The author reused the case study of Dryer (2018) word order pattern.

This is a major methodological advance for typology. These models require statistical expertise, which may limit accessibility for many linguists.

The authors made a clear distinction between replication, and replicability. This denotes that replication is not just re-running the same test, but as testing the dependence of conclusions on analytic choices.

Traitors, not even rebels

https://sites.google.com/view/classroom6x/the-binding-of-isaac-wrath-of-the-lamb cain is just better on waflash

insert heavenly muisic

Hi

67

one solution

climate anxiety is specially true for young groups, this can be useful when first identifying why it's important to focus on young generations when discussing negative impacts of climate change

this is a talk?

media filters

filter

Version 3 of this preprint has been peer-reviewed and recommended by Peer Community in Evolutionary Biology.<br /> See the peer reviews and the recommendation.

This shows what people are currently doing about climate change in India

this could add to the weathering the Storm article because it states the need for a solution

This relates to the nyt article

This directly discusses how everyday life is being impacted by climate change for teens, especially in a crowded place such as India

!!!!!!

quote this ?

how to regulate this or get the info that someone is unsafe ? just research this more !!

should be bold

should be bold

Ottawa

...2024-2025 (millions) https://parks.canada.ca/agence-agency/dp-pd/rft-qfr/rep01_2025

Autorisations budgétaires et dépenses pour le trimestre se termine le 30 septembre de 2025-2026 et 2024-2025 — Version texte

The graph is zoomed out, the title should be inside the graph. Please refer to the last QFR : https://parks.canada.ca/agence-agency/dp-pd/rft-qfr/rep01_2025

This row should be bold

235,275

232,760

...September 30 (Millions) (refer to QFR Q1, the millions is under : https://parks.canada.ca/agence-agency/dp-pd/rft-qfr/rep01_2025)

Budgetary Authorities and Expenditures for the quarter of 2025-26 and 2024-25 ending September 30 — Text version

The graph is zoomed out, the title should be inside the graph. Please refer to the last QFR : https://parks.canada.ca/agence-agency/dp-pd/rft-qfr/rep01_2025

1. FAQ SECTION (Zmniejszenie obaw)

Musi odpowiadać na 5-10 najczęstszych pytań. Dla optyki:

Best practice: Sekcja FAQ na dnie (scroll depth = 70%+), ale musi być

1. PRIMARY CTA - CALL-TO-ACTION (Konwersja)

Button design

• Text: “Kupię teraz” (nie “Submit”, nie “Kup”)
• Color: High contrast na tłem (np. zielony na białym, ciemny na jasnym)
• Size: Duży - minimum 50px wysokość
• Position: Sticky na mobile (zawsze widoczny)
• Feedback: Zaraz jak kliknę, button pokazuje “Adding…” + zmienia się na “In cart ✓”

Drugi CTA (optional but recommended)

“+ DODAJ DO LISTY ŻYCZEŃ” (heart icon) - nie odwraca flow, ale buduje retargeting list

Dlaczego 4.8, a nie 5.0?

Rzeczywistość = bardziej wiarygodne

Review snippets - wyciąg najlepszych 3-5 opinii • Pełne imię i miasto • Fragment tekstu (2-3 linijki) • Verified purchase badge • Data (względna, np. “2 tygodnie temu”)

User-generated content (UGC photos)

Sekcja: “Jak faktycznie wyglądają? Patrz, jak noszą je nasi klienci”

Photos z hashtagu lub wygrane z konkursu - buduje emocjonalne zaufanie

Short overview (50-80 słów, benefit-focused) ❌ “Frame material: TAC. Lens type: Polarized. Weight: 15g. Fit: Regular.”
 ✅ “Lekkie, polaryzacyjne okulary w ikonicznym stylu retro. Chronią oczy 100% UV. Idealne do codziennego noszenia - nie będziesz czuł zmęczenia nawet po 8 godzinach pracy przy komputerze. Włoskie materiały, trwają lata.”

Dlaczego druga? Odpowiada na pytanie: “Co dla mnie robią?” (emocja + logika)

Wariacje produktu - MUSZĄ być dla optyki

Ważne: Gdy klient zmienia wariancję, główne zdjęcie powinno się automatycznie zmienić

PRICE SECTION (Psychologia decyzji cenowej)

Format rabatu - ANCHOR EFFECT ❌ “499 PLN”
 ✅ “Była: 699 PLN → Teraz: 499 PLN (-29%)” lub “ZAOSZCZĘDZISZ: 200 PLN”

Psychologia: Klienci widzą “oszczędność”, nie “cena jest niska”

Visual badge “Top seller” lub “Expert choice” lub “New arrival” - jednorazowo widoczne

1. ABOVE THE FOLD (Co widać bez scrollowania) - SEKCJA NAJKRYTYCZNIEJSZA To first 3-5 sekund na stronie. Jeśli tu klient się nie orientiuje, bounce rate = 50%. Musi być widoczne (bez scrollowania):

PRODUCT TITLE & OVERVIEW (Emocjonalna i logiczna perswazja)

Product title (nie jest to “Okulary”)

❌ “Wayfarer Sunglasses Black”
 ✅ “Ray-Ban Wayfarer 2140 Polarized UV Protection - Classic Black”

Dlaczego druga? Keywords dla SEO + jasne benefits

1. TECHNICAL SPECIFICATIONS (Zmniejszenie ryzyko zwrotu

(Ostatnia linia obrony przed cart abandonment) Umieszczenie kluczowe: BLISKO CTA BUTTON

Fakty: • 75% konsumentów bazuje decyzję na zdjęciach • Lifestyle photos zwiększają konwersję o 25-50% • Bez lifestyle photos: “To jest produkt”, z lifestyle photos: “To mogę być ja” Co musi być w galerii (minimum):

If you find this you are very sigma!

Quizás acá se puede profundizar más en el caso chileno como menciona andreas más arriba

Creo que hay que homogeneizar todos los fairness y justice, nosotros generalmente hemos usado justice

Esto está en el párrafo de arriba

az ELTE Digitális Bölcsészet Tanszékének hivatalos weblapja

egy évente megrendezett konferenciasorozat

a Tanszék kollégája

ELTE

tanszék

szemeszter

Adding title name for each of the plot, rename the x-axis and y-axis, so make it clearly for the readers

move this up and write this in the source mode, so the heading will appear, not as ##

That's also the IMPORT section

Great Work!

Instead of calling "Model" for this section, using the test name as your heading. Like "Linear Regression"

You already called Figure 1 for your first histogram, so for here it should be Figure 3

Same here, Add title name for each of the plot, rename the x-axis and y-axis, so make it clearly for the readers

Maybe change the figure caption, instead of saying "Two histograms....", explain each by each, and try to make them different. And figure number like" Figure 1. " before each caption

This is not ggplot, I would recommend using ggplot because the look of the graph will be a lot more customizable

With your scale for the x-axis, you should edit the binwidth so each bar on the histogram is more visible

I had no idea!

I think there's so much value in opening up these databases for communities to have a hands on experience in how their information is brought to them and the intention that's behind gathering it. It will deepen their underatnding on the concept of archeology and might help to rewrite narrattives nad block out sterotypes.

This helped me understand a lot better

So what I got from this is that newer data collection methods are more objecties than those of the past

Do they mean strictly excavation? Why is it mostly destuctive?

I'm not really sure what this means but I also figure that people might assume that not much theory would be required due to the computerized nature of everything

eLife Assessment

This valuable manuscript provides solid evidence regarding the role of alpha oscillations in sensory gain control. The authors use an attention-cuing task in an initial EEG study followed by a separate MEG replication study to demonstrate that whilst (occipital) alpha oscillations are increased when anticipating an auditory target, so is visual responsiveness as assessed with frequency tagging. The authors propose that their results demonstrate a general vigilance effect on sensory processing and offer a re-interpretation of the inhibitory role of the alpha rhythm.

Reviewer #1 (Public review):

In this study, Brickwedde et al. leveraged a cross-modal task where visual cues indicated whether upcoming targets required visual or auditory discrimination. Visual and auditory targets were paired with auditory and visual distractors, respectively. The authors found that during the cue-to-target interval, posterior alpha activity increased along with auditory and visual frequency-tagged activity when subjects were anticipating auditory targets. The authors conclude that their results imply that alpha modulation does not solely regulate 'gain control' in early visual areas (also referred to as alpha inhibition hypothesis), but rather orchestrates signal transmission to later stages of the processing stream.

Comments on revisions:

I thank the authors for their clarifications. The manuscript is much improved now, in my opinion. The new power spectral density plots and revised Figure 1 are much appreciated. However, there is one remaining point that I am unclear about. In the rebuttal, the authors state the following: "To directly address the question of whether the auditory signal was distracting, we conducted a follow-up MEG experiment. In this study, we observed a significant reduction in visual accuracy during the second block when the distractor was present (see Fig. 7B and Suppl. Fig. 1B), providing clear evidence of a distractor cost under conditions where performance was not saturated."

I am very confused by this statement, because both Fig. 7B and Suppl. Fig. 1B show that the visual- (i.e., visual target presented alone) has a lower accuracy and longer reaction time than visual+ (i.e., visual target presented with distractor). In fact, Suppl. Fig. 1B legend states the following: "accuracy: auditory- - auditory+: M = 7.2 %; SD = 7.5; p = .001; t(25) = 4.9; visual- - visual+: M = -7.6%; SD = 10.80; p < .01; t(25) = -3.59; Reaction time: auditory- - auditory +: M = -20.64 ms; SD = 57.6; n.s.: p = .08; t(25) = -1.83; visual- - visual+: M = 60.1 ms ; SD = 58.52; p < .001; t(25) = 5.23)."

These statements appear to directly contradict each other. I appreciate that the difficulty of auditory and visual trials in block 2 of MEG experiments are matched, but this does not address the question of whether the distractor was actually distracting (and thus needed to be inhibited by occipital alpha). Please clarify.

Author response:

The following is the authors’ response to the previous reviews

Reviewer #1 (Public review):

In this study, Brickwedde et al. leveraged a cross-modal task where visual cues indicated whether upcoming targets required visual or auditory discrimination. Visual and auditory targets were paired with auditory and visual distractors, respectively. The authors found that during the cue-to-target interval, posterior alpha activity increased along with auditory and visual frequency-tagged activity when subjects were anticipating auditory targets. The authors conclude that their results disprove the alpha inhibition hypothesis, and instead implies that alpha "regulates downstream information transfer." However, as I detail below, I do not think the presented data irrefutably disproves the alpha inhibition hypothesis. Moreover, the evidence for the alternative hypothesis of alpha as an orchestrator for downstream signal transmission is weak. Their data serves to refute only the most extreme and physiologically implausible version of the alpha inhibition hypothesis, which assumes that alpha completely disengages the entire brain area, inhibiting all neuronal activity.

We thank the reviewer for taking the time to provide additional feedback and suggestions and we improved our manuscript accordingly.

(1) Authors assign specific meanings to specific frequencies (8-12 Hz alpha, 4 Hz intermodulation frequency, 36 Hz visual tagging activity, 40 Hz auditory tagging activity), but the results show that spectral power increases in all of these frequencies towards the end of the cue-to-target interval. This result is consistent with a broadband increase, which could simply be due to additional attention required when anticipating auditory target (since behavioral performance was lower with auditory targets, we can say auditory discrimination was more difficult). To rule this out, authors will need to show a power spectral density curve with specific increases around each frequency band of interest. In addition, it would be more convincing if there was a bump in the alpha band, and distinct bumps for 4 vs 36 vs 40 Hz band.

This is an interesting point with several aspects, which we will address separately

Broadband Increase vs. Frequency-Specific Effects:

The suggestion that the observed spectral power increases may reflect a broadband effect rather than frequency-specific tagging is important. However, Supplementary Figure 11 shows no difference between expecting an auditory or visual target at 44 Hz. This demonstrates that (1) there is no uniform increase across all frequencies, and (2) the separation between our stimulation frequencies was sufficient to allow differentiation using our method.

Task Difficulty and Performance Differences:

The reviewer suggests that the observed effects may be due to differences in task difficulty, citing lower performance when anticipating auditory targets in the EEG study. This issue was explicitly addressed in our follow-up MEG study, where stimulus difficulty was calibrated. In the second block—used for analysis—accuracy between auditory and visual targets was matched (see Fig. 7B). The replication of our findings under these controlled conditions directly rules out task difficulty as the sole explanation. This point is clearly presented in the manuscript.

Power Spectrum Analysis:

The reviewer’s suggestion that our analysis lacks evidence of frequency-specific effects is addressed directly in the manuscript. While we initially used the Hilbert method to track the time course of power fluctuations, we also included spectral analyses to confirm distinct peaks at the stimulation frequencies. Specifically, when averaging over the alpha cluster, we observed a significant difference at 10 Hz between auditory and visual target expectation, with no significant differences at 36 or 40 Hz in that cluster. Conversely, in the sensor cluster showing significant 36 Hz activity, alpha power did not differ, but both 36 Hz and 40 Hz tagging frequencies showed significant effects These findings clearly demonstrate frequency-specific modulation and are already presented in the manuscript.

(2) For visual target discrimination, behavioral performance with and without the distractor is not statistically different. Moreover, the reaction time is faster with distractor. Is there any evidence that the added auditory signal was actually distracting?

We appreciate the reviewer’s observation regarding the lack of a statistically significant difference in behavioral performance for visual target discrimination with and without the auditory distractor. While this was indeed the case in our EEG experiment, we believe the absence of an accuracy effect may be attributable to a ceiling effect, as overall visual performance approached 100%. This high baseline likely masked any subtle influence of the distractor.

To directly address the question of whether the auditory signal was distracting, we conducted a follow-up MEG experiment. In this study, we observed a significant reduction in visual accuracy during the second block when the distractor was present (see Fig. 7B and Suppl. Fig. 1B), providing clear evidence of a distractor cost under conditions where performance was not saturated.

Regarding the faster reaction times observed in the presence of the auditory distractor, this phenomenon is consistent with prior findings on intersensory facilitation. Auditory stimuli, which are processed more rapidly than visual stimuli, can enhance response speed to visual targets—even when the auditory input is non-informative or nominally distracting (Nickerson, 1973; Diederich & Colonius, 2008; Salagovic & Leonard, 2021). Thus, while the auditory signal may facilitate motor responses, it can simultaneously impair perceptual accuracy, depending on task demands and baseline performance levels.

Taken together, our data suggest that the auditory signal does exert a distracting influence, particularly under conditions where visual performance is not at ceiling. The dual effect—facilitated reaction time but reduced accuracy—highlights the complexity of multisensory interactions and underscores the importance of considering both behavioral and neurophysiological measures.

(3) It is possible that alpha does suppress task-irrelevant stimuli, but only when it is distracting. In other words, perhaps alpha only suppresses distractors that are presented simultaneously with the target. Since the authors did not test this, they cannot irrefutably reject the alpha inhibition hypothesis.

The reviewer’s claim that we did not test whether alpha suppresses distractors presented simultaneously with the target is incorrect. As stated in the manuscript and supported by our data (see point 2), auditory distractors were indeed presented concurrently with visual targets, and they were demonstrably distracting. Therefore, the scenario the reviewer suggests was not only tested—it forms a core part of our design.

Furthermore, it was never our intention to irrefutably reject the alpha inhibition hypothesis. Rather, our aim was to revise and expand it. If our phrasing implied otherwise, we have now clarified this in the manuscript. Specifically, we propose that alpha oscillations:

(a) Exhibit cyclic inhibitory and excitatory dynamics;

(b) Regulate processing by modulating transfer pathways, which can result in either inhibition or facilitation depending on the network context.

In our study, we did not observe suppression of distractor transfer, likely due to the engagement of a supramodal system that enhances both auditory and visual excitability. This interpretation is supported by prior findings (e.g., Jacoby et al., 2012), which show increased visual SSEPs under auditory task load, and by Zhigalov et al. (2020), who found no trial-by-trial correlation between alpha power and visual tagging in early visual areas, despite a general association with attention.

Recent evidence (Clausner et al., 2024; Yang et al., 2024) further supports the notion that alpha oscillations serve multiple functional roles depending on the network involved. These roles include intra- and inter-cortical signal transmission, distractor inhibition, and enhancement of downstream processing (Scheeringa et al., 2012; Bastos et al., 2015; Zumer et al., 2014). We believe the most plausible account is that alpha oscillations support both functions, depending on context.

To reflect this more clearly, we have updated Figure 1 to present a broader signal-transfer framework for alpha oscillations, beyond the specific scenario tested in this study.

We have now revised Figure 1 and several sentences in the introduction and discussion, to clarify this argument.

L35-37: Previous research gave rise to the prominent alpha inhibition hypothesis, which suggests that oscillatory activity in the alpha range (~10 Hz) plays a mechanistic role in selective attention through functional inhibition of irrelevant cortical areas (see Fig. 1; Foxe et al., 1998; Jensen & Mazaheri, 2010; Klimesch et al., 2007).

L60-65: In contrast, we propose that functional and inhibitory effects of alpha modulation, such as distractor inhibition, are exhibited through blocking or facilitating signal transmission to higher order areas (Peylo et al., 2021; Yang et al., 2023; Zhigalov & Jensen, 2020; Zumer et al., 2014), gating feedforward or feedback communication between sensory areas (see Fig. 1; Bauer et al., 2020; Haegens et al., 2015; Uemura et al., 2021).

L482-485: This suggests that responsiveness of the visual stream was not inhibited when attention was directed to auditory processing and was not inhibited by occipital alpha activity, which directly contradicts the proposed mechanism behind the alpha inhibition hypothesis.

L517-519: Top-down cued changes in alpha power have now been widely viewed to play a functional role in directing attention: the processing of irrelevant information is attenuated by increasing alpha power in areas involved with processing this information (Foxe, Simpson, & Ahlfors, 1998; Hanslmayr et al., 2007; Jensen & Mazaheri, 2010).

L566-569: As such, it is conceivable that alpha oscillations can in some cases inhibit local transmission, while in other cases, depending on network location, connectivity and demand, alpha oscillation can facilitate signal transmission. This mechanism allows to increase transmission of relevant information and to block transmission of distractors.

(4) In the abstract and Figure 1, the authors claim an alternative function for alpha oscillations; that alpha "orchestrates signal transmission to later stages of the processing stream." In support, the authors cite their result showing that increased alpha activity originating from early visual cortex is related to enhanced visual processing in higher visual areas and association areas. This does not constitute a strong support for the alternative hypothesis. The correlation between posterior alpha power and frequency-tagged activity was not specific in any way; Fig. 10 shows that the correlation appeared on both 1) anticipating-auditory and anticipating-visual trials, 2) the visual tagged frequency and the auditory tagged activity, and 3) was not specific to the visual processing stream. Thus, the data is more parsimonious with a correlation than a causal relationship between posterior alpha and visual processing.

Again, the reviewer raises important points, which we want to address

The correlation between posterior alpha power and frequency-tagged activity was not specific, as it is present both when auditory and visual targets are expected:

If there is a connection between posterior alpha activity and higher-order visual information transfer, then it can be expected that this relationship remains across conditions and that a higher alpha activity is accompanied by higher frequency-tagged activity, both over trials and over conditions. However, it is possible that when alpha activity is lower, such as when expecting a visual target, the signal-to-noise ratio is affected, which may lead to higher difficulty to find a correlation effect in the data when using non-invasive measurements.

The connection between alpha activity and frequency-tagged activity appears both for auditory as well as visual stimuli and The correlation is not specific to the visual processing stream:

While we do see differences between conditions (e.g. in the EEG-analysis, mostly 36 Hz correlated with alpha activity and only in one condition 40 Hz showed a correlation as well), it is true that in our MEG analysis, we found correlations both between alpha activity and 36 Hz as well as alpha activity and 40 Hz.  

We acknowledge that when analysing frequency-tagged activity on a trial-by-trial basis, where removal of non-timelocked activity through averaging (which we did when we tested for condition differences in Fig. 4 and 9) is not possible, there is uncertainty in the data. Baseline-correction can alleviate this issue, but it cannot offset the possibility of non-specific effects. We therefore decided to repeat the analysis with a fast-fourier calculated power instead of the Hilbert power, in favour of a higher and stricter frequency-resolution, as we averaged over a time-period and thus, the time-domain was not relevant for this analysis. In this more conservative analysis, we can see that only 36 Hz tagged activity when expecting an auditory target correlated with early visual alpha activity.

Additionally, we added correlation analyses between alpha activity and frequency-tagged activity within early visual areas, using the sensor cluster which showed significant condition differences in alpha activity. Here, no correlations between frequency-tagged activity and alpha activity could be found (apart from a small correlation with 40 Hz which could not be confirmed by a median split; see SUPPL Fig. 14 C). The absence of a significant correlation between early visual alpha and frequency-tagged activity has previously been described by others (Zhigalov & Jensen, 2020) and a Bayes factor of below 1 also indicated that the alternative hypotheses is unlikely.

Nonetheless, a correlation with auditory signal is possible and could be explained in different ways. For example, it could be that very early auditory feedback in early visual cortex (see for example Brang et al., 2022) is transmitted alongside visual information to higher-order areas. Several studies have shown that alpha activity and visual as well as auditory processing are closely linked together (Bauer et al., 2020; Popov et al., 2023). Inference on whether or how this link could play out in the case of this manuscript expands beyond the scope of this study.

To summarize, we believe the fact that 36 Hz activity within early visual areas does not correlate with alpha activity on a trial-by-trial basis, but that 36 Hz activity in other areas does, provides strong evidence that alpha activity affects down-stream signal processing.

We mention this analysis now in our discussion:

L533-536: Our data provides evidence in favour of this view, as we can show that early sensory alpha activity does not covary over trials with SSEP magnitude in early visual areas, but covaries instead over trials with SSEP magnitude in higher order sensory areas (see also SUPPL. Fig. 14).

Reviewer #1 (Recommendations for the authors):

The evidence for the alternative hypothesis, that alpha in early sensory areas orchestrates downstream signal transmission, is not strong enough to be described up front in the abstract and Figure 1. I would leave it in the Discussion section, but advise against mentioning it in the abstract and Figure 1.

We appreciate the reviewer’s concern regarding the inclusion of the alternative hypothesis—that alpha activity in early sensory areas orchestrates downstream signal transmission—in the abstract and Figure 1. While we agree that this interpretation is still developing, recent studies (Keitel et al., 2025; Clausner et al., 2024; Yang et al., 2024) provide growing support for this framework.

In response, we have revised the introduction, discussion, and Figure 1 to clarify that our intention is not to outright dismiss the alpha inhibition hypothesis, but to refine and expand it in light of new data. This revision does not invalidate the prior literature on alpha timing and inhibition; rather, it proposes an updated mechanism that may better account for observed effects.

We have though retained Figure 1, as it visually contextualizes the broader theoretical landscape. while at the same time added further analyses to strengthen our empirical support for this emerging view.

References:

Bastos, A. M., Litvak, V., Moran, R., Bosman, C. A., Fries, P., & Friston, K. J. (2015). A DCM study of spectral asymmetries in feedforward and feedback connections between visual areas V1 and V4 in the monkey. NeuroImage, 108, 460–475. https://doi.org/10.1016/j.neuroimage.2014.12.081

Bauer, A. R., Debener, S., & Nobre, A. C. (2020). Synchronisation of Neural Oscillations and Cross-modal Influences. Trends in cognitive sciences, 24(6), 481–495. https://doi.org/10.1016/j.tics.2020.03.003

Brang, D., Plass, J., Sherman, A., Stacey, W. C., Wasade, V. S., Grabowecky, M., Ahn, E., Towle, V. L., Tao, J. X., Wu, S., Issa, N. P., & Suzuki, S. (2022). Visual cortex responds to sound onset and offset during passive listening. Journal of neurophysiology, 127(6), 1547–1563. https://doi.org/10.1152/jn.00164.2021

Clausner T., Marques J., Scheeringa R. & Bonnefond M (2024). Feature specific neuronal oscillations in cortical layers BioRxiv :2024.07.31.605816. https://doi.org/10.1101/2024.07.31.605816

Diederich, A., & Colonius, H. (2008). When a high-intensity "distractor" is better then a low-intensity one: modeling the effect of an auditory or tactile nontarget stimulus on visual saccadic reaction time. Brain research, 1242, 219–230. https://doi.org/10.1016/j.brainres.2008.05.081

Haegens, S., Nácher, V., Luna, R., Romo, R., & Jensen, O. (2011). α-Oscillations in the monkey sensorimotor network influence discrimination performance by rhythmical inhibition of neuronal spiking. Proceedings of the National Academy of Sciences of the United States of America, 108(48), 19377–19382. https://doi.org/10.1073/pnas.1117190108

Jacoby, O., Hall, S. E., & Mattingley, J. B. (2012). A crossmodal crossover: opposite effects of visual and auditory perceptual load on steady-state evoked potentials to irrelevant visual stimuli. NeuroImage, 61(4), 1050–1058. https://doi.org/10.1016/j.neuroimage.2012.03.040

Keitel, A., Keitel, C., Alavash, M., Bakardjian, K., Benwell, C. S. Y., Bouton, S., Busch, N. A., Criscuolo, A., Doelling, K. B., Dugue, L., Grabot, L., Gross, J., Hanslmayr, S., Klatt, L.-I., Kluger, D. S., Learmonth, G., London, R. E., Lubinus, C., Martin, A. E., … Kotz, S. A. (2025). Brain rhythms in cognition – controversies and future directions. ArXiv. https://doi.org/10.48550/arXiv.2507.15639

Nickerson R. S. (1973). Intersensory facilitation of reaction time: energy summation or preparation enhancement?. Psychological review, 80(6), 489–509. https://doi.org/10.1037/h0035437

Popov, T., Gips, B., Weisz, N., & Jensen, O. (2023). Brain areas associated with visual spatial attention display topographic organization during auditory spatial attention. Cerebral cortex (New York, N.Y. : 1991), 33(7), 3478–3489. https://doi.org/10.1093/cercor/bhac285

Salagovic, C. A., & Leonard, C. J. (2021). A nonspatial sound modulates processing of visual distractors in a flanker task. Attention, perception & psychophysics, 83(2), 800–809. https://doi.org/10.3758/s13414-020-02161-5

Scheeringa, R., Petersson, K. M., Kleinschmidt, A., Jensen, O., & Bastiaansen, M. C. (2012). EEG α power modulation of fMRI resting-state connectivity. Brain connectivity, 2(5), 254–264. https://doi.org/10.1089/brain.2012.0088

Spaak, E., Bonnefond, M., Maier, A., Leopold, D. A., & Jensen, O. (2012). Layer-specific entrainment of γ-band neural activity by the α rhythm in monkey visual cortex. Current biology : CB, 22(24), 2313–2318. https://doi.org/10.1016/j.cub.2012.10.020

Yang, X., Fiebelkorn, I. C., Jensen, O., Knight, R. T., & Kastner, S. (2024). Differential neural mechanisms underlie cortical gating of visual spatial attention mediated by alpha-band oscillations. Proceedings of the National Academy of Sciences of the United States of America, 121(45), e2313304121. https://doi.org/10.1073/pnas.2313304121

Zhigalov, A., & Jensen, O. (2020). Alpha oscillations do not implement gain control in early visual cortex but rather gating in parieto-occipital regions. Human brain mapping, 41(18), 5176–5186. https://doi.org/10.1002/hbm.25183

Zumer, J. M., Scheeringa, R., Schoffelen, J. M., Norris, D. G., & Jensen, O. (2014). Occipital alpha activity during stimulus processing gates the information flow to object-selective cortex. PLoS biology, 12(10), e1001965. https://doi.org/10.1371/journal.pbio.1001965

dont do this

Make this part in text not comment, and make sure include discussions section at the end.

Including some headings, like "#Results", "##IMPORT", "##TRANSFORM", "##Shapiro-Wilk Normality Test", "#Discussion"

I have check the survey you did, and is already in the correct order strongly disagree(1), disagree(2), ......, strongly agree(6).

And you recode the strongly disagreee(1) to strongly disagreee(6). So the order is reverse.

So the correct code is only recode -50 and -99 to NA is fine, and keep everything else as the orginal form.

Maybe write one sentence for each of the tests, talk about which of the variable you use and explain your p-value, by saying whether is significiant or not.

Female and Male refer to sex assigned at birth, and women and man refer to gender. Make sure to use corresponding language.

update to COMM_NEIGHBORS statement

If melodrama can complicate public understanding by enhancing perception of largely unrecognized issues, how do we determine when this complication is productive rather than overwhelming or confusing for the audience?

This makes me think of toxic discourse, where environmental harm is frequently hidden behind technical language/ Schwarze's argument that melodrama complicates a situation mirrors readings where this has been discussed.

The concept of oneness of feeling directly connects to the Schwarze's earlier critique of Burke. Burke favors the comic frame because it lessens tension and promotes unity. While melodrama does the opposite. Both approaches depend on how audiences are asked to feel their way into a public controversy.

If melodrama helps uncover environmental harm, when does it go too far? Is there a point where it's polarization becomes counterproductive?

Melodrama is a rhetorical frame build around sharp moral distinctions, emotional amplification, and polarized conflict.

The author argues that melodrama isn't just oversimplified good vs evil rhetoric but it's a set of coordinated appeals that can actually reveal hidden injustices in environmental issues. We should judge whether its appropriate and timely instead of seeing it as automatically harmful.

Deux sujets principaux : - campagne présidentielle de 2024 - contestation du résultat de l'élection présidentielle de 2020

On voit que c'est le principal rédacteur

35:30 - 37:09. In this segment, Professor Weyland reflects on the declining influence of the United States in Latin America, using Venezuela as a case study of waning geopolitical power. He argues that Washington’s inability to prevent Venezuela’s descent into authoritarianism—despite its proximity, economic importance, and oil reserves—reveals a broader erosion of U.S. leverage and credibility in its own hemisphere.

27:08 - 29:43. Russia is mentioned as one of the key international backers sustaining Nicolás Maduro’s regime alongside China and Iran, providing diplomatic cover and helping Venezuela evade U.S. sanctions. These references highlight how global authoritarian alliances, particularly Russian support, limit international leverage and deepen Venezuela’s isolation from Western democracies.

21:18 - 23:08. In this section, Professor Weyland uses humor and historical comparison to highlight the modern dilemma of granting dictators exile as a means to end authoritarian regimes. By referencing former Haitian dictator Jean-Claude Duvalier’s comfortable exile in France, he argues that today’s global norms and public outrage make such safe havens politically impossible—leaving leaders like Maduro with no incentive to relinquish power peacefully.

05:47 - 10:51. This moment underscores the mass exodus caused by economic devastation and repression, linking Venezuela’s political crisis directly to one of the largest refugee movements in the Western Hemisphere.

Probably best to make limitations its own paragraph

I like the structure of this section! I don't have any edits to make here.

I would add some explanation between each output. What do these numbers mean for your results?

If possible, change "GENDER01" just to "Gender" as the legend title

Your inline comments are very good, I would recommend adding just a small paragraph at the end of this section explaining your preprocessing (removing NAs, transforming variables, etc)

I think the inclusion of the research question feels a bit forced and awkward. Unless Dr. Shane specifically said you have to include your research question like this, I would reword the sentence to just start with "This study explored..." and then just explain what you did rather than end the sentence with a question mark.

En réalité, lutte ardente contre le féminisme vu comme l'ennemi idéologique. Dans la plupart du cas, le masculinisme n'est pas là pour défendre les hommes en cohabitant avec le féminisme

hello I'm very lonly

Overall solid section, I like how you briefly reexplain the process and what the relationships turned out to be. Additionally, it was good to propose an explanation for your results. If I were to add anything, it would be explaining why you suggest those certain topics for future research.

Good!

Again, the yellow is not very visible

I know there are figure captions for each graph, but you should also have a small summarization at the end of each section (1.4.2, 1.4.3, etc) that motivates why you chose certain variables and explains your results a bit.

I'm not loving the color choice here it is not very visible on a white background. Some people might have dark mode but it should be visible in both modes.

Graph title?

After this section, you should include a small paragraph explaining your preprocessing (2-3 sentences maybe). Generally no need to explain your library imports, but you should give some broad info on what all your variables cover.

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Reply to the reviewers

The authors do not wish to provide a response at this time.

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Referee #4

Evidence, reproducibility and clarity

Overall, the authors show an interesting and conclusive work on the activation of ERM proteins upon TBXA2R signaling. The use of the ebBRET biosensor to assess ERM-protein activation enables elegant investigation of activation modalities. The Thromboxane A2 analogue U46619 robustly shows activation of ERM proteins in ebBRET assays as well as an increase in ERM-protein phosphorylation status. The functional effects of this signaling pathway are shown convincingly for moesin, where moesin mediates an TBXA2R mediated increase in cell motility, invasion and metastasis of triple-negative breast cancer Hs578 cells in vitro and in vivo. Nonetheless, some points need to be clarified.

Significance

Comment 1: In the title the authors state, that ERM-activation via TBXA2R is controlling invasion and motility of triple-negative breast cancer cells. In the manuscript, there is only data supporting this assumption for moesin (MSN). Therefore, the authors need to change the title accordingly or support additional experiments for the other two ERM-proteins radixin and ezrin. Throughout the experiments, the p-ERM antibody is used to measure ERM-protein activation. Since the effects on invasion and motility observed in Hs578 cells are mainly mediated through moesin, it would be necessary to see, at least for one experiment per cell line (HEK293T, Hs578) the detailed phosphorylation status of ezrin, radixin and moesin separately. As there are specific, phospho-detecting antibodies for this case, this could be done rather easy. Furthermore, showing specific increase of phosphorylated moesin would support the functional data shown in Figure 5 and 6. To investigate the functional effect of TBXA2R mediated activation of ezrin and radixin on cell motility and invasion, similar experiments could be done in e.g. HMC-1-8 breast cancer cells (high ezrin expression) and HCC1187 (high radixin expression).

Comment 2: Figure 1A, C, D: The concentration of staurosporine is with 100 nM relatively high for kinase inhibition. It would be informative to see the assay with increasing staurosporine concentrations, e.g. from 1 nM to 50 nM. In general, a concentration of 1-10 nM should be sufficient for kinase inhibition, preventing unspecific effects of the drug.

Comment 3: The citation for the p-ERM antibody is confusing, as there is only p-Moe used in the cited paper (Roubinet, 2011). There is a p-ERM antibody commercially available (Cell Signaling, Phospho-ezrin (Thr567)/radixin (Thr564)/moesin (Thr558) Antibody #3141). Could you clarify which antibody you are using?

Comment 4: From the inhibitor experiments using C3 transferase toxin (Figure 2), the authors conclude that RhoA plays a role in TBXA2R mediated ERM activation. As mentioned in the manufacturer's description, C3 toxin is inhibiting RhoA, RhoB and RhoC. Therefore, it would be necessary to repeat those experiments under RhoA knockdown conditions (e.g. using an siRNA-based approach) to state that specifically RhoA is involved.

Comment 5: To assess, if the findings in Figure 5 and 6 are due to the higher moesin expression in Hs578 cells or are linked to a specific function of moesin, a re-expression experiment would be informative. To achieve this, the 2D and 3D migration experiments could be redone after re-expression of moesin, ezrin and radixin separately in moesin knockdown conditions.

Minor comments:

• Even though U46619 is a known Thromboxane A2 analogue, including negative and positive controls would strengthen the results. In detail, this could be done by showing a known protein which gets phosphorylated downstream of TBXA2R signaling and a protein which is not affected by this signaling pathway alongside the shown effects on ERM-proteins.
• Figure 1 J: There are no statistics comparing the conditions of SQ-29548 treated cells in presence/absence of U46619, that should be added.
• Figure 1 G, H: How was the quantification for cell periphery performed? In detail, how were the thresholds set for cell periphery / not cell periphery?
• Figure 3 H:
  • The labelling indicating presence of U46619 is missing.
  • Also, what is the rationale behind normalizing MB-453 for 3 cell lines and comparing the BT-549 to MB-157?
• Suppl. Fig 4 D: Define y-axis better. Absorbance at what wave length?
• Define FERM and ERMAD abbreviations in introduction.

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Referee #3

Evidence, reproducibility and clarity

Summary

The Ezrin, radixin, and moesin (ERM) family of proteins orchestrate morphological changes that potentiate metastatic invasion in cancer cells. In this study, Leguay et al. identify the GPCR, TBXA2R, as a key activator of the ERM proteins which promotes motility and invasion in triple-negative breast cancer (TNBC) cells. Using BRET-based sensors developed by them previously for monitoring the activation of ERM proteins and building upon their previous findings on the role of the small GTPase RhoA in the activation of ERM proteins, the authors carefully dissect the molecular pathway leading to the activation of ERM proteins upon stimulation of the TBX2AR. The authors also establish the pathological relevance of the pathway in TNBC using in vitro and in vivo models, opening up possibilities for targeting this pathway in cancer cells. Overall, the study is well-conceived and executed, and the results are clearly described and presented in the manuscript. However, the following comments must be addressed before publication.

Major comments

Fig 1C - Why p-ERM was normalized over Ezrin and not ERM? It would be more appropriate and consistent to normalize against the ERM signal as done in other experiments in the manuscript.

Fig 1E and S3C - The levels of total ERM also seem to change with increasing treatment times. This must be clarified and discussed in the manuscript.

Fig 1F - Why is the mean of all three independent experiments not presented here as in S3C?

Fig 2E - Though SLK seems to play a dominant role in the phosphorylation of ERM in HEK293T cells, the depletion of LOK also substantially reduces the phosphorylation of ERM in the representative figure (Fig 2E), which is not reflected in the quantification (Fig 2F). Indeed, both SLK and LOK seem to be equally crucial in Hs578T cells (Fig 4I), unlike the conclusion here. The authors must check if the quantifications were affected by any white spots in the blot for total ERM as seen in the representative figure. If necessary, the authors must include additional replicates, and the model in Fig 2G should be updated accordingly. If the contributions of LOK are indeed quite minimal in HEK293T cells, then the difference in Hs578T cells must be adequately highlighted and discussed rather than broadly mentioning similar results were observed in both cell lines. The discussion mentions that SLK kinases are the only kinases needed for ERM activation, which conflicts with findings from Hs578T cells, where both SLK and LOK contribute to ERM phosphorylation (Fig 4I). The authors should revise this to reflect their data accurately.

Minor comments

FigS3B should cite the source dataset and not just the database. Also, details of how the extracted data was processed (if any) should be described clearly.

When multiple treatments are involved (for, e.g. U46619 and staurosporine), the exact sequence of treatments and the overlap in timings of different treatments must be clearly mentioned. E.g. fig 1A and 1C. There are a few grammatical errors which need to be fixed. E.g. Paragraph 2 in the second section of results - We next aimed to identify (not identifying) which kinase(s) acts downstream of TBX2AR

Significance

Triple-negative breast cancer, which is characterized by a lack of estrogen, progesterone or HER2 receptors, is a highly metastatic and aggressive form of breast cancer with poor prognosis. Currently, there are fewer treatment options than other types of invasive breast cancer. The current study opens up the possibility of targeting the TBXA2R or the downstream signalling components in TNBC, which are still expressed in TNBC cells. However, certain TNBC sub-types express low levels of p-ERM and TBX2AR (Fig 3E, 3F), indicating a minor role for TBX2AR pathway and targeting this pathway in these subtypes may be inefficient. In addition, certain subtypes express high p-ERM and low TBX2AR indicating alternative pathways for ERM activation. Currently, it is not clear which other GPCRs can contribute to ERM activation by engaging similar downstream effectors. A comprehensive screening of different GPCR antagonists could identify alternative strategies to target the ERM-mediated metastasis in TNBC cells that show low expression of TBX2AR.

Audience The manuscript is relevant to a broad audience, especially to cell biologists, cancer biologists and clinical scientists.

The reviewer's field of expertise includes cell signaling, gene expression, and RNA biology in mammalian systems. Moderate expertise in cancer biology. Limited knowledge of histopathological analysis.

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Referee #2

Evidence, reproducibility and clarity

Leguay et al present an interesting and logical series studies that investigate the activity and signaling of the GPCR TBXA2R in TNBC cells. The premise of the overall study is that metastasis is often associated with a more invasive/motile cancer cell phenotype. The investigators have an interest in ERM (Ezrin, Radixin, Moesin) proteins, which have been implicated in cell motility. The authors link stimulation of TBXAR2, a GPCR, to activation of ERM proteins and also show that TBXAR2 is associated with worse outcome in TNBC patients. Through the use of genetic and pharmacologic tools the authors provide convincing biochemical and cell based data to support their model that stimulation of TBXAR2 activates Gα11 & Gα12/13 which subsequently stimulate RhoA and SLK/LOK which then phosphorylate ERMs. The authors show relevant biologic consequences of the pathway. Data include orthogonal assays with similar results and the manuscript is written clearly and the data are displayed well. Overall it is a solid story that is largely well done. There are a few comments that should be addressed.

Comments:

1. All the biochemical/cell based in vitro data exploit the use of small molecule agonists of TBXAR2, not the natural ligand. A comment on this and why use of TXA2 is not feasible would be helpful to the reader.
2. The data in figures 1-5 are solid and clear. However, I suggest adding a higher magnification inset for the IHC images shown in Fig 3E. It would be useful to be able to distinguish cells in the IHC, a higher mag shot should suffice.
3. A) The use of Hs578t cells for the in vivo modeling is unfortunate. Additionally, the use of iv injection to in a study focused on cell invasion is also unfortunate. The metastatic propensity of Hs578t is not clear, in fact a recent report comparing metastasis in breast cancer cell lines shows that Hs578t perform poorly in terms of metastasis after orthotopic injection (see PMID 38468326). I searched the literature a bit to try and find other examples of iv injection of Hs578t cells, I found 1 (PMID:27654855, I did not search exhaustively), this paper shows significant lung metastasis and does not mention liver metastases. Were other breast cancer cells investigated for the in vivo studies?

B) Why I was interested is because the typical organ that is seeded post iv injection is the lungs (as seen in the above ref), liver metastases post iv injection are not common, especially with breast cancer cells. What did the lungs look like in your experiments?

C) Further while the data presented in figure 6 are supportive of the overall conclusions, the data is modest at best in terms of metastatic burden. Repetition of the experiment using a breast cancer cell line injected orthotopically would likely be more useful in highlighting the importance of the pathway to metastasis. <br /> I understand performing an orthotopic assay may be outside the scope of the study, but it would provide greater impact given the focus of the paper on cell invasion.

Cross-commenting

I think reviewer comments are generally aligned. I was least critical but appreciate the concerns of the other reviewers, especially rev #1 who requested additional validation and controls. In my opinion in vivo studies are not robust, I expect that is due to cell line choice. Repetition of the in vivo study with a breast cancer cell line that is capable of metastasis (from a primary tumor) would be more effective.

Significance

The manuscript presents a solid, logical flow and the biochemical/cell based in vitro data are clean. Clear differences between groups, appropriate controls, and displayed effectively.

The challenge is the in vivo study. IV injection of cancer cells is a valid model for seeding and growing in a target organ BUT it does not reflect cell invasion, which is typically thought of as a step that occurs earlier in the metastatic cascade. That said, the data are supportive with conclusions but not necessarily consistent with expected results based on iv injection of this cell line. A caveat is that the cell line used is characterized as having metastatic characteristics in vitro but is not a consistent metastatic line in vivo. The recommendation is the perform a new in vivo experiment. An orthotopic injection of a strongly metastatic cell line, such as MDA MB 231 or other (see paper ref aboved) would be a more stringent and accurate test of the importance of the pathway to cell invasion in vivo.

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Referee #1

Evidence, reproducibility and clarity

Summary

This manuscript investigates the role of the thromboxane A2 receptor (TBXA2R) in activating ERM (ezrin, radixin, and moesin) proteins to promote cell motility and invasion in triple-negative breast cancer (TNBC) cells. Using TBXA2R stimulation and a series of in vitro and in vivo experiments, the authors report that ERM activation is mediated through a TBXA2R signaling pathway involving Gαq/11 and Gα12/13 subunits, RhoA, and SLK/LOK kinases. They propose that this pathway enhances cell migration, invasion, and metastatic potential in TNBC.

General criticisms

Experimental design and analyses are adequate, even though certain experiments lack appropriate controls or employ the wrong statistical tests. However, the study primarily relies on a single TNBC cell line and heavy use of overexpression systems and/or small molecule inhibitors, raising concerns about the generalizability and specificity of the findings. Furthermore, several conclusions appear premature and unsupported by the current data. Critical controls and additional validation experiments are necessary to support the claims about the role of TBXA2R in metastasis and to justify the strong mechanistic conclusions drawn.

Specific criticisms

Figure 1

TBXA2R expression should be shown to understand whether different ebBRET signals are dependent on the overexpression levels of TBXA2R.

E-F: As ERM levels change over time, one would like to understand whether this is due to misloading or whether there is an underlying biological event going on in the stimulated cells. Are total ERM levels really changing over time? Please add a blot for 1-2 housekeeping proteins as loading controls. This is also crucial to clarify the kinetics of ERM activation; such notable intensity variations make quantifications of non-linear WB signals not fully reliable. In F, mean and SD should be plotted.

G: The authors need to use a PM marker if they want to claim that pERM increases at the cell cortex. TBXA2R localization should also be shown.

Figure 2

A: This reviewer cannot see the purported partial inhibition in Ga12/13 KO cells. Are differences between the two KOs significant? Furthermore, there are reports indicating that YM-254890 may not be specific for Gaq. Experiments on double KO cells are needed to assess the possible redundancy between the two Ga subfamilies. C-D: it is important to add a positive control for the activity of Y-27632 in these experiments. Please show that a ROCK-dependent effect is inhibited in the treated cells. G: The working model is premature as it is unknown whether ROCKi was active. While asking for ROCK1/2 KO cells would be too much, this claim is far-fetched.

Figure 3

B: In the legend, it is not clear what grey and light read colours mark. E-F: This reviewer finds it difficult to believe that p-ERM and TBXA2R signal intensities at the cell cortex could be reliably quantified using IHC images. The representative samples would indicate that p-ERM and TBXA2R positivity are not correlated. It would be crucial to show examples for each of the TNBC subgroups the existence of which is inferred based on p-ERM and TBXA2R staining. The conclusion that "no TNBC samples exhibited high TBXA2R expression and low levels of p-ERMs, further supporting a role for TBXA2R signalling in ERM activation in TNBC" is an overstatement.

Figure 4

The authors wrote that "We focused on the Hs578T cell line, which showed a median level of TBXA2R mRNA expression among the six TNBC cell lines tested". I do not understand the rationale for it as anti-TBXA2R antibodies detecting endogenous TBXA2R are available and thus why not use the median protein levels?

Figure 5

Effects of the knockouts are subtle, and rescue experiments would be needed to corroborate these results. The employed statistical analysis is prone to overestimating differences. The authors should use the superplots instead. The authors might also decide to use other TNBC cell lines to explore the functional relevance of this pathway in BC progression. This is particularly important because Hs578T are poorly tumorigenic, and they often do not form palpable tumours in mice.

Figure 6

The fact that Hs578T are poorly tumorigenic in mice is likely the reason why the authors used the experimental metastasis model. However, it is puzzling that metastases were studied in the liver but not in the lungs. Furthermore, the whole approach is rather artefactual as the TBXA2R agonist was administered for the entire duration of these experiments. What is the pathological relevance of such a study? Including a spontaneous metastasis model or alternative TNBC lines that mimic human disease more closely would help strengthen the functional relevance of this pathway in BC progression and study's translational relevance.

Figure S2

B-M: the pERM signal appears to be perinuclear in some of the tested cell lines. Please use a PM marker.

Figure S3

The authors should use the superplots to analyse the cell migration data.

Discussion

The claim that "our findings demonstrated that kinases of the SLK family are the only kinases needed for ERM activation by TBXA2R" should be tuned down as only 2 cell lines were tested. In this section, the authors should also discuss the proposed pro-metastatic functions of TXA2 and TXA2R in more detail, including vascular permeability. The sweeping conclusion that "TBXA2R expression correlates with phosphorylation and activation of ERMs in TNBC patient samples" clashes with the authors' own results; please stick to the data.

Concluding remarks

This study investigates a signaling pathway whereby TBXA2R thorugh ERM activation enhances the migratory and invasive potential of TNBC cells. However, several improvements are needed to support the main claims. The dependence on a single TNBC cell line, reliance on pharmacological inhibitors with potential off-target effects, and limited in vivo relevance detract from the generalizability of the findings. Additional TNBC models, adeguate controls, and a broader focus on natural metastasis patterns would make the conclusions more compelling. Moderating certain overstated claims would be needed to align the interpretations with the actual data.

Cross-commenting

I found comments in the other reviewers' reports that align with my criticisms on the mouse experiments as well as with those pertaining to the tissue culture work.

Significance

General comments

The manuscript investigates the role of TBXA2R in the regulation of ERM in the context of TNBC metastasis. Much of this TBXA2R signalling axis is already known, as well as that SLK and LOK can phosphorylate ERM in other cell systems. Similarly, the positive role of ERM in cell migration/invasion and cancer progression has long been reported. The somewhat unexpected finding that ERM phosphorylation is independent of ROCK remains not fully convincing. The BC-related part is problematic as the continuous administration a TBXA2R agonist is required for key tumour metrics to show some differences in vivo. This calls into question the main conclusion of the work, namely that the TBXA2R/ERM-dependent pathway is activated during BC progression in TNBC cells.

Audience

Specialists interested in GPCRs and signal transduction or in the cytoskeleton.

Expertise

Rev: cancer cell biology, signal transduction, cytoskeleton, actin biochemistry, multiplexed imaging, mouse model of human diseases.

Co-rev: nanoparticles, cell biology.

Healthy communities require intentional stewardship. leadership is not removed, but distributed and relational.

Education is most meaningful when connected to real practice. CoPs promote authentic, situated learning instead of abstract instruction.

CoPs can act as bridges, transferring knowledge where silos would normally block collaboration.

Learning happens by participating with others not only by listening to an expert. Knowledge is embodied, demonstrated, socially distributed.

Es interesante porque permitir realizar una evaluacion individual.

Version 3 of this preprint has been peer-reviewed and recommended by Peer Community in Genomics.<br /> See the peer reviews and the recommendation.

eLife Assessment

This study provides solid evidence that odor fear conditioning biases olfactory sensory neuron receptor choice in mice and that this bias is detectable in the next generation. The authors use rigorous histological and behavioral analyses, including unsupervised behavioral quantification, to support the conclusion that odor-specific sensory representations can be shaped by experience and partially transmitted across generations. While the behavioral effects in offspring are modest and the mechanistic basis of inheritance remains unresolved, the study offers an important and carefully executed contribution to understanding experience-dependent sensory plasticity and its intergenerational consequences.

Reviewer #1 (Public review):

Summary

The revised manuscript by Liff et al. represents a substantial improvement over the original version. The authors have carefully addressed the key concerns raised in the initial review, most notably by expanding their behavioral analyses and incorporating additional experiments that strengthen the mechanistic links between olfactory sensory neuron (OSN) changes and behavioral outcomes. Their integration of unsupervised Keypoint-MoSeq analysis, extended behavioral metrics (distance travelled, mean speed, freezing time), and the inclusion of behavioral results in the main figures significantly enhance the clarity and impact of the work. The revised discussion also better contextualizes the findings in relation to previous literature, including the discrepancies with Dias & Ressler (2014), and provides more transparency regarding experimental choices.

Overall Evaluation

The revised version has substantially strengthened the manuscript. By addressing the initial concerns with new data, improved analyses, and clearer discussion, the authors provide a much more compelling and rigorous account of how odor-shock conditioning biases OSN fate and influences offspring. Although some questions remain open for future exploration, the present study now makes a clear, well-supported contribution to understanding intergenerational sensory inheritance. I commend the authors for their thoughtful and thorough revisions.

Strengths

Expanded behavioral analysis: The addition of multiple quantitative metrics, inclusion of freezing behavior, and use of Keypoint-MoSeq provide a much richer characterization of behavioral phenotypes in both F0 and F1 generations. These data convincingly demonstrate nuanced odor-specific effects that were not captured in the earlier version.

Improved presentation: Behavioral data, previously relegated to supplementary materials, are now appropriately included in the main figures, supported by supplementary statistical tables. This makes the results more transparent and accessible.

Potential Limitations

Some behavioral effects in the F1 generation remain subtle; the discussion addresses this, but a cautious interpretation of behavioral inheritance would be appropriate.

The MoSeq analysis is a valuable addition, though clarifying what "syllables" represent and how they relate to traditional behavioral measures could aid reader interpretation.

Reviewer #2 (Public review):

Summary:

The authors examined inherited changes to the olfactory epithelium produced by odor-shock pairings. The manuscript demonstrates that odor fear conditioning biases olfactory bulb neurogenesis toward more production of the olfactory sensory neurons engaged by the odor-shock paring. Further the manuscript reveals that this bias remains in first generation male and female progeny produced by trained parents. Surprisingly, there was a disconnect between increased morphology of the olfactory epithelium for the conditioned odor and the response to odor presentation. The expectation based on previous literature and the morphological results were that F1 progeny would also show an aversion to the odor stimulus. However, the authors found that F1 progeny were not more sensitive to the odor compared to littermate controls

Strengths:

The manuscript includes conceptual innovation and some technical innovation. The results validate previous findings that were deemed controversial in the field, which is a major strength of the work. Moreover, these studies were conducted using a combination of genetically modified animals and state-of-the-art imaging techniques, highlighting the rigorous nature of the research. Lastly, the authors provide novel mechanistic details regarding the remodeling of the olfactory epithelium, demonstrating that biased neurogenesis, as opposed to changes in survival rates, account for the increase in odorant receptors after training.

Weaknesses:

The main weakness is the disconnect between the morphological changes reported and the lack of change in aversion to the odorant in F1 progeny. The authors also do not address the mechanisms underlying the inheritance of the phenotype, which may lie outside of the scope of the present study.

Reviewer #3 (Public review):

Liff et al. have made considerable effort to improve their manuscript. In their revised manuscript, the authors have substantiated their claims of intergenerationally inherited changes in the olfactory system in response to odor-dependent fear conditioning. Several new experiments and analyses now strengthen this study.

I still find that the statement that the study provides "insight into the heritability of acquired phenotypes" is somewhat misleading. In their response to this initially raised point the authors correctly point out that their "results provide basic knowledge that will accelerate our ability to uncover the mechanisms driving heritable changes." That said, current "insights" are not mechanistic in nature.

Author response:

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

Reviewer #1 (Public Review):

(1) Discrepancies with previous findings need clarification, especially regarding the absence of similar behavioral effects in F1. Lack of discussion on the decision to modify paradigms instead of using the same model. Presentation of behavioral data in supplementary materials, with a recommendation to include behavioral quantification in main figures. Absence of quantification for freezing behavior, a crucial measure in fear conditioning.

We agree, thank you. One of the major revisions we have made to this version of the manuscript is the addition of much more thorough analysis of our F1 behavior. While not captured by the (relatively gross) measure of the approach-avoid index, further analysis has highlighted interesting differences between the F1s of unpaired and paired offspring, and in an odor-specific manner. As these analyses have given rise to many new results and conclusions, we have attempted to adjust the manuscript to reflect the major change that we do, in fact, find effects in F1, if subtle. 

Classical odor-shock pairing was used in both Dias & Ressler’s and our study to directly expand upon the findings of increase in cell number. This enabled our discovery of biasing of newborn OSNs. For our behavioral readouts, we chose to focus on the ethological behavior of avoidance. From our extensive behavioral analysis (Figures 5 & 6), we successfully identified several behavioral differences in the F1 offspring that had not previously been described.

Reviewer #2 (Public Review):

(1) The main weakness is the disconnect between the morphological changes reported and the lack of change in aversion to the odorant in F1 progeny. The authors also do not address the mechanisms underlying the inheritance of the phenotype, which may lie outside of the scope of the present study.

Thank you for your comments. Our revised manuscript includes both new experiments and new analyses that probe the relationship between a change in cell number and a change in avoidance behavior, and we have revised the manuscript text to address this point directly. In short, we find both in the F0 generation (at extended time points) and in the F1, that an increase in cell number does not always correlate with avoidance behavior. However, we do find nuanced behavioral differences between the offspring of unpaired and paired fathers. Whether the increase in cell number in offspring is necessary to observe the behavioral changes is outside the scope of the current study, but certainly a question we are interested in answering in future work. 

Reviewer #3 (Public Review):

(1) In the abstract / summary, the authors raise expectations that are not supported by the data. For example, it is claimed that "increases in F0 were due to biased stem cell receptor choice." While an active field of study that has seen remarkable progress in the past decade, olfactory receptor gene choice and its relevant timing in particular is still unresolved. Here, Liff et al., do not pinpoint at what stage during differentiation the "biased choice" is made. 

EdU is only taken into stem cells in the S phase, and differences in EdU-labeled M71 or MOR23 OSNs across fear conditioning groups indicates a biasing in subtype identity. We do not make claims regarding the exact stage of OSN maturation at which biasing may occur; rather, we demonstrate that the stem cells that were dividing during EdU administration are more likely to mature into an M71 OSN if a mouse receives paired acetophenone conditioning compared to unpaired or no conditioning (and similarly with MOR23 and lyral). This phenomenon must involve receptor choice, as that is the mechanism by which OSN subtypes form. 

(2) Similarly, the concluding statement that the study provides "insight into the heritability of acquired phenotypes" is somewhat misleading. The experiments do not address the mechanisms underlying heritability. 

We do not claim to provide direct insight into the mechanisms underlying heritability. Our experiments do provide insight into the heritability of acquired phenotypes, as we corroborate previous studies that this olfactory fear conditioning paradigm induces heritable changes in the nose and in behavior. We also demonstrate odor-specific behavioral differences in the offspring conditioned fathers, suggesting that the mechanisms underlying the specific behavioral phenotypes may be unique to the conditioning odorant, and not one universal mechanism. These results provide basic knowledge that will accelerate our ability to uncover the mechanisms driving heritable changes. 

(3) The statement that "the percentage of newborn M71 cells is 4-5 times that of MOR23 may simply reflect differences in the birth rates of the two cell populations" should, if true, result in similar differences in the occurrence of mature OSNs with either receptor identity. According to Fig. 1H & J, however, this is not the case. 

We have removed that statement from the manuscript, as subtype-specific differences in proliferation rates are not the focus of this study and we do not wish to make claims about it based on our EdU experiments. We do not compare our iDISCO cell density counts to EdU co-labeling counts nor ratio counts, as differences between M71 and MOR23 quantification in cleared tissue versus EdU uptake may simply reflect the inherent differences between methodologies. Our claims are solely within M71 cohorts and MOR23 cohorts. 

(4) An important result is that Liff et al., in contrast to results from other studies, "do not observe the inheritance of odor-evoked aversion to the conditioned odor in the F1 generation." This discrepancy needs to be discussed. 

This is discussed in the manuscript, and we report behavioral differences revealed by additional analyses. 

(5) The authors speculate that "the increase in neurons responsive to the conditioned odor could enhance the sensitivity to, or the discrimination of, the paired odor in F0 and F1. This would enable the F1 population to learn that odor predicts shock with fewer training cycles or less odorant when trained with the conditioned odor." This is a fascinating idea that, in fact, could have been readily tested by Liff and coworkers. If this hypothesis were found true, this would substantially enhance the impact of the study for the field.

We agree that additional F1 behavioral paradigms are a major next step to understand the functional behavioral differences that may emerge from an increase in specific OSN subtype. Due to the nontrivial amount of time and effort it requires to generate F1 offspring (on the order of many months), and because we do not test individual offspring in multiple behavioral assays (such that they are naïve to their father’s conditioning odor), these experiments are outside the scope of this current study. 

Reviewer #1 (Recommendations For The Authors):

(1) Considering that the authors are expanding upon the previous findings of Dias and Ressler (2014), it is crucial to clarify the discrepancies in the results between both works in the discussion. While I acknowledge the use of a different experimental design by the authors, if the premise assumes there is a universal mechanism for transgenerational acquired modification it prompts the question: Why don't we observe similar behavioral effects in F1 in the present model? This issue needs extensive discussion in the manuscript to advance the field's understanding of this topic. Additionally, I am also curious about the author's decision to modify the paradigms instead of using exactly the same model to further extend their findings on stem cells, for example. Could you please provide comments on this choice and elaborate on this aspect in the discussion? 

We agree, thank you. One of the major revisions we have made to this version of the manuscript is the addition of much more thorough analysis of our F1 behavior. While not captured by the (relatively gross) measure of the approach-avoid index, further analysis has highlighted interesting differences between the F1s of unpaired and paired offspring, and in an odor-specific manner. As these analyses have given rise to many new results and conclusions, we have attempted to adjust the manuscript to reflect the major change that we do, in fact, find effects in F1, if subtle. 

Classical odor-shock pairing was used in both Dias & Ressler’s and our study to directly expand upon the findings of increase in cell number. This enabled our discovery of biasing of newborn OSNs. For our behavioral readouts, we chose to focus on the ethological behavior of avoidance. From our extensive behavioral analysis (Figures 5 & 6), we successfully identified several behavioral differences in the F1 offspring that had not previously been described. We have revised the discussion section to elaborate on these decisions.

We incorporated the behavioral data into the main figures and included a freezing metric to Figure 5 (F, J, & N). We did do an analysis of time spent freezing in the control vs. conditioned chamber, but since the F0 paired mice spend so little time in the conditioned odor chamber, they also spend most of their time freezing in the control odor chamber. Thus, we felt it was better to show the overall time spent freezing during the trial.

(2) It is unclear why the authors chose to present all behavioral data to supplementary materials. I strongly recommend not only incorporating the behavioral data into the main figures but also expanding the behavioral quantification. It appears that the author dismissed the potential effects on F1 without a thorough exploration of animals' behaviors. The task contains valuable information that could be further investigated, potentially altering the findings or even the conclusions of the study. Notably, the absence of quantification for freezing behavior is incomprehensive. Freezing is a crucial measure in fear conditioning, and it's surprising that the authors did not mention it throughout the manuscript. I encourage the author to include freezing data in the analysis and other behavioral quantification as follows: a) freezing during odor presentation and ITI for conditioning days. b) freezing during odor preference test in all compartments. c) it is not very clear the design of the Odor preference behavioral testing. Is the odor presented in a discrete manner or the order is constantly presented in the compartment? Could the authors quantify the latency to avoid after the visit in the compartment? d) in the video it is very clear the animals are doing a lot of risk assessment, this could be also analyzed and included as a fear measure.  

Thanks for the suggestion. We incorporated the behavioral data into the main figures and included a freezing metric to Figure 5 (F, J, & N). We did do an analysis of time spent freezing in the control vs. conditioned chamber, but since the F0 paired mice spend so little time in the conditioned odor chamber, they also spend most of their time freezing in the control odor chamber. Thus, we felt it was better to show the overall time spent freezing during the trial. In the methods section we describe that the odor is continuously bubbled into the chamber throughout the trial, but we have clarified this in the main text as well. As for further behavioral metrics like latencies and risk assessment, initial analyses have not shown anything in the F1 data that we wished to report here. Future work from the lab will investigate this further.

(3) In the Dias and Ressler paper, a crucial difference exists between the models that could elucidate the absence of transgenerational effects on F1. In their study, the presence of the unconditioned stimulus (US) is consistent across all generations in the startle task. I am curious whether, in the present study, the authors considered pairing the F1 with a US-paired task in a protocol that does not induce fear conditioning (e.g., lower shock intensity or fewer pairings). Could this potentially lead to an increased response in the parental-paired offspring? Did the author consider this approach? I understand how extensive this experiment can be, therefore I'm not directly requesting, although it would be a fantastic achievement if the results are positive. Please consider discussing this fundamental difference in the manuscript. 

To clarify, the F1 generation is presented with the unconditioned stimulus, just never conditioned with it. In these experiments, we were primarily interested in the F1’s naïve reaction to their father’s conditioning odorant, and whether the presentation of that odor in the absence of a stressor would lead to any fear-like behavioral responses.

We have considered the experiments you have suggested and have ongoing projects in the lab further investigating F1 effects and whether their father’s experiences affect their ability to learn in conditioning tasks. Because of the amount of time and effort it requires to generate F1 offspring, and because we do not wish to test individual offspring in multiple assays, we do not present any of these experiments in the current manuscript. Ongoing work is looking into whether 1-day (vs. 3-day) conditioning is sufficient in the offspring of paired mice, and we appreciate the suggestion of subthreshold shock intensity. We will also clarify in the discussion that future work will try to answer these questions. 

(4) If the videos were combined it would be better to appreciate the behavioral differences of paired vs unpaired. 

Thank you for the suggestion, fixed. Video S1 is now a combination of unpaired and paired example videos. 

(5) Figure 3E, is there an outlier in the paired group that is driving the difference? Please run an outlier test on the data if this has not been done. If already done, please express the stats. 

We ran an outlier test using the ROUT method (Q=1%) and did not find any outliers to be removed. We also ran the same test on all other data and removed one mouse from the Acetophenone F1 Paired group in Figure 5 (also described in the Methods section). 

(6) I understand that using the term "olfactory" twice in the title may seem redundant. However, the authors specifically demonstrate the effects of olfactory fear conditioning. I suggest including "odor-induced" before "fear conditioning" in the title for greater specificity and accuracy. This modification would better reflect the study's focus on olfactory fear conditioning, especially given the authors did not explore fear conditioning broadly (e.g., contextual, and auditory aspects were not examined). 

Thank you for your feedback. We found “olfactory” twice as cumbersome. We have changed the title to “Fear conditioning biases olfactory sensory neuron expression across generations”, to more accurately highlight the importance of the olfactory sensory neuron expression, intergenerationally. 

(7) The last page of the manuscript has a list of videos (8 videos), but only two were presented.

We have made sure to include all 7 videos (videos 1 and 2 were combined) in this version.  

Reviewer #2 (Recommendations For The Authors):

(1) The analyses mentioned on lines 210-220 should be presented. 

Thank you for the suggestion. We have removed this part of the manuscript as we do not have a large enough n to draw conclusions about cell longevity in this paper. Future studies in the lab will incorporate this analysis.

Reviewer #3 (Recommendations For The Authors):

(1) The manuscript contains several supplementary figures and movies that are not referred to in the main text. 

All supplementary figures and movies are now referred to in the manuscript text.

(2) In the abstract, the authors state that they "investigated changes in the morphology of the olfactory epithelium." I think that is (technically) not what they did. In fact, the authors do not show any morphometry of the epithelium (e.g., thickness, layers, etc.), but count the density of OSNs that share a specific receptor identity. Along the same lines, the authors state in the abstract that recent work has shown that conditioning is "resulting in increases in olfactory receptor frequencies." However, recent studies did not show increased "receptor frequencies", but changes in cell count. Whether (or not) receptor expression per OSN is also changed remains unknown (would be interesting though). 

Yes, agreed. We changed “morphology” to “cellular composition.” We also changed any references to “receptor frequencies” to “olfactory sensory neuron frequencies.”

(3) Reference 20 needs to be updated. 

Thank you, updated.

(4) l.52: the distribution of OSNs into (four) zones is a somewhat outdated concept as zonal boundaries are rather blurry. Generally, of course, dorsoventral differences are real. 

Yes, we agree and changed the verbiage to “region” as opposed to “zone.” We mainly bring this up because it later becomes relevant that both M71 and MOR23 are expressed in the same (antero-dorsal) region and thus can be quantified with the same methodology.

(5) Fig. 3B & C: the EdU background staining is quite peculiar. Any reason why the epithelium is mostly (with the sustentacular nuclei being a noticeable exception) devoid of background? 

We use the ThermoFisher Click-iT Plus EdU kit (Invitrogen, C10638) and it has consistently produced very good signal to noise ratio.

Responses to Editor’s note

We thank the editor for their constructive suggestions. 

(1) Should you choose to revise your manuscript, please include full statistical reporting including exact p-values wherever possible alongside the summary statistics (test statistic and df) and 95% confidence intervals. These should be reported for all key questions and not only when the p-value is less than 0.05. 

Thank you for the suggestion. We created two supplementary tables with statistical reporting: Table S1 for the main figure statistics, and Table S2 for the supplementary figure statistics.

• erect_clitoris
• long_labia
• cameltoe

Reminded us about things like the shameful sinners trope -- in which people who have disabled children and say things like "Oh, I actually love them" sometimes get praised for how they treat disabled people

Contemporary conversations about disability including the over policing of disabled Black bodies

Inspirational overcomers trope

This reminds us of the conversation we'd had about tropes like the "bitter cripple"

These emphasize that it depends on the person and what they want to be called. This might connect to the reading about the "Glossary of Ableist Terms" & Simi Linton "Reassigning Meaning" about "nice words"

Connects to how the disabilities aren't always the problem, it's how society reacts to and views them -- social model

Invisible disabilities -- just because you can't see the disability doesn't mean it isn't there

"We're not here to talk about me, we're here to talk about poetry"

"We're not here to talk about me, we're here to talk about poetry"

"We're not here to talk about me, we're here to talk about poetry"

Certain presidents or politicans would hide their disabilities to avoid that being the main focus on them

Absence of a disability hierarchy -- disability often put under one framework, but really that framework only holds true in some ways, disability awareness is often seen as only one thing, but there's a lot under that umbrella term

Test

eLife Assessment

This important study demonstrates that some degree of spatial tuning (e.g., place cells) and ability to decode spatial location emerges in sufficiently complex systems trained to process visual information. This intriguing observation challenges existing approaches and findings used in the study of spatial navigation. However, the strength of evidence regarding the nature and quality of spatial tuning, its compatibility with experimental data, and the overall interpretation of the study remains incomplete. This work will be of interest to the research community of spatial navigation.

Reviewer #1 (Public review):

Summary:

This study investigated spatial representations in deep feedforward neural network models (DDNs) that were often used in solving vision tasks. The authors create a three-dimensional virtual environment, and let a simulated agent randomly forage in a smaller two-dimensional square area. The agent "sees" images of the room within its field of view from different locations and heading directions. These images were processed by DDNs. Analyzing model neurons in DDNs, they found response properties similar to those of place cells, border cells and head direction cells in various layers of deep nets. A linear readout of network activity can decode key spatial variables. In addition, after removing neurons with strong place/border/head direction selectivity, one can still decode these spatial variables from remaining neurons in the DNNs. Based on these results, the authors argue that that the notion of functional cell types in spatial cognition is misleading.

Comments on the revision:

In the revision, the authors proposed that their model should be interpreted as a null model, rather than the actual model of the spatial navigation system in the brain. In the revision, the authors also argued that the criterion used in the place cell literature was arbitrary. However, the strength of the present work still depends on how well the null model can explain the experimental findings. It seems that currently the null model failed to explain important aspects of the response properties of different functional cell types in the hippocampus.

Strengths:

This paper contains interesting and original ideas, and I enjoy reading it. Most previous studies (e.g., Banino, Nature, 2018; Cueva & Wei, ICLR, 2018; Whittington et al, Cell, 2020) using deep network models to investigate spatial cognition mainly relied on velocity/head rotation inputs, rather than vision (but see Franzius, Sprekeler, Wiskott, PLoS Computational Biology, 2007). Here, the authors find that, under certain settings, visual inputs alone may contain enough information about the agent's location, head direction and distance to the boundary, and such information can be extracted by DNNs. This is an interesting observation from these models.

Weaknesses:

While the findings reported here are interesting, it is unclear whether they are the consequence of the specific model setting and how well they would generalize. Furthermore, I feel the results are over-interpreted. There are major gaps between the results actually shown and the claim about the "superfluousness of cell types in spatial cognition". Evidence directly supporting the overall conclusion seems to be weak at the moment.

Comments on the revision:

The authors showed that the results generalized to different types of networks. The results were generally robust to different types of deep network architectures. This partially addressed my concern. It remains unclear whether the findings would generalize across different types of environment. Regarding this point, the authors argued that the way how they constructed the environment was consistent with the typical experimental setting in studying spatial navigation system in rodents. After the revision, it remains unclear what the implications of the work is for the spatial navigation system in the brain, given that the null model neurons failed to reproduce certain key properties of place cells (although I agreed with the authors that examining such null models are useful and would encourage one to rethink about the approach used to study these neural systems).

Major concerns:

(1) The authors reported that, in their model setting, most neurons throughout the different layers of CNNs show strong spatial selectivity. This is interesting and perhaps also surprising. It would be useful to test/assess this prediction directly based on existing experimental results. It is possible that the particular 2-d virtual environment used is special. The results will be strengthened if similar results hold for other testing environments.

In particular, examining the pictures shown in Fig. 1A, it seems that local walls of the 'box' contain strong oriented features that are distinct across different views. Perhaps the response of oriented visual filters can leverage these features to uniquely determine the spatial variable. This is concerning because this is is a very specific setting that is unlikely to generalize.

[Updated after revision]: This concern is partially addressed in the revision. The authors argued that the way how they constructed the environment is consistent with the typical experimental setting in studying spatial navigation system in rodents.

(2) Previous experimental results suggest that various function cell types discovered in rodent navigation circuits persist in dark environments. If we take the modeling framework presented in this paper literally, the prediction would be that place cells/head direction cells should go away in darkness. This implies that key aspects of functional cell types in the spatial cognition are missing in the current modeling framework. This limitation needs to be addressed or explicitly discussed.

[Updated after revision]: The authors proposed that their model should be treated as a null model, instead of a candidate model for the brain's spatial navigation system. This clarification helps to better position this work. I would like to thank the authors for making this point explicit. However, this doesn't fully address the issues raised. The significance of the reported results still depend on how well the null model can explain the experimental findings. If the null model failed to explain important aspects of the firing properties of functional cell types, that would speak in favor of the usefulness of the concept of functional cell types.

(3) Place cells/border cell/ head direction cells are mostly studied in the rodent's brain. For rodents, it is not clear whether standard DNNs would be good models of their visual systems. It is likely that rodent visual system would not be as powerful in processing visual inputs as the DNNs used in this study.

[Updated after revision]: The authors didn't specifically address this. But clarifying their work as a null model partially addresses this concern.

(4) The overall claim that the functional cell types defined in spatial cognition are superfluous seems to be too strong based on the results reported here. The paper only studied a particular class of models, and arguably, the properties of these models have a major gap to those of real brains. Even though that, in the DNN models simulated in this particular virtual environment, (i) most model neurons have strong spatial selectivity; (ii) removing model neurons with the strongest spatial selectivity still retain substantial spatial information, why is this relevant to the brain? The neural circuits may operate in a very different regime. Perhaps a more reasonable interpretation of the results would be: these results raise the possibility that those strongly selective neurons observed in the brain may not be essential for encoding certain features, as something like this is observed in certain models. It is difficult to draw definitive conclusions about the brain based on the results reported.

[Updated after revision]: The authors clarified that their model should be interpreted as a null model. This partially addresses the concern raised here. However, some concerns remain- it remains unclear what new insights the current work offers in terms of understanding the spatial navigation systems. It seems that this work concerns more about the approach to studying the neural systems. Perhaps this point could be made even more clear.

Reviewer #3 (Public review):

Summary:

In this paper, the authors demonstrate the inevitability of the emergence of spatial information in sufficiently complex systems, even those that are only trained on object recognition (i.e. not a "spatial" system). As such, they present an important null hypothesis that should be taken into consideration for experimental design and data analysis of spatial tuning and its relevance for behavior.

Strengths:

The paper's strengths include the use of a large multi-layer network trained in a detailed visual environment. This illustrates an important message for the field: that spatial tuning can be a result of sensory processing. While this is a historically recognized and often-studied fact in experimental neuroscience, it is made more concrete with the use of a complex sensory network. Indeed, the manuscript is a cautionary tale for experimentalists and computational researchers alike against blindly applying and interpreting metrics without adequate controls. The addition of the deep network, i.e. the argument that sufficient processing increases the likelihood of such a confound, is a novel and important contribution.

Weaknesses:

However, the work has a number of significant weaknesses. Most notably: the spatial tuning that emerges is precisely that we would expect from visually-tuned neurons, and they do not engage with literature that controls for these confounds or compare the quality or degree of spatial tuning with neural data; the ability to linearly decode position from a large number of units is not a strong test of spatial cognition; and the authors make strong but unjustified claims as to the implications of their results in opposition to, as opposed to contributing to, work being done in the field.

The first weakness is that the degree and quality of spatial tuning that emerges in the network is not analyzed to the standards of evidence that have been used in well-controlled studies of spatial tuning in the brain. Specifically, the authors identify place cells, head direction cells, and border cells in their network, and their conjunctive combinations. However, these forms of tuning are the most easily confounded by visual responses, and it's unclear if their results will extend to observed forms of spatial tuning that are not.

For example, consider the head direction cells in Figure 3C. In addition to increased activity in some directions, these cells also have a high degree of spatial nonuniformity, suggesting they are responding to specific visual features of the environment. In contrast, the majority of HD cells in the brain are only very weakly spatially selective, if at all, once an animal's spatial occupancy is accounted for (Taube et al 1990, JNeurosci). While the preferred orientation of these cells are anchored to prominent visual cues, when they rotate with changing visual cues the entire head direction system rotates together (cells' relative orientation relationships are maintained, including those that encode directions facing AWAY from the moved cue), and thus these responses cannot be simply independent sensory-tuned cells responding to the sensory change) (Taube et al 1990 JNeurosci, Zugaro et al 2003 JNeurosci, Ajbi et al 2023).

As another example, the joint selectivity of detected border cells with head direction in Figure 3D suggests that they are "view of a wall from a specific angle" cells. In contrast, experimental work on border cells in the brain has demonstrated that these are robust to changes in the sensory input from the wall (e.g. van Wijngaarden et al 2020), or that many of them are are not directionally selective (Solstad et al 2008).

The most convincing evidence of "spurious" spatial tuning would be the emergence of HD-independent place cells in the network, however, these cells are a very small minority (in contrast to hippocampal data, Thompson and Best 1984 JNeurosci, Rich et al 2014 Science), the examples provided in Figure 3 are significantly more weakly tuned than those observed in the brain.

Indeed, the vast majority of tuned cells in the network are conjunctively selective for HD (Figure 3A). While this conjunctive tuning has been reported, many units in the hippocampus/entorhinal system are not strongly hd selective (Muller et al 1994 JNeurosci, Sangoli et al 2006 Science, Carpenter et al 2023 bioRxiv). Further, many studies have been done to test and understand the nature of sensory influence (e.g. Acharya et al 2016 Cell), and they tend to have a complex relationship with a variety of sensory cues, which cannot readily be explained by straightforward sensory processing (rev: Poucet et al 2000 Rev Neurosci, Plitt and Giocomo 2021 Nat Neuro). E.g. while some place cells are sometimes reported to be directionally selective, this directional selectivity is dependent on behavioral context (Markus et al 1995, JNeurosci), and emerges over time with familiarity to the environment (Navratiloua et al 2012 Front. Neural Circuits). Thus, the question is not whether spatially tuned cells are influenced by sensory information, but whether feed-forward sensory processing alone is sufficient to account for their observed turning properties and responses to sensory manipulations.

These issues indicate a more significant underlying issue of scientific methodology relating to the interpretation of their result and its impact on neuroscientific research. Specifically, in order to make strong claims about experimental data, it is not enough to show that a control (i.e. a null hypothesis) exists, one needs to demonstrate that experimental observations are quantitatively no better than that control.

Where the authors state that "In summary, complex networks that are not spatial systems, coupled with environmental input, appear sufficient to decode spatial information." what they have really shown is that it is possible to decode some degree of spatial information. This is a null hypothesis (that observations of spatial tuning do not reflect a "spatial system"), and the comparison must be made to experimental data to test if the so-called "spatial" networks in the brain have more cells with more reliable spatial info than a complex-visual control.

Further, the authors state that "Consistent with our view, we found no clear relationship between cell type distribution and spatial information in each layer. This raises the possibility that "spatial cells" do not play a pivotal role in spatial tasks as is broadly assumed." Indeed, this would raise such a possibility, if 1) the observations of their network were indeed quantitatively similar to the brain, and 2) the presence of these cells in the brain were the only evidence for their role in spatial tasks. However, 1) the authors have not shown this result in neural data, they've only noticed it in a network and mentioned the POSSIBILITY of a similar thing in the brain, and 2) the "assumption" of the role of spatially tuned cells in spatial tasks is not just from the observation of a few spatially tuned cells. But from many other experiments including causal manipulations (e.g. Robinson et al 2020 Cell, DeLauilleon et al 2015 Nat Neuro), which the authors conveniently ignore. Thus, I do not find their argument, as strongly stated as it is, to be well-supported.

An additional weakness is that linear decoding of position is not a measure of spatial cognition. The ability to decode position from a large number of weakly tuned cells is not surprising. However, based on this ability to decode, the authors claim that "'spatial' cells do not play a privileged role in spatial cognition". To justify this claim, the authors would need to use the network to perform e.g. spatial navigation tasks, then investigate the networks' ability to perform these tasks when tuned cells were lesioned.

Finally, I find a major weakness of the paper to be the framing of the results in opposition to, as opposed to contributing to, the study of spatially tuned cells. For example, the authors state that "If a perception system devoid of a spatial component demonstrates classically spatially-tuned unit representations, such as place, head-direction, and border cells, can "spatial cells" truly be regarded as 'spatial'?" Setting aside the issue of whether the perception system in question does indeed demonstrate spatially-tuned unit representations comparable to those in the brain, I ask "Why not?" This seems to be a semantic game of reading more into a name than is necessarily there. The names (place cells, grid cells, border cells, etc) describe an observation (that cells are observed to fire in certain areas of an animal's environment). They need not be a mechanistic claim (that space "causes" these cells to fire) or even, necessarily, a normative one (these cells are "for" spatial computation). This is evidenced by the fact that even within e.g. the place cell community, there is debate as to these cells' mechanisms and function (eg memory, navigation, etc), or if they can even be said to only serve a single one function. However, they are still referred to as place cells, not as a statement of their function but as a history-dependent label that refers to their observed correlates with experimental variables. Thus, the observation that spatially tuned cells are "inevitable derivatives of any complex system" is itself an interesting finding which contributes to, rather than contradicts, the study of these cells. It seems that the authors have a specific definition in mind when they say that a cell is "truly" "spatial" or that a biological or artificial neural network is a "spatial system", but this definition is not stated, and it is not clear that the terminology used in the field presupposes their definition.

In sum, the authors have demonstrated the existence of a control/null hypothesis for observations of spatially-tuned cells. However, 1) It is not enough to show that a control (null hypothesis) exists, one needs to test if experimental observations are no better than control, in order to make strong claims about experimental data, 2) the authors do not acknowledge the work that has been done in many cases specifically to control for this null hypothesis in experimental work or to test the sensory influences on these cells, and 3) the authors do not rigorously test the degree or source of spatial tuning of their units.

Comments on revisions:

While I'm happy to admit that standards of spatial tuning are not unified or consistent across the field, I do not believe the authors have addressed my primary concern: they have pointed out a null model, and then have constructed a strong opinion around that null model without actually testing if it's sufficient to account for neural data. I've slightly modified my review to that effect.

I do think it would be good for the authors to state in the manuscript what they mean when they say that a cell is "truly" "spatial" or that a biological or artificial neural network is a "spatial system". This is implied throughout, but I was unable to find what would distinguish a "truly" spatial system from a "superfluous" one.

Author response:

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

Reviewer #1 (Public Review):

but see Franzius, Sprekeler, Wiskott, PLoS Computational Biology, 2007

We have discussed the differences with this work in the response to Editor recommendations above.

While the findings reported here are interesting, it is unclear whether they are the consequence of the specific model setting, and how well they would generalize.

We have considered deep vision models across different architectures in our paper, which include traditional feedforward convolutional neural networks (VGG-16), convolutional neural networks with skip connections (ResNet-50) and the Vision Transformer (VIT) which employs self-attention instead of convolution as its core information processing unit.

In particular, examining the pictures shown in Fig. 1A, it seems that local walls of the ’box’ contain strong oriented features that are distinct across different views. Perhaps the response of oriented visual filters can leverage these features to uniquely determine the spatial variable. This is concerning because this is a very specific setting that is unlikely to generalize.

The experimental set up is based on experimental studies of spatial cognition in rodents. They are typically foraging in square or circular environments. Indeed, square environments will have more borders and corners that will provide information about the spatial environment, which is true in both empirical studies and our simulations. In any navigation task, and especially more realistic environments, visual information such as borders or landmarks likely play a major role in spatial information available to the agent. In fact, studies that do not consider sensory information to contribute to spatial information are likely missing a major part of how animals navigate.

The prediction would be that place cells/head direction cells should go away in darkness. This implies that key aspects of functional cell types in the spatial cognition are missing in the current modeling framework.

We addressed this comment in our response to the editor’s highlight. To briefly recap, we do not intend to propose a comprehensive model of the brain that captures all spatial phenomena, as we would not expect this from an object recognition network. Instead, we show that such a simple and nonspatial model can reproduce key signatures of spatial cells, raising important questions about how we interpret spatial cell types that dominate current research.

Reviewer #2 (Public Review):

The network used in the paper is still guided by a spatial error signal [...] one could say that the authors are in some way hacking this architecture and turning it into a spatial navigation one through learning.

To be clear, the base networks we use do not undergo spatial error training. They have either been pre-trained on image classification tasks or are untrained. We used a standard neuroscience approach: training linear decoders on representations to assess the spatial information present in the network layers. The higher decoding errors in early layer representations (Fig. 2A) indicate that spatial information differs across layers—an effect that cannot be attributed to the linear decoder alone.

My question is whether the paper is fighting an already won battle.

Intuitive cell type discovery are still being celebrated. Concentrating on this kind of cell type discovery has broader implications that could be deleterious to the future of science. One point to note is that this issue depends on the area or subfield of neuroscience. In some subfields, papers that claim to find cell types with a strong claim of specific functions are relatively rare, and population coding is common (e.g., cognitive control in primate prefrontal cortex, neural dynamics of motor control). Although rodent neuroscience as a field is increasingly adopting population approaches, influential researchers and labs are still publishing “cell types” and in top journals (here are a few from 2017-2024: Goal cells (Sarel et al., 2017), Object-vector cells (Høydal et al., 2019), 3D place cells (Grieves et al., 2020), Lap cells (Sun et al., 2020), Goal-vector cells (Ormond and O’Keefe, 2022), Predictive grid cells (Ouchi and Fujisawa, 2024).

In some cases, identification of cell types is only considered a part of the story, and there are analyses on behavior, neural populations, and inactivationbased studies. However, our view (and suggest this is shared amongst most researchers) is that a major reason these papers are reviewed and accepted to top journals is because they have a simple, intuitive “cell type” discovery headline, even if it is not the key finding or analysis that supports the insightful aspects of the work. This is unnecessary and misleading to students of neuroscience, related fields, and the public, it affects private and public funding priorities and in turn the future of science. Worse, it could lead the field down the wrong path, or at the least distribute attention and resources to methods and papers that could be providing deeper insights. Consistent with the central message of our work, we believe the field should prioritize theoretical and functional insights over the discovery of new “cell types”.

Reviewer #3 (Public Review):

The ability to linearly decode position from a large number of units is not a strong test of spatial information, nor is it a measure of spatial cognition

Using a linear decoder to test what information is contained in a population of neurons available for downstream areas is a common technique in neuroscience (Tong and Pratte, 2012; DiCarlo et al., 2012) including spatial cells (e.g., Diehl et al. 2017; Horrocks et al. 2024). A linear decoder is used because it is a direct mapping from neurons to potential output behavior. In other words, it only needs to learn some mapping to link one set of neurons to another set which can “read out” the information. As such, it is a measure of the information contained in the population, and it is a lower bound of the information contained - as both biological and artificial neurons can do more complex nonlinear operations (as the activation function is nonlinear).

We understand the reviewer may understand this concept but we explain it here to justify our position and for completeness of this public review.

For example, consider the head direction cells in Figure 3C. In addition to increased activity in some directions, these cells also have a high degree of spatial nonuniformity, suggesting they are responding to specific visual features of the environment. In contrast, the majority of HD cells in the brain are only very weakly spatially selective, if at all, once an animal’s spatial occupancy is accounted for (Taube et al 1990, JNeurosci). While the preferred orientation of these cells are anchored to prominent visual cues, when they rotate with changing visual cues the entire head direction system rotates together (cells’ relative orientation relationships are maintained, including those that encode directions facing AWAY from the moved cue), and thus these responses cannot be simply independent sensory-tuned cells responding to the sensory change) (Taube et al 1990 JNeurosci, Zugaro et al 2003 JNeurosci, Ajbi et al 2023).

As we have noted in our response to the editor, one of the main issues is how the criteria to assess what they are interested in is created in a subjective, and biased way, in a circular fashion (seeing spatial-like responses, developing criteria to determine a spatial response, select a threshold).

All the examples the reviewer provides concentrate on strict criteria developed after finding such cells. What is the purpose of these cells for function, for behavior? Just finding a cell that looks like it is tuned to something does not explain its function. Neuroscience began with tuning curves in part due to methodological constraints, which was a promising start, but we propose that this is not the way forward.

The metrics used by the authors to quantify place cell tuning are not clearly defined in the methods, but do not seem to be as stringent as those commonly used in real data. (e.g. spatial information, Skaggs et al 1992 NeurIPS).

We identified place cells following the definition from Tanni et al. (2022), by one of the leading labs in the field. Since neurons in DNNs lack spikes, we adapted their criteria by focusing on the number of spatial bins in the ratemap rather than spike-based measures. However, our central argument is that the very act of defining spatial cells is problematic. Researchers set out to find place cells to study spatial representations, find spatially selective cells with subjective, qualitative criteria (sometimes combined with prior quantitative criteria, also subjectively defined), then try to fine-tune the criteria to more “stringent” criteria, depending on the experimental data at hand. It is not uncommon to see methodological sections that use qualitative judgments, such as: “To avoid bias ... we applied a loose criteria for place cells” Tanaka et al. (2018) , which reflects the lack of clarity for and subjectivity of place cell selection criteria.

A simple literature survey reveals inconsistent criteria across studies. For place field selection, Dombeck et al. (2010) required mean firing rates exceeding 25% of peak rate, while Tanaka et al. (2018) used a 20% threshold. Speed thresholds also vary dramatically: Dombeck et al. (2010) calculated firing rates only when mice moved faster than 8.3 cm/s, whereas Tanaka et al. (2018) used 2 cm/s. Additional criteria differ further: Tanaka et al. (2018) required firing rates between 1-10 Hz and excluded cells with place fields larger than 1/3 of the area, while Dombeck et al. (2010) selected fields above 1.5 Hz, and Tanni et al. (2022) used a 10 spatial bins to 1/2 area threshold. As Dombeck et al. (2010) noted, differences in recording methods and place field definitions lead to varying numbers of identified place cells. Moreover, Grijseels et al. (2021) demonstrated that different detection methods produce vastly different place cell counts with minimal overlap between identified populations.

This reflects a deeper issue. Unlike structurally and genetically defined cell types (e.g., pyramidal neurons, interneurons, dopamingeric neurons, cFos expressing neurons), spatial cells lack such clarity in terms of structural or functional specialization and it is unclear whether such “cell types” should be considered cell types in the same way. While scientific progress requires standardized definitions, the question remains whether defining spatial cells through myriad different criteria advances our understanding of spatial cognition. Are researchers finding the same cells? Could they be targeting different populations? Are they missing cells crucial for spatial cognition that they exclude due to the criteria used? We think this is likely. The inconsistency matters because different criteria may capture genuinely different neural populations or computational processes.

Variability in definitions and criteria is an issue in any field. However, as we have stated, the deeper issue is whether we should be defining and selecting these cells at all before commencing analysis. By defining and restricting to spatial “cell types”, we risk comparing fundamentally different phenomena across studies, and worse, missing the fundamental unit of spatial cognition (e.g., the population).

We have added a paragraph in Discussion (lines 357-366) noting the inconsistency in place cell selection criteria in the literature and the consequences of using varying criteria.

We have also added a sentence (lines 354-356) raising the comparison of functionally defined spatial cell types with structurally and genetically defined cell types in the Discussion.

Thus, the question is not whether spatially tuned cells are influenced by sensory information, but whether feed-forward sensory processing alone is sufficient to account for their observed turning properties and responses to sensory manipulations.

These issues indicate a more significant underlying issue of scientific methodology relating to the interpretation of their result and its impact on neuroscientific research. Specifically, in order to make strong claims about experimental data, it is not enough to show that a control (i.e. a null hypothesis) exists, one needs to demonstrate that experimental observations are quantitatively no better than that control.

Where the authors state that ”In summary, complex networks that are not spatial systems, coupled with environmental input, appear sufficient to decode spatial information.” what they have really shown is that it is possible to decode *some degree* of spatial information. This is a null hypothesis (that observations of spatial tuning do not reflect a ”spatial system”), and the comparison must be made to experimental data to test if the so-called ”spatial” networks in the brain have more cells with more reliable spatial info than a complex-visual control.

We agree that good null hypotheses with quantitative comparisons are important. However, it is not clear that researchers in the field have not been using a null hypothesis, rather they make the assumption that these cell types exist and are functional in the way they assume. We provide one null hypothesis. The field can and should develop more and stronger null hypotheses.

In our work, we are mainly focusing on criteria of finding spatial cells, and making the argument that simply doing this is misleading. Researcher develop criteria and find such cells, but often do not go further to assess whether they are real cell “types”, especially if they exclude other cells which can be misleading if other cells also play a role in the function of interest.

But from many other experiments including causal manipulations (e.g. Robinson et al 2020 Cell, DeLauilleon et al 2015 Nat Neuro), which the authors conveniently ignore. Thus, I do not find their argument, as strongly stated as it is, to be well-supported.

We acknowledge that there are several studies that have performed inactivation studies that suggest a strong role for place cells in spatial behavior. Most studies do not conduct comprehensive analyses to confirm that their place cells are in fact crucial for the behavior at hand.

One question is how the criteria were determined. Did the researchers make their criteria based on what “worked”, so they did not exclude cells relevant to the behavior? What if their criteria were different, then the argument could have been that non-place cells also contribute to behavior.

Another question is whether these cells are the same kinds of cells across studies and animals, given the varied criteria across studies? As most studies do not follow the same procedures, it is unclear whether we can generalize these results across cells and indeed, across task and spatial environments.

Finally, does the fact that the place cells – the strongly selective cells with a place field – have a strong role in navigation provide any insight into the mechanism? Identifying cells by itself does not contribute to our understanding of how they work. Consistent with our main message, we argue that performing analyses and building computational models that uncover how the function of interest works is more valuable than simply naming cells.

Finally, I find a major weakness of the paper to be the framing of the results in opposition to, as opposed to contributing to, the study of spatially tuned cells. For example, the authors state that ”If a perception system devoid of a spatial component demonstrates classically spatially-tuned unit representations, such as place, head-direction, and border cells, can ”spatial cells” truly be regarded as ’spatial’?” Setting aside the issue of whether the perception system in question does indeed demonstrate spatiallytuned unit representations comparable to those in the brain, I ask ”Why not?” This seems to be a semantic game of reading more into a name then is necessarily there. The names (place cells, grid cells, border cells, etc) describe an observation (that cells are observed to fire in certain areas of an animal’s environment). They need not be a mechanistic claim... This is evidenced by the fact that even within e.g. the place cell community, there is debate about these cells’ mechanisms and function (eg memory, navigation, etc), or if they can even be said to serve only a single function. However, they are still referred to as place cells, not as a statement of their function but as a history-dependent label that refers to their observed correlates with experimental variables. Thus, the observation that spatially tuned cells are ”inevitable derivatives of any complex system” is itself an interesting finding which *contributes to*, rather than contradicts, the study of these cells. It seems that the authors have a specific definition in mind when they say that a cell is ”truly” ”spatial” or that a biological or artificial neural network is a ”spatial system”, but this definition is not stated, and it is not clear that the terminology used in the field presupposes their definition.

We have to agree to disagree with the reviewer on this point. Although researchers may reflect on their work and discuss what the mechanistic role of these cells are, it is widely perceived that cell type discovery is perceived as important to journals and funders due to its intuitive appeal and easy-tounderstand impact – even if there is no finding of interest to be reported. As noted in the comment above, papers claiming cell type discovery continue to be published in top journals and is continued to be funded.

Our argument is that maybe “cell type” discovery research should not celebrated in the way it is, and in fact they shouldn’t be discovered when they are not genuine cell types like structural or genetic cell types. By using this term it make it appear like they are something they are not, which is misleading. They may be important cells, but providing a name like a “place” cell also suggests other cells are not encoding space - which is very unlikely to be true.

In sum, our view is that finding and naming cells through a flawed theoretical lens that may not actually function as their names suggests can lead us down the wrong path and be detrimental to science.

Reviewer #1 (Recommendations For The Authors):

The novelty of the current study relative to the work by Franzius, Sprekeler, Wiskott (PLoS Computational Biology, 2007) needs to be carefully addressed. That study also modeled the spatial correlates based on visual inputs.

Our work differs from Franzius et al. (2007) on both theoretical and experimental fronts. While both studies challenge the mechanisms underlying spatial cell formation, our theoretical contributions diverge. Franzius et al. (2007) assume spatial cells are inherently important for spatial cognition and propose a sensory-driven computational mechanism as an alternative to mainstream path integration frameworks for how spatial cells arise and support spatial cognition. In contrast, we challenge the notion that spatial cells are special at all. Using a model with no spatial grounding, we demonstrate that 1) spatial cells as naturally emerge from complex non-linear processing and 2) are not particularly useful for spatial decoding tasks, suggesting they are not crucial for spatial cognition.

Our approach employs null models with fixed weights—either pretrained on classification tasks or entirely random—that process visual information non-sequentially. These models serve as general-purpose information processors without spatial grounding. In contrast, Franzius et al. (2007)’s model learns directly from environmental visual information, and the emergence of spatial cells (place or head-direction cells) in their framework depends on input statistics, such as rotation and translation speeds. Notably, their model does not simultaneously generate both place and head-direction cells; the outcome varies with the relative speed of rotation versus translation. Their sensory-driven model indirectly incorporates motion information through learning, exhibiting a time-dependence influenced by slow-feature analysis.

Conversely, our model simultaneously produces units with place and headdirection cell profiles by processing visual inputs sampled randomly across locations and angles, independent of temporal or motion-related factors. This positions our model as a more general and fundamental null hypothesis, ideal for challenging prevailing theories on spatial cells due to its complete lack of spatial or motion grounding.

Finally, unlike Franzius et al. (2007), who do not evaluate the functional utility of their spatial representations, we test whether the emergent spatial cells are useful for spatial decoding. We find that not only do spatial cells emerge in our non-spatial model, but they also fail to significantly aid in location or head-direction decoding. This is the central contribution of our work: spatial cells can arise without spatial or sensory grounding, and their functional relevance is limited. We have updated the manuscript to clarify the novelty of the current contribution to previous work (lines 324-335).

In Fig. 2, it may be useful to plot the error in absolute units, rather than the normalized error. The direction decoding can be quantified in terms of degree Also, it would be helpful to compare the accuracy of spatial localization to that of the actual place cells in rodents.

We argue it makes more sense and put comparison in perspective when we normalize the error by dividing the maximal error possible under each task. For transparency, we plot the errors in absolute physical units used by the Unity game engine in the updated Appendix (Fig. 1).

Reviewer #2 (Recommendations For The Authors):

Regarding the involvement of ’classified cells’ in decoding, I think a useful way to present the results would be to show the relationship between ’placeness’, ’directioness’ and ’borderness’ and the strength of the decoder weights. Either as a correlation or as a full scatter plot.

We appreciate your suggestion to visualize the relationship between units’ spatial properties and their corresponding decoder weights. We believe it would be an important addition to our existing results. Based on the exclusion analyses, we anticipated the correlation to be low, and the additional results support this expectation.

As an example, we present unit plots below for VGG-16 (pre-trained and untrained, at its penultimate layer with sampling rate equals 0.3; Author response image 1 and 2). Additional plots for various layers and across models are included in the supplementary materials (Fig. S12-S28). Consistently across conditions, we observed no significant correlations between units’ spatial properties (e.g., placeness) and their decoding weight strengths. These results further corroborate the conclusions drawn from our exclusion analyses.

Reviewer #3 (Recommendations For The Authors):

My main suggestions are that the authors: -perform manipulations to the sensory environment similar to those done in experimental work, and report if their tuned cells respond in similar ways -quantitatively compare the degree of spatial tuning in their networks to that seen in publicly available data -re-frame the discussion of their results to critically engage with and contribute to the field and its past work on sensory influences to these cells

As we noted in our opening section, our model is not intended as a model of the brain. It is a non-spatial null model, and we present the surprising finding that even such a model contains spatial cell-like units if identified using criteria typically used in the field. This raises the question whether simply finding cells that show spatial properties is sufficient to grant the special status of “cell type” that is involved in the brain function of interest.

Author response image 1.

VGG-16 (pre-trained), penultimate layer units, show no apparent relationship between spatial properties and their decoder weight strengths.

Author response image 2.

VGG-16 (untrained), penultimate layer units, show no apparent relationship between spatial properties and their decoder weight strengths.

Furthermore, our main simulations were designed to be compared to experimental work where rodents foraged around square environments in the lab. We did not do an extensive set of simulations as the purpose of our study is not to show that we capture exactly every single experimental finding, but rather raise the issues with the functional cell type definition and identification approach for progressing neuroscientific knowledge.

Finally, as we note in more detail below, different labs use different criteria for identifying spatial cells, which depend both on the lab and the experimental design. Our point is that we can identify such cells using criteria set by neuroscientists, and that such cell types may not reflect any special status in spatial processing. Additional simulations that show less alignment with certain datasets will not provide support for or against our general message.

References

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This appears to be out of date.

I'm pretty sure I meant to add a note here explaining that the IT staff can change the urgency rank of the topic by themselves.

the squares seem to be flipped wrt to their description, i.e. horizontal vs vertical

Ch10: They discovered that within each species, there is some regularity in the ratios of the bases: the amount of adenine is always equal to the amount of thymine (A = T), and the amount of guanine is always equal to the amount of cytosine (G = C) (Table 10.1). These findings became known as Chargaff’s rules. p.296

Chargaff's rule: G=C & A=T

Ch10: He discovered that DNA consists of a large number of linked, repeating units, called nucleotides; each nucleotide contains a sugar, a phosphate, and a base. p.296

Nucleotide is made up of three components: sugar, phosphate, and base

I think this really shows how fast things are changing with media. People don’t rely on cable anymore because streaming is way easier and cheaper. It’s interesting how TV is still a big part of life, just in a different form through apps and the internet.

Alarming

make this shi easier twin or im finna slime you out </3

then suggest lah

unidecode()

A link would be usefull: https://collections.ushmm.org/search/

The DATETIME benchmark seems to be limited by its exclusion of relative weekday expressions, such as "next Monday," which necessitate resolving dates based on a reference timestamp rather than absolute formats. This is a significant limitation because real-world applications of date-time processing frequently involve contextual relativity in natural language, meaning the benchmark may overestimate model performance by not testing the computational inference required for ambiguous, everyday scenarios.

コマンドオプションについても少し触れたほうが良いと思います。

nits: 今までがこの表記ですが、「〜たり、〜たり」にしたほうがよいか悩ましいですが、文章の見直しとして一応コメントしておきます。

Python 3.14で実行すると最後に when serializing dict item 'birth' が出力されます。

Markdownで {code-block} dark になっているので、 {code-block} bash にしたほうが良さそうです。

また、キャプションもあったほうが良さそうです。

单体比例

曝光剂量

固含量

溶剂

接触角测试条件

树脂2

树脂1

接触角2

接触角1

公式ドキュメントによると、ここは ImageDraw.text の方が正しいような気がします。 https://pillow.readthedocs.io/en/stable/reference/ImageDraw.html#PIL.ImageDraw.ImageDraw.text

もしそうだとすると、引数の最後に font_size=None も入れる必要がありそうです。

树脂2

树脂1

结构3

结构2

结构1

配方3接触角3

配方2接触角2

配方1接触角1

公式ドキュメントの定義と少し違っています。 https://openpyxl.readthedocs.io/en/stable/api/openpyxl.reader.excel.html#openpyxl.reader.excel.load_workbook

頭に「$」を付けたほうが良さそうです。

また、Markdownが {code-block} dark になっているので {code-block} bash にしたほうが良さそうです。

実際に実行してみると、 attack! の下に以下が出力されました。

0

「#」を付けたほうが良さそうです。

Markdownが {code-block} dark になっているので {code-block} bash にしたほうが良さそうです。

design gap

visualization map making

key term indeed

顶涂5接触角5

顶涂4接触角4

顶涂3接触角3

顶涂2接触角2

顶涂1接触角1

结构3

结构1

结构4

结构2

test annotation

Explore the differences between MVC, MVVM, and MVP design patterns in Swift. Learn how each pattern structures your iOS app for better scalability, testability, and clean architecture.

Authorship Provision in Augment

inspiration

Hyperscope

公式ドキュメントの定義と少し違っています。 https://docs.python.org/ja/3/library/csv.html#csv.csvwriter.writerows

公式ドキュメントの定義と少し違っています。 https://docs.python.org/ja/3/library/csv.html#csv.csvwriter.writerow

ここも少し違いますね。