above, the figure helps the reader coordinate low PA with increased mechanosensitivity. Without the graphic reviewers got confused that PA increased the threshold which corresponds to a decreased sensitivity to pain. Nonetheless we removed our conclusion about fly thresholds from the abstract and made clearer in the main text the lack of mechanism downstream of PLD in flies including endocytosis. Supplemental Figure S2H also helps emphasize this. .

Nav channels are interesting, and since PLD contribute to endocytosis and Nav channels are also regulated by endocytosis there is likely a PLD specific effect using Nav channels. There are many ways PA likely regulates mechanosensitive thresholds, but we feel Nav is beyond the scope of our paper. Someone else will need to do those studies. We have amended a paragraph in the conclusion which clearly states we do not know the specific mechanism at work here with the suggestions for future research to discover the role of lipid and lipid-modifying enzymes in mechanosensitive neurons.

There may be fundamental flaws in how the statistics have been conducted. The methods section indicates that all statistical testing was performed with a Student's t-test. A visual scan of many of the data sets in the figures suggests that they are not normally distributed, thus a parametric test such as a Student's t-test is not valid. The authors should assess if each data set is normally distributed, and if not, a non-parametric statistical test should be applied. I recommend assessing the robustness of the statistical analyses and adjusting as necessary.

Response: We thank the reviewer for pointing this out, indeed there is some asymmetry in Figure 6C-d. The p values with Mann Whitney were slightly improved p=0.016 and p=0.0022 for 6c and 6d respectively. For reference, the students t-test had slightly worse statistics p=0.040 and p=0.0023. The score remained the same 1 and 2 stars respectively.

The references provided for the statement regarding cascade activation of the TRPs are incredibly out of date. While it is clear that TRPV4 can be activated by a second messenger cascade downstream of osmotic swelling of cells, TRPV4 has also been shown to be activated by mechanical inputs at the cell-substrate interface, even when the second messenger cascade is inhibited. Recommend updating the references to reflect more current understanding of channel activation.

Response: We thank the reviewer for pointing this out. We have updated the references and changed the comment to “can be” instead of “are”. The reference is more general to multiple ion channel types including KCNQ4. This should avoid any perceived conflict with the cellsubstrate interface mechanism which we very much agree is a correct mechanism for TRP channels.

Minor comments re text editing etc:

The central messages of the manuscript would benefit from extensive work to increase the precision of the writing of the manuscript and the presentation of data in the figures, such textual changes alone would help address a number of the concerns outlined in this review, by clarifying some ambiguities. There are numerous errors throughout, ranging from grammatical issues, ambiguities with definitions, lack of scale bars in images, lack of labels on graph axes, lack of clarity due to the mode of presentation of sample numbers (it would be far more precise to indicate specific numbers for each sample rather than a range, which is ambiguous and confusing), unnecessary and repeat information in the methods section. Below are some examples but this list is not exhaustive.

Response: Thank you, reviewer # 1 also had many of these concerns. We have gone through the entire paper and improved the precision of the writing of the manuscript. We have also added the missing error bar to Figure 6. And axis labels have been added to the inset images. The redundancy in cell culture methods has been removed. Where a range is small and there are lots of values, the exact number of ‘n’ are graphically displayed in the dot plot for each condition.

Text:

I recommend considering how to discuss the various aspects of channel activation. A convention in the field is to use mechanical activation or mechanical gating to describe that process where the mechanical stimulus is directly coupled to the channel gating mechanism. This would be the case for the activation of TREK-1 by membrane stretch alone. The increase in activation by PLD2 activity then reflects a modulation of the mechanical activation of the channel, because the relevant gating stimulus is PA, rather than force/stretch. The sum of these events could be described as shear-evoked or mechanically-evoked, TREK-1 mediated currents (thus making it clear that the mechanical stimulus initiates the relevant cascade, but the gating stimulus may be other than direct mechanical input.) Given the interesting and compelling data offered in this manuscript regarding the sensitisation of TREK-1 dependent mechanicallyevoked currents by PLD2, an increase in the precision of the language would help convey the central message of this work.

Response; We agree there needs to be convention. We have taken the suggestion of mechanically evoked and we suggest the following definitions:

1. Mechanical activation of PLD2: direct force on the lipids releasing PLD2 from nonactivating lipids.

2. Mechanical activation/gating of TREK1: direct force from lipids from either tension or hydrophobic mismatch that opens the channel.

3. Mechanically evoked: a mechanical event that leads to a downstream effect. The effect is mechanically “evoked”.

4. Spatial patterning/biochemistry: nanoscopic changes in the association of a protein with a nanoscopic lipid cluster or compartment.

An example of where discussion of mechanical activation is ambiguous in the text is found at line 109: "channel could be mechanically activated by a movement from GM1 to PIP2 lipids." In this case, the sentence could be suggesting that the movement between lipids provides the mechanical input that activates the channel, which is not what the data suggest.

Response: Were possible we have replaced “movement” with “spatial patterning” and “association” and “dissociation” from specific lipid compartment. This better reflects the data we have in this paper. However, we do think that a movement mechanically activates the channel, GM1 lipids are thick and PIP2 lipids are thin, so movement between the lipids could activate the channel through direct lipid interaction. We will address this aspect in a future paper.

Inconsistencies with usage:

• TREK1 versus TREK-1

Response: corrected to TREK-1

• mPLD2 versus PLD2

Response: where PLD2 represents mouse this has been corrected.

• K758R versus xPLD2

Response: we replaced K758R in the methods with xPLD2.

• HEK293T versus HEK293t Response: we have changed all instances to read HEK293T.

• Drosophila melanogaster and D. melanogaster used inconsistently and in many places incorrectly

Response: we have read all to read the common name Drosophila.

Line 173: misspelled methylbetacyclodextrin

Response corrected

Line 174: degree symbol missing

Response corrected

Line 287: "the decrease in cholesterol likely evolved to further decrease the palmate order in the palmitate binding site"... no evidence, no support for this statement, falsely attributes intention to evolutionary processes .

Response: we have removed the reference to evolution at the request of the reviewer, it is not necessary. But we do wish to note that to our knowledge, all biological function is scientifically attributed to evolution. The fact that cholesterol decreases in response to shear is evidence alone that the cell evolved to do it.

Line 307: grammatical error

Response: the redundant Lipid removed.

Line 319: overinterpreted - how is the mechanosensitivy of GPCRs explained by this translocation?

Response: all G-alpha subunits of the GPCR complex are palmitoylated. We showed PLD (which has the same lipidation) is mechanically activated. If the palmitate site is disrupted for PLD2, then it is likely disrupted for every G-alpha subunit as well.

Line 582: what is the wild type referred to here?

Response: human full length with a GFP tag.

Methods:

• Sincere apologies if I missed something but I do not recall seeing any experiments using purified TREK-1 or flux assays. These details should be removed from the methods section

Response: Removed.

• There is significant duplication of detail across the methods (three separate instances of electrophysiology details) these could definitely be consolidated.

Response: Duplicates removed.

Figures:

• Figure 2- b box doesn't correspond to inset. Bottom panel should provide overview image for the cell that was assessed with shear. In bottom panel, circle outlines an empty space.

Response: We have widened the box slightly to correspond so the non shear box corresponds to the middle panel. We have also added the picture for the whole cell to Fig S2g and outlined the zoom shown in the bottom panel of Fig 2b as requested. The figure is of the top of a cell. We also added the whole cell image of a second sheared cell.

Author response image 1.

• Figure 3 b+c: inset graph lacking axis labels

Response; the inset y axis is the same as the main axis. We added “pair corr. (5nM)” and a description in the figure legend to make this clearer. The purpose of the inset is to show statistical significance at a single point. The contrast has been maximized but without zooming in points can be difficult to see.

• Figure 5: replicate numbers missing and individual data points lacking in panels b + c, no labels of curve in b + c, insets, unclear what (5 nm) refers to in insets.

Response: Thank you for pointing out these errors. The N values have been added. Similar to figure 3, the inset is a bar graph of the pair correlation data at 5 nm. A better explanation of the data has been added to the figure legend.

• Figure 6: no scale bar, no clear membrane localization evident from images presented, panel g offers virtually nothing in terms of insight

Response: We have added scale bars to figure 6b. Figure 6g is intentionally simplistic, we found that correlating decreased threshold with increased pain was confusing. A previous reviewer claimed our data was inconsistent. The graphic avoids this confusion. We also added negative effects of low PA on downstream effects to the right panel. This helps graphically show we don’t know the downstream effects.

Reviewer #3 (Recommendations For The Authors):

Minor suggestions:

1. line 162, change 'heat' to 'temperature'.

Response: changed.

1. in figure 1, it would be helpful to keep the unit for current density consistent among different panels. 1e is a bit confusing: isn't the point of Figure 1 that most of TREK1 activation is not caused by direct force-sensing?

Response: Yes, the point of figure 1 is to show that in a biological membrane over expressed TREK-1 is a downstream effector of PLD2 mechanosensation which is indirect. We agree the figure legend in the previous version of the paper is very confusing.

There is almost no PLD2 independent current in our over expressed system, which is represented by no ions in the conduction pathway of the channel despite there being tension on the membrane.

Purified TREK-1 is only mechanosensitive in a few select lipids, primarily crude Soy PC. It was always assumed that HEK293 and Cos cells had the correct lipids since over expressed TREK-1 responded to mechanical force in these lipids. But that does not appear to be correct, or at least only a small amount of TREK-1 is in the mechanosensitive lipids. Figure 1e graphically shows this. The arrows indicate tension, but the channel isn’t open with xPLD2 present. We added a few sentences to the discussion to further clarify.

Panels c has different units because the area of the tip was measured whereas in d the resistance of the tip was measured. They are different ways for normalizing for small differences in tip size.

1. line 178, ~45 of what?

Response: Cells were fixed for ~30 sec.

1. line 219 should be Figure 4f?

Response: thank you, yes Figure 4f.

Previous public reviews with minor updates.

Reviewer #1 (Public Review):

Force sensing and gating mechanisms of the mechanically activated ion channels is an area of broad interest in the field of mechanotransduction. These channels perform important biological functions by converting mechanical force into electrical signals. To understand their underlying physiological processes, it is important to determine gating mechanisms, especially those mediated by lipids. The authors in this manuscript describe a mechanism for mechanically induced activation of TREK-1 (TWIK-related K+ channel. They propose that force induced disruption of ganglioside (GM1) and cholesterol causes relocation of TREK-1 associated with phospholipase D2 (PLD2) to 4,5-bisphosphate (PIP2) clusters, where PLD2 catalytic activity produces phosphatidic acid that can activate the channel. To test their hypothesis, they use dSTORM to measure TREK-1 and PLD2 colocalization with either GM1 or PIP2. They find that shear stress decreases TREK-1/PLD2 colocalization with GM1 and relocates to cluster with PIP2. These movements are affected by TREK-1 C-terminal or PLD2 mutations suggesting that the interaction is important for channel re-location. The authors then draw a correlation to cholesterol suggesting that TREK-1 movement is cholesterol dependent. It is important to note that this is not the only method of channel activation and that one not involving PLD2 also exists. Overall, the authors conclude that force is sensed by ordered lipids and PLD2 associates with TREK-1 to selectively gate the channel. Although the proposed mechanism is solid, some concerns remain.

1) Most conclusions in the paper heavily depend on the dSTORM data. But the images provided lack resolution. This makes it difficult for the readers to assess the representative images.

Response: The images were provided are at 300 dpi. Perhaps the reviewer is referring to contrast in Figure 2? We are happy to increase the contrast or resolution.

As a side note, we feel the main conclusion of the paper, mechanical activation of TREK-1 through PLD2, depended primarily on the electrophysiology in Figure 1b-c, not the dSTORM. But both complement each other.

2) The experiments in Figure 6 are a bit puzzling. The entire premise of the paper is to establish gating mechanism of TREK-1 mediated by PLD2; however, the motivation behind using flies, which do not express TREK-1 is puzzling.

Response: The fly experiment shows that PLD mechanosensitivity is more evolutionarily conserved than TREK-1 mechanosensitivity. We have added this observation to the paper.

-Figure 6B, the image is too blown out and looks over saturated. Unclear whether the resolution in subcellular localization is obvious or not.

Response: Figure 6B is a confocal image, it is not dSTORM. There is no dSTORM in Figure 6. We have added the error bars to make this more obvious. For reference, only a few cells would fit in the field of view with dSTORM.

-Figure 6C-D, the differences in activity threshold is 1 or less than 1g. Is this physiologically relevant? How does this compare to other conditions in flies that can affect mechanosensitivity, for example?

Response: Yes, 1g is physiologically relevant. It is almost the force needed to wake a fly from sleep (1.2-3.2g). See ref 33. Murphy Nature Pro. 2017.

3) 70mOsm is a high degree of osmotic stress. How confident are the authors that a cell health is maintained under this condition and b. this does indeed induce membrane stretch? For example, does this stimulation activate TREK-1?

Response: Yes, osmotic swell activates TREK1. This was shown in ref 19 (Patel et al 1998). We agree the 70 mOsm is a high degree of stress. This needs to be stated better in the paper.

Reviewer #2 (Public Review):

This manuscript by Petersen and colleagues investigates the mechanistic underpinnings of activation of the ion channel TREK-1 by mechanical inputs (fluid shear or membrane stretch) applied to cells. Using a combination of super-resolution microticopy, pair correlation analysis and electrophysiology, the authors show that the application of shear to a cell can lead to changes in the distribution of TREK-1 and the enzyme PhospholipaseD2 (PLD2), relative to lipid domains defined by either GM1 or PIP2. The activation of TREK-1 by mechanical stimuli was shown to be sensi>zed by the presence of PLD2, but not a catalytically dead xPLD2 mutant. In addition, the activity of PLD2 is increased when the molecule is more associated with PIP2, rather than GM1 defined lipid domains. The presented data do not exclude direct mechanical activation of TREK-1, rather suggest a modulation of TREK-1 activity, increasing sensitivity to mechanical inputs, through an inherent mechanosensitivity of PLD2 activity. The authors additionally claim that PLD2 can regulate transduction thresholds in vivo using Drosophila melanogaster behavioural assays. However, this section of the manuscript overstates the experimental findings, given that it is unclear how the disruption of PLD2 is leading to behavioural changes, given the lack of a TREK-1 homologue in this organism and the lack of supporting data on molecular function in the relevant cells.

Response: We agree, the downstream effectors of PLD2 mechanosensitivity are not known in the fly. Other anionic lipids have been shown to mediate pain see ref 46 and 47. We do not wish to make any claim beyond PLD2 being an in vivo contributor to a fly’s response to mechanical force. We have removed the speculative conclusions about fly thresholds from the abstract.

That said we do believe we have established a molecular function at the cellular level. We showed PLD is robustly mechanically activated in a cultured fly cell line (BG2-c2) Figure 6a of the manuscript. And our previous publication established mechanosensation of PLD (Petersen et. al. Nature Com 2016) through mechanical disruption of the lipids. At a minimum, the experiments show PLDs mechanosensitivity is evolutionarily better conserved across species than TREK1.

This work will be of interest to the growing community of scientists investigating the myriad mechanisms that can tune mechanical sensitivity of cells, providing valuable insight into the role of functional PLD2 in sensi>zing TREK-1 activation in response to mechanical inputs, in some cellular systems.

The authors convincingly demonstrate that, post application of shear, an alteration in the distribution of TREK-1 and mPLD2 (in HEK293T cells) from being correlated with GM1 defined domains (no shear) to increased correlation with PIP2 defined membrane domains (post shear). These data were generated using super-resolution microticopy to visualise, at sub diffraction resolution, the localisation of labelled protein, compared to labelled lipids. The use of super-resolution imaging enabled the authors to visualise changes in cluster association that would not have been achievable with diffraction limited microticopy. However, the conclusion that this change in association reflects TREK-1 leaving one cluster and moving to another overinterprets these data, as the data were generated from sta>c measurements of fixed cells, rather than dynamic measurements capturing molecular movements.

When assessing molecular distribution of endogenous TREK-1 and PLD2, these molecules are described as "well correlated: in C2C12 cells" however it is challenging to assess what "well correlated" means, precisely in this context. This limitation is compounded by the conclusion that TREK-1 displayed little pair correlation with GM1 and the authors describe a "small amount of TREK-1 trafficked to PIP2". As such, these data may suggest that the findings outlined for HEK293T cells may be influenced by artefacts arising from overexpression.

The changes in TREK-1 sensitivity to mechanical activation could also reflect changes in the amount of TREK-1 in the plasma membrane. The authors suggest that the presence of a leak currently accounts for the presence of TREK-1 in the plasma membrane, however they do not account for whether there are significant changes in the membrane localisation of the channel in the presence of mPLD2 versus xPLD2. The supplementary data provide some images of fluorescently labelled TREK-1 in cells, and the authors state that truncating the c-terminus has no effect on expression at the plasma membrane, however these data provide inadequate support for this conclusion. In addition, the data reporting the P50 should be noted with caution, given the lack of saturation of the current in response to the stimulus range.

Response: We thank the reviewer for his/her concern about expression levels. We did test TREK-1 expression. mPLD decreases TREK-1 expression ~two-fold (see Author response image 2 below). We did not include the mPLD data since TREK-1 was mechanically activated with mPLD. For expression to account for the loss of TREK-1 stretch current (Figure 1b), xPLD would need to block surface expression of TREK-1 prior to stretch. The opposite was true, xPLD2 increased TREK-1 expression (see Figure S2c). Furthermore, we tested the leak current of TREK-1 at 0 mV and 0 mmHg of stretch. Basal leak current was no different with xPLD2 compared to endogenous PLD (Figure 1d; red vs grey bars respectively) suggesting TREK-1 is in the membrane and active when xPLD2 is present. If anything, the magnitude of the effect with xPLD would be larger if the expression levels were equal.

Author response image 2.

TREK expression at the plasma membrane. TREK-1 Fluorescence was measured by GFP at points along the plasma membrane. Over expression of mouse PLD2 (mPLD) decrease the amount of full-length TREK-1 (FL TREK) on the surface more than 2-fold compared to endogenously expressed PLD (enPLD) or truncated TREK (TREKtrunc) which is missing the PLD binding site in the C-terminus. Over expression of mPLD had no effect on TREKtrunc.

Finally, by manipulating PLD2 in D. melanogaster, the authors show changes in behaviour when larvae are exposed to either mechanical or electrical inputs. The depletion of PLD2 is concluded to lead to a reduction in activation thresholds and to suggest an in vivo role for PA lipid signaling in setting thresholds for both mechanosensitivity and pain. However, while the data provided demonstrate convincing changes in behaviour and these changes could be explained by changes in transduction thresholds, these data only provide weak support for this specific conclusion. As the authors note, there is no TREK-1 in D. melanogaster, as such the reported findings could be accounted for by other explanations, not least including potential alterations in the activation threshold of Nav channels required for action potential generation. To conclude that the outcomes were in fact mediated by changes in mechanotransduction, the authors would need to demonstrate changes in receptor potential generation, rather than deriving conclusions from changes in behaviour that could arise from alterations in resting membrane potential, receptor potential generation or the activity of the voltage gated channels required for action potential generation.

Response: We are willing to restrict the conclusion about the fly behavior as the reviewers see fit. We have shown PLD is mechanosensitivity in a fly cell line, and when we knock out PLD from a fly, the animal exhibits a mechanosensation phenotype. We tried to make it clear in the figure and in the text that we have no evidence of a particular mechanism downstream of PLD mechanosensation.

This work provides further evidence of the astounding flexibility of mechanical sensing in cells. By outlining how mechanical activation of TREK-1 can be sensitised by mechanical regulation of PLD2 activity, the authors highlight a mechanism by which TREK-1 sensitivity could be regulated under distinct physiological conditions.

Reviewer #3 (Public Review):

The manuscript "Mechanical activation of TWIK-related potassium channel by nanoscopic movement and second messenger signaling" presents a new mechanism for the activation of TREK-1 channel. The mechanism suggests that TREK1 is activated by phosphatidic acids that are produced via a mechanosensitive motion of PLD2 to PIP2-enriched domains. Overall, I found the topic interesting, but several typos and unclarities reduced the readability of the manuscript. Additionally, I have several major concerns on the interpretation of the results. Therefore, the proposed mechanism is not fully supported by the presented data. Lastly, the mechanism is based on several previous studies from the Hansen lab, however, the novelty of the current manuscript is not clearly stated. For example, in the 2nd result section, the authors stated, "fluid shear causes PLD2 to move from cholesterol dependent GM1 clusters to PIP2 clusters and this activated the enzyme". However, this is also presented as a new finding in section 3 "Mechanism of PLD2 activation by shear."

For PLD2 dependent TREK-1 activation. Overall, I found the results compelling. However, two key results are missing.

1. Does HEK cells have endogenous PLD2? If so, it's hard to claim that the authors can measure PLD2-independent TREK1 activation.

Response: yes, there is endogenous PLD (enPLD). We calculated the relative expression of xPLD2 vs enPLD. xPLD2 is >10x more abundant (Fig. S3d of Pavel et al PNAS 2020, ref 14 of the current manuscript). Hence, as with anesthetic sensitivity, we expect the xPLD to out compete the endogenous PLD, which is what we see. We added the following sentence and reference : “The xPLD2 expression is >10x the endogenous PLD2 (enPLD2) and out computes the TREK-1 binding site for PLD25.”

1. Does the plasma membrane trafficking of TREK1 remain the same under different conditions (PLD2 overexpression, truncation)? From Figure S2, the truncated TREK1 seem to have very poor trafficking. The change of trafficking could significantly contribute to the interpretation of the data in Figure 1.

Response: If the PLD2 binding site is removed (TREK-1trunc), yes, the trafficking to the plasma membrane is unaffected by the expression of xPLD and mPLD (Author response image 2 above). For full length TREK1 (FL-TREK-1), co-expression of mPLD decreases TREK expression (Author response image 2) and coexpression with xPLD increases TREK expression (Figure S2f). This is exactly opposite of what one would expect if surface expression accounted for the change in pressure currents. Hence, we conclude surface expression does not account for loss of TREK-1 mechanosensitivity with xPLD2. A few sentences was added to the discussion. We also performed dSTORM on the TREKtruncated using EGFP. TREK-truncated goes to PIP2 (see figure 2 of 6)

Author response image 3.

To better compare the levels of TREK-1 before and after shear, we added a supplemental figure S2f where the protein was compared simultaneously in all conditions. 15 min of shear significantly decreased TREK-1 except with mPLD2 where the levels before shear were already lowest of all the expression levels tested.

For shear-induced movement of TREK1 between nanodomains. The section is convincing, however I'm not an expert on super-resolution imaging. Also, it would be helpful to clarify whether the shear stress was maintained during fixation. If not, what is the >me gap between reduced shear and the fixed state. lastly, it's unclear why shear flow changes the level of TREK1 and PIP2.

Response: Shear was maintained during the fixing. xPLD2 blocks endocytosis, presumably endocytosis and or release of other lipid modifying enzymes affect the system. The change in TREK-1 levels appears to be directly through an interaction with PLD as TREK trunc is not affected by over expression of xPLD or mPLD.

For the mechanism of PLD2 activation by shear. I found this section not convincing. Therefore, the question of how does PLD2 sense mechanical force on the membrane is not fully addressed. Par>cularly, it's hard to imagine an acute 25% decrease cholesterol level by shear - where did the cholesterol go? Details on the measurements of free cholesterol level is unclear and additional/alternative experiments are needed to prove the reduction in cholesterol by shear.

Response: The question “how does PLD2 sense mechanical force on the membrane” we addressed and published in Nature Comm. In 2016. The title of that paper is “Kinetic disruption of lipid rafts is a mechanosensor for phospholipase D” see ref 13 Petersen et. al. PLD is a soluble protein associated to the membrane through palmitoylation. There is no transmembrane domain, which narrows the possible mechanism of its mechanosensation to disruption.

The Nature Comm. reviewer identified as “an expert in PLD signaling” wrote the following of our data and the proposed mechanism:

“This is a provocative report that identi0ies several unique properties of phospholipase D2 (PLD2). It explains in a novel way some long established observations including that the enzyme is largely regulated by substrate presentation which 0its nicely with the authors model of segregation of the two lipid raft domains (cholesterol ordered vs PIP2 containing). Although PLD has previously been reported to be involved in mechanosensory transduction processes (as cited by the authors) this is the 0irst such report associating the enzyme with this type of signaling... It presents a novel model that is internally consistent with previous literature as well as the data shown in this manuscript. It suggests a new role for PLD2 as a force transduction tied to the physical structure of lipid rafts and uses parallel methods of disrup0on to test the predic0ons of their model.”

Regarding cholesterol. We use a fluorescent cholesterol oxidase assay which we described in the methods. This is an appropriate assay for determining cholesterol levels in a cell which we use routinely. We have published in multiple journals using this method, see references 28, 30, 31. Working out the metabolic fate of cholesterol after sheer is indeed interesting but well beyond the scope of this paper. Furthermore, we indirectly confirmed our finding using dSTORM cluster analysis (Figure 3d-e). The cluster analysis shows a decrease in GM1 cluster size consistent with our previous experiments where we chemically depleted cholesterol and saw a similar decrease in cluster size (see ref 13). All the data are internally consistent, and the cholesterol assay is properly done. We see no reason to reject the data.

Importantly, there is no direct evidence for "shear thinning" of the membrane and the authors should avoid claiming shear thinning in the abstract and summary of the manuscript.

Response: We previously established a kinetic model for PLD2 activation see ref 13 (Petersen et al Nature Comm 2016). In that publication we discussed both entropy and heat as mechanisms of disruption. Here we controlled for heat which narrowed that model to entropy (i.e., shear thinning) (see Figure 3c). We provide an overall justification below. But this is a small refinement of our previous paper, and we prefer not to complicate the current paper. We believe the proper rheological term is shear thinning. The following justification, which is largely adapted from ref 13, could be added to the supplement if the reviewer wishes.

Justification: To establish shear thinning in a biological membrane, we initially used a soluble enzyme that has no transmembrane domain, phospholipase D2 (PLD2). PLD2 is a soluble enzyme and associated with the membrane by palmitate, a saturated 16 carbon lipid attached to the enzyme. In the absence of a transmembrane domain, mechanisms of mechanosensation involving hydrophobic mismatch, tension, midplane bending, and curvature can largely be excluded. Rather the mechanism appears to be a change in fluidity (i.e., kinetic in nature). GM1 domains are ordered, and the palmate forms van der Waals bonds with the GM1 lipids. The bonds must be broken for PLD to no longer associate with GM1 lipids. We established this in our 2016 paper, ref 13. In that paper we called it a kinetic effect, however we did not experimentally distinguish enthalpy (heat) vs. entropy (order). Heat is Newtonian and entropy (i.e., shear thinning) is non-Newtonian. In the current study we paid closer attention to the heat and ruled it out (see Figure 3c and methods). We could propose a mechanism based on kinetic disruption, but we know the disruption is not due to melting of the lipids (enthalpy), which leaves shear thinning (entropy) as the plausible mechanism.

The authors should also be aware that hypotonic shock is a very dirty assay for stretching the cell membrane. Ouen, there is only a transient increase in membrane tension, accompanied by many biochemical changes in the cells (including acidification, changes of concentration etc). Therefore, I would not consider this as definitive proof that PLD2 can be activated by stretching membrane.

Response: Comment noted. We trust the reviewer is correct. In 1998 osmotic shock was used to activate the channel. We only intended to show that the system is consistent with previous electrophysiologic experiments.

References cited:

1 Du G, Huang P, Liang BT, Frohman MA. Phospholipase D2 localizes to the plasma membrane and regulates angiotensin II receptor endocytosis. Mol Biol Cell 2004;15:1024–30. htps://doi.org/10.1091/mbc.E03-09-0673.

2 Koch T, Wu DF, Yang LQ, Brandenburg LO, Höllt V. Role of phospholipase D2 in the agonist-induced and constistutive endocytosis of G-protein coupled receptors. J Neurochem 2006;97:365–72. htps://doi.org/10.1111/j.1471-4159.2006.03736.x.

3 Wheeler DS, Underhill SM, Stolz DB, Murdoch GH, Thiels E, Romero G, et al. Amphetamine activates Rho GTPase signaling to mediate dopamine transporter internalization and acute behavioral effects of amphetamine. Proc Natl Acad Sci U S A 2015;112:E7138–47. htps://doi.org/10.1073/pnas.1511670112.

4 Rankovic M, Jacob L, Rankovic V, Brandenburg L-OO, Schröder H, Höllt V, et al. ADP-ribosylation factor 6 regulates mu-opioid receptor trafficking and signaling via activation of phospholipase D2. Cell Signal 2009;21:1784–93. htps://doi.org/10.1016/j.cellsig.2009.07.014.

5 Pavel MA, Petersen EN, Wang H, Lerner RA, Hansen SB. Studies on the mechanism of general anesthesia. Proc Natl Acad Sci U S A 2020;117:13757–66. htps://doi.org/10.1073/pnas.2004259117.

6 Call IM, Bois JL, Hansen SB. Super-resolution imaging of potassium channels with genetically encoded EGFP. BioRxiv 2023. htps://doi.org/10.1101/2023.10.13.561998.

Author response:

The following is the authors’ response to the original reviews.

Public reviews:

Reviewer #1:

This work by Leclercq and colleagues performed metabolomics on biospecimens collected from 96 patients diagnosed with several types of alcohol use disorders (AUD). The authors discovered strong alterations in circulating glycerophospholipids, bile acids, and some gut microbe-derived metabolites in AUD patients compared to controls. An exciting part of this work is that metabolomics was also performed in frontal cortex of post-mortem brains and cerebrospinal fluid of heavy alcohol users, and some of the same metabolites were seen to be altered in the central nervous system. This is an important study that will form the basis for hypothesis generation around diet-microbe-host interactions in alcohol use disorder. The work is done in a highly rigorous manner, and the rigorously collected human samples are a clear strength of this work. Overall, many new insights may be gained by this work, and it is poised to have a high impact on the field.

Strengths:

(1) The rigorously collected patient-derived samples.

(2) There is high rigor in the metabolomics investigation.

(3) Statistical analyses are well-described and strong.

(4) An evident strength is the careful control of taking blood samples at the same time of the day to avoid alterations in meal- and circadian-related fluctuations in metabolites.

Weaknesses:

(1) Some validation in animal models of ethanol exposure compared to pair-fed controls would help strengthen causal relationships between metabolites and alterations in the CNS.

(2) The classification of "heavy alcohol users" based on autopsy reports may not be that accurate.

(3) The fact that most people with alcohol use disorder choose to drink over eating food, there needs to be some more discussion around how dietary intake (secondary to heavy drinking) most likely has a significant impact on the metabolome.<br />

We thank this reviewer for his/her encouraging comments and for highlighting the fact that this study is important in the field to generate hypotheses around diet-microbe-host interactions in alcohol use disorder.

Concerning weakness #1: Regarding the validation in animal models of ethanol exposure, we were very careful in our discussion to avoid pretending that the study allowed to test causality of the factors. This was certainly not the objective of the present study. The testing of causality would indeed probably necessitate animal models but these models could only test the effects of one single metabolite at a time and could not at the same time capture the complexity of the changes occurring in AUD patients. The testing of metabolites would be a totally different topic. Hence, we do not feel comfortable in conducting rodent experiments for several reasons. First, AUD is a very complex pathology with physiological and psychological/psychiatric alterations that are obviously difficult to reproduce in animal models. Secondly, as mentioned by the reviewer, AUD pathology spontaneously leads to nutritional deficits, including significant reductions in carbohydrates, lipids, proteins and fiber intakes. We have recently published a paper in which we carefully conducted detailed dietary anamneses and described the changes in food habits in AUD patients (Amadieu et al., 2021). As explained below, some blood metabolites that are significantly correlated with depression, anxiety and craving belong to the xanthine family and are namely theobromine, theophylline, and paraxanthine, which derived from metabolism of coffee, tea or chocolate (which are not part of the normal diet of mice or rats).Therefore, conducting an experiment in animal model of ethanol exposure compared to pair-fed controls will omit the important impact of nutrition in blood metabolomics and consequently won’t mimic the human AUD pathology. In addition, if we take into consideration the European Directive 2010/63/EU (on the protection of animals used for scientific purposes) which aims at Reducing (Refining, Replacing) the number of animals used in experiment, it is extremely difficult to justify, at the ethical point of view, the need to reproduce human results in an animal model that won’t be able to mimic the nutritional, physiological and psychological alterations of alcohol use disorder.

Concerning weakness #2: The classification of subjects to the group who have a history of heavy alcohol use was not solely on autopsy record, but was also based on medical history i.e. diagnosis of alcohol-related diseases: ICD-10 codes F10.X, G31.2, G62.1, G72.1, I42.6, K70.0-K70.4, K70.9, and K86.0, or signs of heavy alcohol use in the clinical or laboratory findings, e.g., increased levels of gamma-glutamyl transferase, mean corpuscular volume, carbohydrate-deficient transferrin, as stated in the methods section of the manuscript. In Finland, the medical records from the whole life of the subjects are available. We consider that getting diagnosis of alcohol-related disease is clear sign of history of heavy alcohol use.

Concerning weakness#3:  As explained above, we do agree with the reviewer that AUD is not only “drinking alcohol” but is also associated with reduction in food intake that obviously influenced the metabolomics data presented in this current study.  We have therefore added some data, which have not been published before, in the results section that refer to key nutrients modified by alcohol intake and we refer to those data and their link with metabolomics in the discussion section: