Author response:

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

eLife Assessment

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

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

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

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

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

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

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

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

Public Reviews:

Reviewer (1 (Public review):

Summary

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

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

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

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

Strengths of study

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

Limitations

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

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

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

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

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

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

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

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

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

The updated document has addressed this caveat.

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

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

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

This caveat has been addressed in the revised manuscript.

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

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

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

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

Comments on the latest version:

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

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

Reviewer 2 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

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

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

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

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

Conclusions:

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

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

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

Reviewer 3 (Public review):

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

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

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

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

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

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

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

(2 3.2) Small Sample Size

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

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

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

(3 3.3) Statistical Concerns

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

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

Several points require clarification or improvement:

(4) Correlation Methods: The manuscript does not specify whether the reported correlation analyses are based on Pearson or Spearman correlation.

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

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

We will add the confidence intervals to the second revision of our manuscript.

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

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

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

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

(8) Figure 2C

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

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

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

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

We will highlight these motivations more clearly in the Methods of the revised manuscript.

(9 3.4) Interpretation of Aperiodic Signal

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

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

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

Quote:

“3.4 Interpretation of aperiodic signal:

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

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

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

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

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

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

(10) Additionally, the authors state:

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

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

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

Our analyses were based on previous findings in the literature.

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

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

(12 3.5) Problems with EEG Preprocessing and Analysis

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

As mentioned in the Methods (Page 15 Line 376) and the previous response, the pop_resample function used by EEGLAB applies an anti-aliasing filter, at half the resampling frequency (as per the Nyquist theorem https://eeglab.org/tutorials/05_Preprocess/resampling.html). The upper cut off of the low pass filter set by EEGlab prior to down sampling (30 Hz) is still far above the frequency of interest in the current study  (1-20 Hz), thus allowing us to derive valid results.

Quote:

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

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

Moreover, the resting-state data were not resampled to 60 Hz. We will make this clearer in the Methods of the revised manuscript.

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

The expected effects of this anti-aliasing filter can be seen in the attached Figure R1, showing an example participant’s spectrum in the 1-30 Hz range (as opposed to the 1-20 Hz plotted in the manuscript), clearly showing a 30-40 dB drop at 30 Hz. Any aliasing due to, for example, remaining line noise, would additionally be visible in this figure (as well as Figure 3) as a peak.

Author response image 1.

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

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

Quote:

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

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

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

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

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

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

Quote:

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

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

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

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

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

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

Quote:

“3.5 Problems with EEG preprocessing and analysis:

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

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

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

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

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

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

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

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

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

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

The time segment was the length of the epoch, that is, 1 second for the resting state conditions and 6.25 seconds for the visual stimulation conditions. This has now been explicitly stated in the revised manuscript (Page 14, Lines 379-380).<br /> - "We excluded the alpha range (8-14 Hz) for this fit to avoid biasing the results due to documented differences in alpha activity between CC and SC individuals (Bottari et al., 2016; Ossandón et al., 2023; Pant et al., 2023)." This does not really make sense, as the FOOOF algorithm first fits the 1/f slope, for which the alpha activity is not relevant.

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

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

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

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

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

(14) The authors mention:

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

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

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

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

eLife Assessment

This potentially useful study involves neuro-imaging and electrophysiology in a small cohort of congenital cataract patients after sight recovery and age-matched control participants with normal sight. It aims to characterize the effects of early visual deprivation on excitatory and inhibitory balance in the visual cortex. While the findings are taken to suggest the existence of persistent alterations in Glx/GABA ratio and aperiodic EEG signals, the evidence supporting these claims is incomplete. Specifically, small sample sizes, lack of a specific control cohort, and other methodological limitations will likely restrict the usefulness of the work, with relevance limited to scientists working in this particular subfield.

As pointed out in the public reviews, there are very few human models which allow for assessing the role of early experience on neural circuit development. While the prevalent research in permanent congenital blindness reveals the response and adaptation of the developing brain to an atypical situation (blindness), research in sight restoration addresses the question of whether and how atypical development can be remediated if typical experience (vision) is restored. The literature on the role of visual experience in the development of E/I balance in humans, assessed via Magnetic Resonance Spectroscopy (MRS), has been limited to a few studies on congenital permanent blindness. Thus, we assessed sight recovery individuals with a history of congenital blindness, as limited evidence from other researchers indicated that the visual cortex E/I ratio might differ compared to normally sighted controls.

Individuals with total bilateral congenital cataracts who remained untreated until later in life are extremely rare, particularly if only carefully diagnosed patients are included in a study sample. A sample size of 10 patients is, at the very least, typical of past studies in this population, even for exclusively behavioral assessments. In the present study, in addition to behavioral assessment as an indirect measure of sensitive periods, we investigated participants with two neuroimaging methods (Magnetic Resonance Spectroscopy and electroencephalography) to directly assess the neural correlates of sensitive periods in humans. The electroencephalography data allowed us to link the results of our small sample to findings documented in large cohorts of both, sight recovery individuals and permanently congenitally blind individuals. As pointed out in a recent editorial recommending an “exploration-then-estimation procedure,” (“Consideration of Sample Size in Neuroscience Studies,” 2020), exploratory studies like ours provide crucial direction and specific hypotheses for future work.

We included an age-matched sighted control group recruited from the same community, measured in the same scanner and laboratory, to assess whether early experience is necessary for a typical excitatory/inhibitory (E/I) ratio to emerge in adulthood. The present findings indicate that this is indeed the case. Based on these results, a possible question to answer in future work, with individuals who had developmental cataracts, is whether later visual deprivation causes similar effects. Note that even if visual deprivation at a later stage in life caused similar effects, the current results would not be invalidated; by contrast, they are essential to understand future work on late (permanent or transient) blindness.

Thus, we think that the present manuscript has far reaching implications for our understanding of the conditions under which E/I balance, a crucial characteristic of brain functioning, emerges in humans.

Finally, our manuscript is one of the first few studies that relate MRS neurotransmitter concentrations to parameters of EEG aperiodic activity. Since present research has been using aperiodic activity as a correlate of the E/I ratio, and partially of higher cognitive functions, we think that our manuscript additionally contributes to a better understanding of what might be measured with aperiodic neurophysiological activity.

Public Reviews:<br /> Reviewer #1 (Public Review):

Summary:

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

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

The same participants then took part in an EEG experiment. The authors selected only two electrodes placed in the visual cortex for analysis and reported a group difference in an EEG index of neural activity, the aperiodic intercept, as well as the aperiodic slope, considered a proxy for cortical inhibition. They report an exploratory correlation between the aperiodic intercept and Glx in one out of three EEG conditions.

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

Strengths of study:

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

Limitations:

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

Applying strict criteria, we only included individuals who were born with no patterned vision in the CC group. The population of individuals who have remained untreated past infancy is small in India, despite a higher prevalence of childhood cataract than Germany. Indeed, from the original 11 CC and 11 SC participants tested, one participant each from the CC and SC group had to be rejected, as their data had been corrupted, resulting in 10 participants in each group.

It was a challenge to recruit participants from this rare group with no history of neurological diagnosis/intake of neuromodulatory medications, who were able and willing to undergo both MRS and EEG. For this study, data collection took more than 2.5 years.

We took care of the validity of our results with two measures; first, we assessed not just MRS, but additionally, EEG measures of E/I ratio. The latter allowed us to link results to a larger population of CC individuals, that is, we replicated the results of a larger group of 28 additional individuals (Ossandón et al., 2023) in our sub-group.

Second, we included a control voxel. As predicted, all group effects were restricted to the occipital voxel.

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

The existing work on visual deprivation and neurochemical changes, as assessed with MRS, has been limited to permanent congenital blindness. In fact, most of the studies on permanent blindness included only congenitally blind or early blind humans (Coullon et al., 2015; Weaver et al., 2013), or, in separate studies, only late-blind individuals (Bernabeu et al., 2009). Thus, accordingly, we started with the most “extreme” visual deprivation model, sight recovery after congenital blindness. If we had not observed any group difference compared to normally sighted controls, investigating other groups might have been trivial. Based on our results, subsequent studies in late blind individuals, and then individuals with developmental cataracts, can be planned with clear hypotheses.

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

Worse data quality in the frontal than the visual cortex has been repeatedly observed in the MRS literature, attributable to magnetic field distortions (Juchem & Graaf, 2017) resulting from the proximity of the region to the sinuses (recent example: (Rideaux et al., 2022)). Nevertheless, we chose the frontal control region rather than a parietal voxel, given the potential neurochemical changes in multisensory regions of the parietal cortex due to blindness. Such reorganization would be less likely in frontal areas associated with higher cognitive functions. Further, prior MRS studies of the visual cortex have used the frontal cortex as a control region as well (Pitchaimuthu et al., 2017; Rideaux et al., 2022). In the revised manuscript, we more explicitly inform the reader about this data quality difference between regions in the Methods (Pages 11-12, MRS Data Quality/Table 2) and Discussion (Page 25, Lines 644- 647).

Importantly, while in the present study data quality differed between the frontal and visual cortex voxel, it did not differ between groups (Supplementary Material S6).  

Further, we checked that the frontal cortex datasets for Glx and GABA+ concentrations were of sufficient quality: the fit error was below 8.31% in both groups (Supplementary Material S3). For reference, Mikkelsen et al. reported a mean GABA+ fit error of 6.24 +/- 1.95% from a posterior cingulate cortex voxel across 8 GE scanners, using the Gannet pipeline. No absolute cutoffs have been proposed for fit errors. However, MRS studies in special populations (I/E ratio assessed in narcolepsy (Gao et al., 2024), GABA concentration assessed in Autism Spectrum Disorder (Maier et al., 2022) have used frontal cortex data with a fit error of <10% to identify differences between cohorts (Gao et al., 2024; Pitchaimuthu et al., 2017). Based on the literature, MRS data from the frontal voxel of the present study would have been of sufficient quality to uncover group differences.

In the revised manuscript, we added the recently published MRS quality assessment form to the supplementary materials (Supplementary Excel File S1). Additionally, we would like to allude to our apriori prediction of group differences for the visual cortex, but not for the frontal cortex voxel. Finally, EEG data quality did not differ between frontal and occipital electrodes; therefore, lower sensitivity of frontal measures cannot easily explain the lack of group differences for frontal measures.

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

Indeed, higher inhibition was not predicted, which we attempt to reconcile in our discussion section. We base our discussion mainly on the non-human animal literature, which has shown evidence of homeostatic changes after prolonged visual deprivation in the adult brain (Barnes et al., 2015). It is also interesting to note that after monocular deprivation in adult humans, resting GABA+ levels decreased in the visual cortex (Lunghi et al., 2015). Assuming that after delayed sight restoration, adult neuroplasticity mechanisms must be employed, these studies would predict a “balancing” of the increased excitatory drive following sight restoration by a commensurate increase in inhibition (Keck et al., 2017). Additionally, the EEG results of the present study allowed for speculation regarding the underlying neural mechanisms of an altered E/I ratio. The aperiodic EEG activity suggested higher spontaneous spiking (increased intercept) and increased inhibition (steeper aperiodic slope between 1-20 Hz) in CC vs SC individuals (Ossandón et al., 2023).

In the revised manuscript, we have more clearly indicated that these speculations are based primarily on non-human animal work, due to the lack of human studies on the subject (Page 23, Lines 609-613).

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

The goal of the present study was to assess whether we would observe changes in E/I ratio after restoring vision at all. We would not have included patients without nystagmus in the CC group of the present study, since it would have been unlikely that they experienced congenital patterned visual deprivation. Amongst diagnosticians, nystagmus or strabismus might not be considered genuine “comorbidities” that emerge in people with congenital cataracts. Rather, these are consequences of congenital visual deprivation, which we employed as diagnostic criteria. Similarly, absorbed lenses are clear signs that cataracts were congenital. As in other models of experience dependent brain development (e.g. the extant literature on congenital permanent blindness, including anophthalmic individuals (Coullon et al., 2015; Weaver et al., 2013), some uncertainty remains regarding whether the (remaining, in our case) abnormalities of the eye, or the blindness they caused, are the factors driving neural changes. In case of people with reversed congenital cataracts, at least the retina is considered to be intact, as they would otherwise not receive cataract removal surgery.

However, we consider it unlikely that strabismus caused the group differences, because the present study shows group differences in the Glx/GABA+ ratio at rest, regardless of eye opening or eye closure, for which strabismus would have caused distinct effects. By contrast, the link between GABA concentration and, for example, interocular suppression in strabismus, have so far been documented during visual stimulation (Mukerji et al., 2022; Sengpiel et al., 2006), and differed in direction depending on the amblyopic vs. non-amblyopic eye. Further, one MRS study did not find group differences in GABA concentration between the visual cortices of 16 amblyopic individuals and sighted controls (Mukerji et al., 2022), supporting that the differences in Glx/GABA+ concentration which we observed were driven by congenital deprivation, and not amblyopia-associated visual acuity or eye movement differences. 

In the revised manuscript, we discussed the inclusion criteria in more detail, and the aforementioned reasons why our data remains interpretable (Page 5, Lines 143 – 145, Lines 147-149). 

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

In the revised manuscript, we have clearly indicated that the exploratory correlation analyses are reported to put forth hypotheses for future studies (Page 4, Lines 118-128; Page 5, Lines 132-134; Page 25, Lines 644- 647).

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

The correlation between chronological age and aperiodic intercept was observed across groups, but the correlation between Glx and the intercept of the aperiodic EEG activity was seen only in the CC group, even though the SC group was matched for age. Thus, such a correlation was very unlikely to be predominantly driven by an effect of chronological age.

In the revised manuscript, we added the linear regressions with age as a covariate (Supplementary Material S16, referred to in the main Results, Page 21, Lines 534-537), demonstrating the significant relationship between aperiodic intercept and Glx concentration in the CC group. 

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

In the revised manuscript, we improved the phrasing (Page 5, Lines 130-132) and consistently reported the correlations as exploratory in the Methods and Discussion. We consider the correlation analyses as exploratory due to our sample size and the absence of prior work. However, we did hypothesize that both MRS and EEG markers would concurrently be altered in CC vs SC individuals.

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

The aperiodic intercept and slope did not differ between CC and SC individuals for Fp1 and Fp2, suggesting the spatial specificity of the results. In the revised manuscript, we added this analysis to the Supplementary Material (Supplementary Material S14) and referred to it in our Results (Page 20, Lines 513-514).

Further, Glx concentration in the visual cortex did not correlate with the aperiodic intercept in the SC group (Figure 4), suggesting that this relationship was indeed specific to the CC group.

The data from all electrodes has been analyzed and published in other studies as well (Pant et al., 2023; Ossandón et al., 2023). 

Reviewer #2 (Public Review):

Summary:

The manuscript reports non-invasive measures of activity and neurochemical profiles of the visual cortex in congenitally blind patients who recovered vision through the surgical removal of bilateral dense cataracts. The declared aim of the study is to find out how restoring visual function after several months or years of complete blindness impacts the balance between excitation and inhibition in the visual cortex.

Strengths:

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

Weaknesses:

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

Longitudinal studies would indeed be the best way to test the hypothesis that the lower E/I ratio in the CC group observed by the present study is a consequence of sight restoration.

We have now explicitly stated this in the Limitations section (Page 25, Lines 654-655).

However, longitudinal studies involving neuroimaging are an effortful challenge, particularly in research conducted outside of major developed countries and dedicated neuroimaging research facilities. Crucially, however, had CC and SC individuals, as well as permanently congenitally blind vs SC individuals (Coullon et al., 2015; Weaver et al., 2013), not differed on any neurochemical markers, such a longitudinal study might have been trivial. Thus, in order to justify and better tailor longitudinal studies, cross-sectional studies are an initial step.

(2.2) MR Spectroscopy shows a reduced GLX/GABA ratio in patients vs. sighted controls; however, this finding remains rather isolated, not corroborated by other observations. The difference between patients and controls only emerges for the GLX/GABA ratio, but there is no accompanying difference in either the GLX or the GABA concentrations. There is an attempt to relate the MRS data with acuity measurements and electrophysiological indices, but the explorative correlational analyses do not help to build a coherent picture. A bland correlation between GLX/GABA and visual impairment is reported, but this is specific to the patients' group (N=10) and would not hold across groups (the correlation is positive, predicting the lowest GLX/GABA ratio values for the sighted controls - the opposite of what is found). There is also a strong correlation between GLX concentrations and the EEG power at the lowest temporal frequencies. Although this relation is intriguing, it only holds for a very specific combination of parameters (of the many tested): only with eyes open, only in the patient group.

We interpret these findings differently, that is, in the context of experiments from non-human animals and the larger MRS literature (Page 23, Lines 609-611).

Homeostatic control of E/I balance assumes that the ratio of excitation (reflected here by Glx) and inhibition (reflected here by GABA+) is regulated. Like prior work (Gao et al., 2024, 2024; Narayan et al., 2022; Perica et al., 2022; Steel et al., 2020; Takado et al., 2022; Takei et al., 2016), we assumed that the ratio of Glx/GABA+ is indicative of E/I balance rather than solely the individual neurotransmitter levels. One of the motivations for assessing the ratio vs the absolute concentration is that as per the underlying E/I balance hypothesis, a change in excitation would cause a concomitant change in inhibition, and vice versa, which has been shown in non-human animal work (Fang et al., 2021; Haider et al., 2006; Tao & Poo, 2005) and modeling research (Vreeswijk & Sompolinsky, 1996; Wu et al., 2022). Importantly, our interpretation of the lower E/I ratio is not just from the Glx/GABA+ ratio, but additionally, based on the steeper EEG aperiodic slope (1-20 Hz). 

As stated in the Discussion section and Response 1.4, we did not expect to see a lower Glx/GABA+ ratio in CC individuals. We discuss the possible reasons for the direction of the correlation with visual acuity and aperiodic offset during passive visual stimulation, and offer interpretations and (testable) hypotheses.

We interpret the direction of the Glx/GABA+ correlation with visual acuity to imply that patients with highest (compensatory) balancing of the consequences of congenital blindness (hyperexcitation), in light of visual stimulation, are those who recover best. Note, the sighted control group was selected based on their “normal” vision. Thus, clinical visual acuity measures are not expected to sufficiently vary, nor have the resolution to show strong correlations with neurophysiological measures. By contrast, the CC group comprised patients highly varying in visual outcomes, and thus were ideal to investigate such correlations.

This holds for the correlation between Glx and the aperiodic intercept, as well. Previous work has suggested that the intercept of the aperiodic activity is associated with broadband spiking activity in neural circuits (Manning et al., 2009). Thus, an atypical increase of spiking activity during visual stimulation, as indirectly suggested by “old” non-human primate work on visual deprivation (Hyvärinen et al., 1981) might drive a correlation not observed in healthy populations.

In the revised manuscript, we have more clearly indicated in the Discussion that these are possible post-hoc interpretations (Page 23, Lines 584-586; Page 24, Lines 609-620; Page 24, Lines 644-647; Pages 25, Lines 650 - 657). We argue that given the lack of such studies in humans, it is all the more important that extant data be presented completely, even if the direction of the effects are not as expected.

(2.3) For these reasons, the reported findings do not allow us to draw firm conclusions on the relation between EEG parameters and E/I ratio or on the impact of early (vs. late) visual experience on the excitation/inhibition ratio of the human visual cortex.

Indeed, the correlations we have tested between the E/I ratio and EEG parameters were exploratory, and have been reported as such.

We have now made this clear in all the relevant parts of the manuscript (Introduction, Page 5, Lines 132-135; Methods, Page 16, Line 415; Results, Page 21, Figure 4; Discussion, Page 22, Line 568, Page 25, Lines 644-645, Page 25, Lines 650-657).

The goal of our study was not to compare the effects of early vs. late visual experience. The goal was to study whether early visual experience is necessary for a typical E/I ratio in visual neural circuits. We provided clear evidence in favor of this hypothesis. Thus, the present results suggest the necessity of investigating the effects of late visual deprivation. In fact, such research is missing in permanent blindness as well.

Reviewer #3 (Public Review):

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

My expertise is in EEG (particularly in the decomposition of periodic and aperiodic activity) and statistical methods. I have several major concerns in terms of methodological and statistical approaches along with the (over)interpretation of the results. These major concerns are detailed below.

(3.1) Variability in visual deprivation:

- The document states a large variability in the duration of visual deprivation (probably also the age at restoration), with significant implications for the sensitivity period's impact on visual circuit development. The variability and its potential effects on the outcomes need thorough exploration and discussion.

We work with a rare, unique patient population, which makes it difficult to systematically assess the effects of different visual histories while maintaining stringent inclusion criteria such as complete patterned visual deprivation at birth. Regardless, we considered the large variance in age at surgery and time since surgery as supportive of our interpretation: group differences were found despite the large variance in duration of visual deprivation. Moreover, the existing variance was used to explore possible associations between behavior and neural measures, as well as neurochemical and EEG measures.

In the revised manuscript, we have detailed the advantages (Methods, Page 5, Lines 143 – 145, Lines 147-149; Discussion, Page 26, Lines 677-678) and disadvantages (Discussion, Page 25, Lines 650-657) of our CC sample, with respect to duration of congenital visual deprivation.

(3.2) Sample size:

- The small sample size is a major concern as it may not provide sufficient power to detect subtle effects and/or overestimate significant effects, which then tend not to generalize to new data. One of the biggest drivers of the replication crisis in neuroscience.

We address the small sample size in our Discussion, and make clear that small sample sizes were due to the nature of investigations in special populations. In the revised manuscript, we added the sample sizes of previous studies using MRS in permanently blind individuals (Page 4, Lines 108 - 109). It is worth noting that our EEG results fully align with those of larger samples of congenital cataract reversal individuals (Page 25, Lines 666-676, Supplementary Material S18, S19) (Ossandón et al., 2023), providing us confidence about their validity and reproducibility. Moreover, our MRS results and correlations of those with EEG parameters were spatially specific to occipital cortex measures.

The main problem with the correlation analyses between MRS and EEG measures is that the sample size is simply too small to conduct such an analysis. Moreover, it is unclear from the methods section that this analysis was only conducted in the patient group (which the reviewer assumed from the plots), and not explained why this was done only in the patient group. I would highly recommend removing these correlation analyses.

In the revised manuscript, we have more clearly marked the correlation analyses as exploratory (Introduction, Page 4, Lines 118-128 and Page 5, Lines 132-134; Methods Page 16, Line 415; Discussion Page 22, Line 568, Page 24, Lines 644-645, Page 25, Lines 650-657); note that we do not base most of our discussion on the results of these analyses.

As indicated by Reviewer 1, reporting them allows for deriving more precise hypothesis for future studies. It has to be noted that we investigate an extremely rare population, tested outside of major developed economies and dedicated neuroimaging research facilities. In addition to being a rare patient group, these individuals come from poor communities. Therefore, we consider it justified to report these correlations as exploratory, providing direction for future research.

(3.3) Statistical concerns:

- The statistical analyses, particularly the correlations drawn from a small sample, may not provide reliable estimates (see https://www.sciencedirect.com/science/article/pii/S0092656613000858, which clearly describes this problem).

It would undoubtedly be better to have a larger sample size. We nonetheless think it is of value to the research community to publish this dataset, since 10 multimodal data sets from a carefully diagnosed, rare population, representing a human model for the effects of early experience on brain development, are quite a lot. Sample sizes in prior neuroimaging studies in transient blindness have most often ranged from n = 1 to n = 10. They nevertheless provided valuable direction for future research, and integration of results across multiple studies provides scientific insights. 

Identifying possible group differences was the goal of our study, with the correlations being an exploratory analysis, which we have clearly indicated in the methods, results and discussion.

- Statistical analyses for the MRS: The authors should consider some additional permutation statistics, which are more suitable for small sample sizes. The current statistical model (2x2) design ANOVA is not ideal for such small sample sizes. Moreover, it is unclear why the condition (EO & EC) was chosen as a predictor and not the brain region (visual & frontal) or neurochemicals. Finally, the authors did not provide any information on the alpha level nor any information on correction for multiple comparisons (in the methods section). Finally, even if the groups are matched w.r.t. age, the time between surgery and measurement, the duration of visual deprivation, (and sex?), these should be included as covariates as it has been shown that these are highly related to the measurements of interest (especially for the EEG measurements) and the age range of the current study is large.

In our ANOVA models, the neurochemicals were the outcome variables, and the conditions were chosen as predictors based on prior work suggesting that Glx/GABA+ might vary with eye closure (Kurcyus et al., 2018). The study was designed based on a hypothesis of group differences localized to the occipital cortex, due to visual deprivation. The frontal cortex voxel was chosen to indicate whether these differences were spatially specific. Therefore, we conducted separate ANOVAs based on this study design.

We have now clarified the motivation for these conditions in the Introduction (Page 4, Lines 122-125) and the Methods (Page 9, Lines 219-224).

In the revised manuscript, we added the rationale for parametric analyses for our outcomes (Shapiro-Wilk as well as Levene’s tests, Supplementary Material S9). Note that in the Supplementary Materials (S12, S14), we have reported the correlations between visual history metrics and MRS/EEG outcomes, thereby investigating whether the variance in visual history might have driven these results. Specifically, we found a (negative) correlation between visual cortex Glx/GABA+ concentration during eye closure and the visual acuity in the CC group (Figure 2c). None of the other exploratory correlations between MRS/EEG outcomes vs time since surgery, duration of blindness or visual acuity were significant in the CC group (Supplementary Material S12, S15).  

The alpha level used for the ANOVA models specified in the Methods section was 0.05. The alpha level for the exploratory analyses reported in the main manuscript was 0.008, after correcting for (6) multiple comparisons using the Bonferroni correction, also specified in the Methods. Note that the p-values following correction are expressed as multiplied by 6, due to most readers assuming an alpha level of 0.05 (see response regarding large p-values).

We used a control group matched for age, recruited and tested in the same institutes, using the same setup. We feel that we followed the gold standards for recruiting a healthy control group for a patient group.

- EEG statistical analyses: The same critique as for the MRS statistical analyses applies to the EEG analysis. In addition: was the 2x3 ANOVA conducted for EO and EC independently? This seems to be inconsistent with the approach in the MRS analyses, in which the authors chose EO & EC as predictors in their 2x2 ANOVA.

The 2x3 ANOVA was not conducted independently for the eyes open/eyes closed condition. The ANOVA conducted on the EEG metrics was 2x3 because it had two groups (CC, SC) and three conditions (eyes open (EO), eyes closed (EC) and visual stimulation (LU)) as predictors.

- Figure 4: The authors report a p-value of >0.999 with a correlation coefficient of -0.42 with a sample size of 10 subjects. This can't be correct (it should be around: p = 0.22). All statistical analyses should be checked.

As specified in the Methods and Figure legend, the reported p values in Figure 4 have been corrected using the Bonferroni correction, and therefore multiplied by the number of comparisons, leading to the seemingly large values.

Additionally, to check all statistical analyses, we put the manuscript through an independent Statistics Check (Nuijten & Polanin, 2020) (https://michelenuijten.shinyapps.io/statcheck-web/) and have uploaded the consistency report with the revised Supplementary Material (Supplementary Report 1).

- Figure 2c. Eyes closed condition: The highest score of the *Glx/GABA ratio seems to be ~3.6. In subplot 2a, there seem to be 3 subjects that show a Glx/GABA ratio score > 3.6. How can this be explained? There is also a discrepancy for the eyes-closed condition.

The three subjects that show the Glx/GABA+ ratio > 3.6 in subplot 2a are in the SC group, whereas the correlations plotted in figure 2c are only for the CC group, where the highest score is indeed ~3.6.

(3.4) Interpretation of aperiodic signal:

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

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

In the revised manuscript, we have cited those studies not already included in the Introduction (Page 3, Lines 92-94).

- Especially the aperiodic intercept is a very sensitive measure to many influences (e.g. skull thickness, electrode impedance...). As crucial results (correlation aperiodic intercept and MRS measures) are facing this problem, this needs to be reevaluated. It is safer to make statements on the aperiodic slope than intercept. In theory, some of the potentially confounding measures are available to the authors (e.g. skull thickness can be computed from T1w images; electrode impedances are usually acquired alongside the EEG data) and could be therefore controlled.

All electrophysiological measures indeed depend on parameters such as skull thickness and electrode impedance. As in the extant literature using neurophysiological measures to compare brain function between patient and control groups, we used a control group matched in age/sex, recruited in the same region, tested with the same devices, and analyzed with the same analysis pipeline. For example, impedance was kept below 10 kOhm for all subjects.

This is now mentioned in the Methods, Page 13, Line 344.

There is no evidence available suggesting that congenital cataracts are associated with changes in skull thickness that would cause the observed pattern of group results. Moreover, we cannot think of how any of the exploratory correlations between neurophysiological measures and MRS measures could be accounted for by a difference e.g. in skull thickness.

- The authors wrote: "Higher frequencies (such as 20-40 Hz) have been predominantly associated with local circuit activity and feedforward signaling (Bastos et al., 2018; Van Kerkoerle et al., 2014); the increased 20-40 Hz slope may therefore signal increased spontaneous spiking activity in local networks. We speculate that the steeper slope of the aperiodic activity for the lower frequency range (1-20 Hz) in CC individuals reflects the concomitant increase in inhibition." The authors confuse the interpretation of periodic and aperiodic signals. This section refers to the interpretation of the periodic signal (higher frequencies). This interpretation cannot simply be translated to the aperiodic signal (slope).

Prior work has not always separated the aperiodic and periodic components, making it unclear what might have driven these effects in our data. The interpretation of the higher frequency range was intended to contrast with the interpretations of lower frequency range, in order to speculate as to why the two aperiodic fits might go in differing directions. Note that Ossandón et al. reported highly similar results (group differences for CC individuals and for permanently congenitally blind humans) for the aperiodic activity between 20-40 Hz and oscillatory activity in the gamma range.

In the revised Discussion, we removed this section. We primarily interpret the increased offset and prior findings from fMRI-BOLD data (Raczy et al., 2023) as an increase in broadband neuronal firing.

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

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

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

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

(3.5) Problems with EEG preprocessing and analysis:

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

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

(3.6) Validity of GABA measurements and results:

- According the a newer study by the authors of the Gannet toolbox (https://analyticalsciencejournals.onlinelibrary.wiley.com/doi/abs/10.1002/nbm.5076), the reliability and reproducibility of the gamma-aminobutyric acid (GABA) measurement can vary significantly depending on acquisition and modeling parameter. Thus, did the author address these challenges?

We took care of data quality while acquiring MRS data by ensuring appropriate voxel placement and linewidth prior to scanning (Page 9, Lines 229-237). We now address this explicitly in the Methods in the “MRS Data Quality” section. Acquisition as well as modeling parameters were constant for both groups, so they cannot have driven group differences.

The linked article compares the reproducibility of GABA measurement using Osprey (Oeltzschner et al., 2020), which was released in 2020 and uses linear combination modeling to fit the peak, as opposed to Gannet’s simple peak fitting (Hupfeld et al., 2024). The study finds better test-retest reliability for Osprey compared to Gannet’s method.

As the present work was conceptualized in 2018, we used Gannet 3.0, which was the state-of-the-art edited-spectrum analysis toolbox at the time, and still is widely used.

In the revised manuscript, we re-analyzed the data using linear combination modeling with Osprey (Oeltzschner et al., 2020), and reported that the main findings remained the same, i.e. the Glx/GABA+ concentration ratio was lower in the visual cortex of congenital cataract reversal individuals compared to normally sighted controls, regardless of whether participants were scanned with eyes open or with eyes closed. Further, NAA concentration did not differ between groups (Supplementary Material S3). Thus, we demonstrate that our findings were robust to analysis pipelines, and state this in the Methods (Page 9, Lines 242-246) and Results (Page 19, Lines 464-467).

- Furthermore, the authors wrote: "We confirmed the within-subject stability of metabolite quantification by testing a subset of the sighted controls (n=6) 2-4 weeks apart. Looking at the supplementary Figure 5 (which would be rather plotted as ICC or Blant-Altman plots), the within-subject stability compared to between-subject variability seems not to be great. Furthermore, I don't think such a small sample size qualifies for a rigorous assessment of stability.

Indeed, we did not intend to provide a rigorous assessment of within-subject stability. Rather, we aimed to confirm that data quality/concentration ratios did not systematically differ between the same subjects tested longitudinally; driven, for example, by scanner heating or time of day. As with the phantom testing, we attempted to give readers an idea of the quality of the data, as they were collected from a primarily clinical rather than a research site.

In the revised manuscript, we have removed the statement regarding stability and the associated section.

- "Why might an enhanced inhibitory drive, as indicated by the lower Glx/GABA ratio" Is this interpretation really warranted, as the results of the group differences in the Glx/GABA ratio seem to be rather driven by a decreased Glx concentration in CC rather than an increased GABA (see Figure 2).

We used the Glx/GABA+ ratio as a measure, rather than individual Glx or GABA+ concentration, which did not significantly differ between groups. As detailed in Response 2.2, we think this metric aligns better with an underlying E/I balance hypothesis and has been used in many previous studies (Gao et al., 2024; Liu et al., 2015; Narayan et al., 2022; Perica et al., 2022).

Our interpretation of an enhanced inhibitory drive additionally comes from the combination of aperiodic EEG (1-20 Hz) and MRS measures, which, when considered together, are consistent with a decreased E/I ratio.

In the revised manuscript, we have rewritten the Discussion and removed this section.   

- Glx concentration predicted the aperiodic intercept in CC individuals' visual cortices during ambient and flickering visual stimulation. Why specifically investigate the Glx concentration, when the paper is about E/I ratio?

As stated in the methods, we exploratorily assessed the relationship between all MRS parameters (Glx, GABA+ and Glx/GABA+ ratio) with the aperiodic parameters (slope, offset), and corrected for multiple comparisons accordingly. We think this is a worthwhile analysis considering the rarity of the dataset/population (see 1.2, 1.6, 2.1 and Reviewer 1’s comments about future hypotheses). We only report the Glx – aperiodic intercept correlation in the main manuscript as it survived correction for multiple comparisons.

(3.7) Interpretation of the correlation between MRS measurements and EEG aperiodic signal:

- The authors wrote: "The intercept of the aperiodic activity was highly correlated with the Glx concentration during rest with eyes open and during flickering stimulation (also see Supplementary Material S11). Based on the assumption that the aperiodic intercept reflects broadband firing (Manning et al., 2009; Winawer et al., 2013), this suggests that the Glx concentration might be related to broadband firing in CC individuals during active and passive visual stimulation." These results should not be interpreted (or with very caution) for several reasons (see also problem with influences on aperiodic intercept and small sample size). This is a result of the exploratory analyses of correlating every EEG parameter with every MRS parameter. This requires well-powered replication before any interpretation can be provided. Furthermore and importantly: why should this be specifically only in CC patients, but not in the SC control group?

We have indicated clearly in all parts of the manuscript that these correlations are presented as exploratory. Further, we interpret the Glx-aperiodic offset correlation, and none of the others, as it survived the Bonferroni correction for multiple comparisons. We offer a hypothesis in the Discussion as to why such a correlation might exist in the CC but not the SC group (see response 2.2), and do not speculate further.

(3.8) Language and presentation:

- The manuscript requires language improvements and correction of numerous typos. Over-simplifications and unclear statements are present, which could mislead or confuse readers (see also interpretation of aperiodic signal).

In the revised manuscript, we have checked that speculations are clearly marked, and typos are removed.

- The authors state that "Together, the present results provide strong evidence for experience-dependent development of the E/I ratio in the human visual cortex, with consequences for behavior." The results of the study do not provide any strong evidence, because of the small sample size and exploratory analyses approach and not accounting for possible confounding factors.

We disagree with this statement and allude to convergent evidence of both MRS and neurophysiological measures. The latter link to corresponding results observed in a larger sample of CC individuals (Ossandón et al., 2023). In the revised manuscript, we have rephrased the statement as “to provide initial evidence” (Page 22, Line 676).

- "Our results imply a change in neurotransmitter concentrations as a consequence of *restoring* vision following congenital blindness." This is a speculative statement to infer a causal relationship on cross-sectional data.

As mentioned under 2.1, we conducted a cross-sectional study which might justify future longitudinal work. In order to advance science, new testable hypotheses were put forward at the end of a manuscript.

In the revised manuscript, we rephrased the sentence and added “might imply” to better indicate the hypothetical character of this idea (Page 22, Lines 586-587).

- In the limitation section, the authors wrote: "The sample size of the present study is relatively high for the rare population , but undoubtedly, overall, rather small." This sentence should be rewritten, as the study is plein underpowered. The further justification "We nevertheless think that our results are valid. Our findings neurochemically (Glx and GABA+ concentration), and anatomically (visual cortex) specific. The MRS parameters varied with parameters of the aperiodic EEG activity and visual acuity. The group differences for the EEG assessments corresponded to those of a larger sample of CC individuals (n=38) (Ossandón et al., 2023), and effects of chronological age were as expected from the literature." These statements do not provide any validation or justification of small samples. Furthermore, the current data set is a subset of an earlier published paper by the same authors "The EEG data sets reported here were part of data published earlier (Ossandón et al., 2023; Pant et al., 2023)." Thus, the statement "The group differences for the EEG assessments corresponded to those of a larger sample of CC individuals (n=38) " is a circular argument and should be avoided.

Our intention was not to justify having a small sample, but to justify why we think the results might be valid as they align with/replicate existing literature.

In the revised manuscript, we added a figure showing that the EEG results of the 10 subjects considered here correspond to those of the 28 other subjects of Ossandón et al (Supplementary Material S18). We adapted the text accordingly, clearly stating that the pattern of EEG results of the ten subjects reported here replicate those of the 28 additional subjects of Ossandón et al. (2023) (Page 25, Lines 671-672).

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Recommendations for the Authors:

Reviewer #1 (Recommendations for The Authors):

Thank you for the interesting submission. I have inserted my comments to the authors here. Some of them will be more granular comments related to the concerns raised in the public review.

(1) Introduction:

Could you please justify the rationale for using eyes open and eyes closed in the MRS condition, and the use of the three different conditions in the EEG experiment? If these resulted in negative findings, then the implications should be discussed.

Previous work with MRS in sighted individuals has suggested that eye opening in darkness results in a decrease of visual cortex GABA+ concentration, while visual stimulation results in an increase of Glx concentration, compared to a baseline concentration at eye closure (Kurcyus et al., 2018). Moreover visual stimulation/eye opening is known to result in an alpha desynchronization (Adrian & Matthews, 1934).

While previous work of our group has shown significantly reduced alpha oscillatory activity in congenital cataract reversal individual, desynchronization following eye opening was indistinguishable when compared to normally sighted controls (Ossandón et al., 2023; Pant et al., 2023).

Thus, we decided to include both conditions to test whether a similar pattern of results would emerge for GABA+/Glx concentration.

We added our motivation to the Introduction of the revised manuscript (Page 4, Lines 122-125) along with the Methods (Page 9, Lines 219-223).

It does not become clear from the introduction why a higher intercept is predicted in the EEG measure. The rationale for this hypothesis needs to be explained better.

Given the prior findings suggesting an increased E/I ratio in CC individuals and the proposed link between neuronal firing (Manning et al., 2009) and the aperiodic intercept, we expected a higher intercept for the CC compared to the SC group.

We have now added this explanation to the Introduction (Page 4, Lines 126-128).

(2) Participants

Were participants screened for common MRS exclusion criteria such as history of psychiatric conditions or antidepressant medication, which could alter neurochemistry? If not, then this needs to be pointed out.

All participants were clinically screened at the LV Prasad Eye Institute, and additionally self-reported no neurological or psychiatric conditions or medications. Moreover, all subjects were screened based exclusion criteria for being scanned using the standard questionnaire of the radiology center.

We have now made this clear in the Methods (Page 7, Lines 168-171).

Table 1 needs to show the age of the participant, which can only be derived by adding the columns 'duration of deprivation' and 'time since surgery'. Table 1 also needs to include the controls.

We have accordingly modified Table 1 in the revised manuscript and added age for the patients as well as the controls (Table 1, Pages 6-7).

The control cohort is not specific enough to exclude reduced visual acuity, or co-morbidities, as the primary driver of the differences between groups. Ideally, a cohort with developmental cataracts is recruited. Normally sighted participants as a control cohort cannot distinguish between different types of sight loss, or stages of plasticity.

The goal of this study was not to distinguish between different types of sight loss or stages of plasticity. We aimed to assess whether the most extreme forms of visual deprivation (i.e. congenital and total patterned vision loss) affected the E/I ratio. Low visual acuity and nystagmus are genuine diagnostic criteria (Methods, Page 5, Lines 142-145). Visual acuity cannot solely explain the current findings, since the MRS data were acquired both with eyes closed or diffuse visual stimulation in a dimly lit room, without any visual task.

With the awareness of the present results, we consider it worthwhile for the future to investigate additional groups such as developmental cataract-reversal individuals, to narrow down the contribution of the age of onset and degree of visual deprivation to the observed group differences.

(3) Data collection and analysis

- More detail is needed: how long were the sessions, how long was each part?

We have added this information on Page 7, Lines 178-181 of the Methods. MRS scanning took between 45 and 60 minutes, EEG testing took 20 minutes excluding the time for capping, and visual acuity testing took 3-5 minutes.

- It should be mentioned here that the EEG data is a reanalysis of a subset of legacy data, published previously in Ossandón et al., 2023; Pant et al., 2023.

In the revised manuscript, we explicitly state at the beginning of the “Electrophysiology recordings” section of the Methods (Page 13, Lines 331-334) that the EEG datasets were a subset of previously published data.

(4) MRS Spectroscopy

- Please fill out the minimum reporting standards form (Lin et al., 2021), or report all the requested measures in the main document https://pubmed.ncbi.nlm.nih.gov/33559967/

We have now filled out this form and added it as Supplementary Material (Supplementary Excel File 1). Additionally, all the requested information has been moved to the Methods section of the main document (MRS Data Quality, Pages 10-12).

- Information on how the voxels were placed is missing. The visual cortex voxel is not angled parallel to the calcarine, as is a common way to capture processing in the early visual cortex. Describe in the paper what the criteria for successful placement were, and how was it ensured that non-brain tissue was avoided in a voxel of this size.

Voxel placement was optimized in each subject to avoid the meninges, ventricles, skull and subcortical structures, ensured by examining the voxel region across slices in the acquired T1 volume for each subject. Saturation bands were placed to nullify the skull signal during MRS acquisition, at the anterior (frontal) and posterior (visual) edge of the voxel for every subject. Due to limitations in the clinical scanner rotated/skewed voxels were not possible, and thus voxels were not always located precisely parallel to the calcarine.

We have added this information to Page 9 (Lines 229-237) of the revised manuscript.

- Figure 1. shows voxels that are very close to the edge of the brain (frontal cortex) or to the tentorium (visual cortex). Could the authors please calculate the percentage overlap between the visual cortex MRS voxel and the visual cortex, and compare them across groups to ensure that there is no between-group bias from voxel placement?

We have now added the requested analysis to Supplementary Material S2 and referred to it in the main manuscript on Page 9, Lines 236-237.

Briefly, the percentage overlap with areas V1-V6 in every individual subject’s visual cortex voxel was 60% or more; the mean overlap in the CC group was 67% and the SC group 70%. The percentage overlap did not differ between groups ( t-test (t(18) = -1.14, p = 0.269)).

- Figure 1. I would recommend displaying data on a skull-stripped image to avoid identifying information from the participant's T1 profile.

We have now replaced the images in Figure 1 with skull-stripped images. Note that images from SPM12 were used instead of GannetCoregister, as GannetCoregister only displays images with the skull.

- Please show more rigor with the MRS quality measures. Several examples of inconsistency and omissions are below.

• SNR was quantified and shows a difference in SNR between voxel positions, with lower SNR in the frontal cortex. No explanation or discussion of the difference was provided.

• Looking at S1, the linewidth of NAA seems to be a lot broader in the frontal cortex than in the visual cortex. The figures suggest that acquisition quality was very different between voxel locations, making the comparison difficult.

• Linewidth of NAA is a generally agreed measure of shim quality in megapress acquisitions (Craven et al., 2022).

The data quality difference between the frontal and visual cortices has been observed in the literature (Juchem & Graaf, 2017; Rideaux et al., 2022). We nevertheless chose a frontal cortex voxel as control site instead of the often-chosen sensorimotor cortex. The main motivation was to avoid any cortical region linked to sensory processing since crossmodal compensation as a consequence of visual deprivation is a well-documented phenomenon.

We now make this clearer in the Methods (Page 11, Lines 284 – 299), in the Discussion/Limitations (Page 25, Lines 662 - 665).  

- To get a handle on the data quality, I would recommend that the authors display their MRS quality measures in a separate section 'MRS quality measure', including NAA linewidth, NAA SNR, GABA+ CRLB, Glx CRLB, and test for the main effects and interaction of voxel location (VC, FC) and group (SC, CC) and discuss any discrepancies.

We have moved all the quality metric values for GABA+, Glx and NAA from the supplement to the Methods section (see Table 2), and added the requested section titled “MRS Data quality.”

We have conducted the requested analyses and reported them in Supplementary Material S6: there was a strong effect of region confirming that data quality was better in the visual than frontal region. We have referred to this in the main manuscript on Page 11, Line 299.

In the revised manuscript, we discuss the data quality in the frontal cortex, and how we ensured it was comparable to prior work. Moreover, there were no significant group effects, or group-by-region interactions, suggesting that group differences observed for the visual cortex voxel cannot be accounted for by differences in data quality. We now included a section on data quality, both in the Methods (Page 11, Lines 284 – 299), and the limitations section of the Discussion (Page 25, Lines 662 - 665).

Please clarify the MRS acquisition, "Each MEGA- PRESS scan lasted for 8 minutes and was acquired with the following specifications: TR = 2000 ms, TE = 68 ms, Voxel size = 40 mm x 30 mm x 25mm, 192 averages (each consists of two TRs). "192 averages x 2 TRs x 2s TR = 12.8 min, not 8 min, apologies if I have misunderstood these details.

We have corrected this error in the revised manuscript and stated the parameters more clearly – there were a total of 256 averages, resulting in an (256 repetitions with 1 TR * 2 s/60) 8.5-minute scan (Page 8, Lines 212-213).

- What was presented to participants in the eyes open MRS? Was it just normal room illumination or was it completely dark? Please add details to your methods.

The scans were conducted in regular room illumination, with no visual stimulation.

We have now clarified this on Page 9 (Lines 223-224) of the Methods.

(5) MRS analysis

How was the tissue fraction correction performed? Please add or refer to the exact equation from Harris et al., 2015.

We have clarified that the reported GABA+/Glx values are water-normalized alpha corrected values (Page 10, Line 249), and cited Harris et al., 2015 on Page 10 (Line 251) of the Methods.

(6) Statistical approach

How was the sample size determined? Please add your justification for the sample size

We collected as many qualifying patients as we were able to recruit for this study within 2.5 years of data collection (commencing August 2019, ending February 2022), given the constraints of the patient population and the pandemic. We have now made this clear in the Discussion (Page 25, Lines 650-652).

Please report the tests for normality.

We have now reported the Shapiro-Wilk test results for normality as well as Levene’s test for homogeneity of variance between groups for every dependent variable in our dataset in Supplementary Material S9, and added references to it in the descriptions of the statistical analyses (Methods, Page13, Lines 326-329 and Page 15, Lines 400-402).

Calculate the Bayes Factor where possible.

As our analyses are all frequentist, instead of re-analyzing the data within a Bayesian framework, we added partial eta squared values for all the reported ANOVAs (η_p^²) for readers to get an idea of the effect size (Results).

I recommend partial correlations to control for the influence of age, duration, and time of surgery, rather than separate correlations.

Given the combination of small sample size and the expected multicollinearity in our variables (duration of blindness, for example, would be expected to correlate with age, as well as visual acuity post-surgery), partial correlations could not be calculated on this data.

We are aware of the limits of correlational analyses. Given the unique data set of a rare population we had exploratorily planned to relate behavioral, EEG and MRS parameters by calculating correlations. Since no similar data existed when we started (and to the best of our knowledge our data set is still unique), these correlation analyses were explorative, but the most transparent to run.

We have now clearly outlined these limitations in our Introduction (Page 5, Lines 133-135), Methods (Page 15, Lines 408-410) and Discussion section (Page 24, Line 634, Page 25, Lines 652-65) to ensure that the results are interpreted with appropriate caution.

(7) Visual acuity

Is the VA monocular average, from the dominant eye, or bilateral?

We have now clarified that the VA reported here is bilateral (Methods, Page 7 Line 165 and Page 15, Line 405). Bilateral visual acuity in congenital cataract-reversal individuals typically corresponds to the visual acuity of the best eye.

It is mentioned here that correlations with VA are exploratory, please be consistent as the introduction mentions that there was a hypothesis that you sought to test.

We have now accordingly modified the Introduction (Page 5, Lines 133-135) and added the appropriate caveats in the discussion with regards to interpretations (Page 25, Lines 652-665).

(8) Correlation analyses between MRS and EEG

It is mentioned here that correlations between EEG and MRS are exploratory, please consistently point out the exploratory nature, as these results are preliminary and should not be overinterpreted ("We did not have prior hypotheses as to the best of our knowledge no extant literature has tested the correlation between aperiodic EEG activity and MRS measures of GABA+,Glx and Glx/GABA+." ).

In the revised manuscript, we explicitly state the reported associations between EEG (aperiodic component) and MRS parameters allow for putting forward directed / more specific hypotheses for future studies (Introduction, Page 5, Lines 133-135; Methods, Page 15, Line 415. Discussion, Page 25, Lines 644-645 and Lines 652-665).

(9) Results

Figure 2 uses the same y-axis for the visual cortex and frontal cortex to facilitate a comparison between the two locations. Comparing Figure 2 a with b demonstrates poorer spectral peaks and reduced amplitudes. Lower spectral quality in the frontal cortex voxel could contribute to the absence of a group effect in the control voxel location. The major caveat that spectral quality differs between voxels needs to be pointed out and the limitations thereof discussed.

We have now explicitly pointed out this issue in the Methods (MRS Data Quality, Supplementary Material S6) and Discussion in the Limitations section (Page 25, Lines 662-665). While data quality was lower for the frontal compared to the visual cortex voxels, as has been observed previously (Juchem & Graaf, 2017; Rideaux et al., 2022), this was not an issue for the EEG recordings. Thus, lower sensitivity of frontal measures cannot easily explain the lack of group differences for frontal measures. Crucially, data quality did not differ between groups.

The results in 2c are the result of multiple correlations with metabolite values ("As in previous studies, we ran a number of exploratory correlation analyses between GABA+, Glx, and Glx/GABA+ concentrations, and visual acuity at the date of testing, duration of visual deprivation, and time since surgery respectively in the CC group"), it seems at least six for the visual acuity measure (VA vs Glx, VA vs GABA+, VA vs Glx/GABA+ x 2 conditions). While the trends are interesting, they should be interpreted with caution because of the exploratory nature, small sample size, the lack of multiple comparison correction, and the influence of two extreme data points. The authors should not overinterpret these results and should point out the need for replication.

See response to (6) last section, which we copy here for convenience:

We are aware of the limits of correlational analyses. Given the unique data set of a rare population we exploratorily related behavioral, EEG and MRS parameters by calculating correlations. Since no similar data existed when we started (and to the best of our knowledge our data set is still unique), these correlation analyses were explorative, but the most transparent to run.

We have now clearly outlined these limitations in our Discussion section to ensure that the results are interpreted with appropriate caution (Discussion, Page 25, Lines 644-645 and Lines 652-665).

(10) Discussion:

Please explain the decrease in E/I balance from MRS in view of recent findings on an increase in E/I balance in CC using RSN-fMRI (Raczy et al., 2022) and EEG (Ossandon et al. 2023).

We have edited our Abstract (Page 1-2, Lines 31-35) and Discussion (Page 23, Lines 584-590; Page 24, Lines 613-620). In brief, we think our results reflect a homeostatic regulation of E/I balance, that is, an increase in inhibition due to an increase in stimulus driven excitation following sight restoration.

Names limitations but does nothing to mitigate concerns about spatial specificity. The limitations need to be rewritten to include differences in SNR between the visual cortex and frontal lobe. Needs to include caveats of small samples, including effect inflation.

We have now discussed the data quality differences between the visual and frontal cortex voxel in MRS data quality, which we find irrespective of group (MRS Data Quality, Supplementary Material S6). We also reiterate why this might not explain our results; data quality was comparable to prior studies which have found group differences in frontal cortex (Methods Page 11, Lines 284 – 299), and data quality did not differ between groups. Further, EEG data quality did not differ across frontal and occipital regions, but group differences in EEG datasets were localized to the occipital cortex.

Reviewer #2 (Recommendations for The Authors):

To address the main weakness, the authors could consider including data from a third group, of congenitally blind individuals. Including this would go a very long way towards making the findings interpretable and relating them to the rest of the literature.

Unfortunately, recruitment of these groups was not possible due to the pandemic. Indeed, we would consider a pre- vs post- surgery approach the most suitable design in the future, which, however, will require several years to be completed. Such time and resource intensive longitudinal studies are justified by the present cross-sectional results.

We have explicitly stated our contribution and need for future studies in the Limitations section of the Discussion (Page 25, Lines 650-657).

Analysing the amplitude of alpha rhythms, as well as the other "aperiodic" components, would be useful to relate the profile of the tested patients with previous studies. Visual inspection of Figure 3 suggests that alpha power with eyes closed is not reduced in the patients' group compared to the controls. This would be inconsistent with previous studies (including research from the same group) and it could suggest that the small selected sample is not really representative of the sight-recovery population - certainly one of the most heterogeneous study populations. This further highlights the difficulty of drawing conclusions on the effects of visual experience merely based on this N=10 set of patients.

Alpha power was indeed reduced in the present subsample of 10 CC individuals (Supplementary Material S19). A possible source of the confusion (that the graphs of the CC and SC group look so similar for the EC condition in Figure 3) likely is that the spectra are shown with aperiodic components not yet removed, and scales to accommodate very different alpha power values. As documented in Supplementary Material S18 and S19, alpha power and the aperiodic intercept/slope results of the resting state data in the present 10 CC individuals correspond to the results from a larger sample of CC individuals (n = 28) in Ossandón et al., 2023. We explicitly highlight this “replication” in the main manuscript (Page 25 -26, Lines 671-676). Thus, the present sub-sample of CC individuals are representative for their population.

To further characterise the MRS results, the authors may consider an alternative normalisation scheme. It is not clear whether the lack of significant GABA and GLX differences in the face of a significant group difference in the GLX/GABA ratio is due to the former measures being noisier since taking the ratio between two metabolites often helps reduce inter-individual variability and thereby helps revealing group differences. It remains an open question whether the GABA or GLX concentrations would show significant group differences after appropriate normalisation (e.g. NAA?).

We repeated the analysis with Creatine-normalized values of GABA+ and Glx, and the main results i.e. reduced Glx/GABA+ concentration in the visual cortex of CC vs SC individuals, and no such difference in the frontal cortex, remained the same (Supplementary Material S5).

Further, we re-analyzed the data using Osprey, an open-source toolbox that uses linear combination modeling, and found once more that our results did not change (Supplementary Material S3). We refer to these findings in the Methods (Page 10, Lines 272-275) and Results (Page 10, Lines 467-471) of the main manuscript.

In fact, the Glx concentration in the visual cortex of CC vs SC individuals was significantly decreased when Cr-normalized values were used (which was not significant in the original analysis). However, we do not interpret this result as it was not replicated with the water-normalized values from Gannet or Osprey.

I suggest revising the discussion to present a more balanced picture of the existent evidence of the relation between E/I and EEG indices. Although there is evidence that the 1/f slope changes across development, in a way that could be consistent with a higher slope reflecting more immature and excitable tissue, the link with cortical E/I is far from established, especially when referring to specific EEG indices (intercept vs. slope, measured in lower vs. higher frequency ranges).

We have revised the Introduction (Page 4, Line 91, Lines 101-102) and Discussion (Page 22, Lines 568-569, Page 24, Lines 645-647 and Lines 654-657) in the manuscript accordingly; we allude to the fact that the links between cortical E/I and aperiodic EEG indices have not yet been unequivocally established in the literature.

Minor:

- The authors estimated NAA concentration with different software than the one used to estimate GLX and GABA; this examined the OFF spectra only; I suggest that the authors consider running their analysis with LCModel, which would allow a straightforward approach to estimate concentrations of all three metabolites from the same edited spectrum and automatically return normalised concentrations as well as water-related ones.

We re-analyzed all of the MRS datasets using Osprey, which uses linear combination modelling and has shown quantification results similar to LCModel for NAA (Oeltzschner et al., 2020). The results of a lower Glx/GABA+ concentration in the visual cortex of CC vs SC individuals, and no difference in NAA concentration, were replicated using this pipeline.

We have now added these analyses to the Supplementary Material S3 and referred to them in the Methods (Page 9, Lines 242-246) and Results (Page 18, Lines 464-467).

- Of course the normalisation used to estimate GABA and GLX values is completely irrelevant when the two values are expressed as ratio GLX/GABA - this may be reflected in the text ("water normalised GLX/GABA concentration" should read "GLX/GABA concentration" instead).

We have adapted the text on Page 16 (Line 431) and have ensured that throughout the manuscript the use of “water-normalized” is in reference to Glx or GABA+ concentration, and not the ratio.

- Please specify which equation was used for tissue correction - is it alpha-correction?

We have clarified that the reported GABA+/Glx values are water-normalized alpha corrected values (Page 10, Line 249), and cited Harris et al., 2015 on Page 10 (Line 251) of the Methods.

- Since ANOVA was used, the assumption is that values are normally distributed. Please report evidence supporting this assumption.

We have now reported the Shapiro-Wilk test results for normality as well as Levene’s test for homogeneity of variance between groups for every dependent variable in our dataset in Supplementary Material S9, and added references to it in the Methods (Page 13, Lines 326-329 and Page 15, Lines 400-402).

Reviewer #3 (Recommendations for The Authors):

In addition to addressing major comments listed in my Public Review, I have the following, more granular comments, which should also be addressed:

(1) The paper's structure could be improved by presenting visual acuity data before diving into MRS and EEG results to better contextualize the findings.

We now explicitly state in the Methods (Page 5, Line 155) that lower visual acuity is expected in a cohort of CC individuals with long lasting congenital visual deprivation.

We have additionally included a plot of visual acuities of the two groups (Supplementary Material S1).

(2) The paper should better explain the differences between CC for which sight is restored and congenitally blind patients. The authors write in the introduction that there are sensitive periods/epochs during the lifespan for the development of local inhibitory neural circuits. and "Human neuroimaging studies have similarly demonstrated that visual experience during the first weeks and months of life is crucial for the development of visual circuits. If human infants born with dense bilateral cataracts are treated later than a few weeks from birth, they suffer from a permanent reduction of not only visual acuity (Birch et al., 1998; Khanna et al., 2013) and stereovision (Birch et al., 1993; Tytla et al., 1993) but additionally from impairments in higher-level visual functions, such as face perception (Le Grand et al., 2001; Putzar et al., 2010; Röder et al., 2013)...".

Thus it seems that the current participants (sight restored after a sensitive period) seem to be similarly affected by the development of the local inhibitory circuits as congenitally blind. To assess the effect of plasticity and sight restoration longitudinal data would be necessary.

In the Introduction (Page 2, Lines 59-64; Page 3, Lines 111-114) we added that in order to identify sensitive periods e.g. for the elaboration of visual neural circuits, sight recovery individuals need to be investigated. The study of permanently blind individuals allows for investigating the role of experience (whether sight is necessary to introduce the maturation of visual neural circuits), but not whether visual input needs to be available at early epochs in life (i.e. whether sight restoration following congenital blindness could nevertheless lead to the development of visual circuits).

This is indeed the conclusion we make in the Discussion section. We have now highlighted the need for longitudinal assessments in the Discussion (Page 25, Lines 654-656).

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

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

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

(4) "For this scan, participants were instructed to keep their eyes closed and stay as still as possible." Why should it be important to have the eyes closed during a T1w data acquisition? This statement at this location does not make sense.

To avoid misunderstandings, we removed this statement in this context.

(5) "Two SC subjects did not complete the frontal cortex scan for the EO condition and were excluded from the statistical comparisons of frontal cortex neurotransmitter concentrations."<br /> Why did the authors not conduct whole-brain MRS, which seems to be on the market for quite some time (e.g. https://www.ncbi.nlm.nih.gov/pmc/articles/PMC3590062/) ?

Similar to previous work (Coullon et al., 2015; Weaver et al., 2013) our hypothesis was related to the visual cortex, and we chose the frontal cortex voxel as a control. This has now been clarified in the Introduction (Page 4, Lines 103-114), Methods (Page 9, Lines 225-227) and Discussion (Page 25, Lines 662-665).

(6) In "....during visual stimulation with stimuli that changed in luminance (LU) (Pant et al., 2023)." the authors should provide a link on the visual stimulation, which is provided further below

In the revised manuscript, we have moved up the description of the visual stimulation (Page 13, Line 336).

(7) "During the EO condition, participants were asked to fixate on a blank screen." This is not really possible. Typically, resting state EO conditions include a fixation cross, as the participants would not be able to fixate on a blank screen and move their eyes, which would impact the recordings.

We have now rephrased this as “look towards” with the goal of avoiding eye movements (Page 14, Line 347).

(8) "Components corresponding to horizontal or vertical eye movements were identified via visual inspection and removed (Plöchl et al., 2012)." It is unclear what the Plöchl reference should serve for. Is the intention of the authors to state that manual (and subjective) visual inspection of the ICA components is adequate? I would recommend removing this reference.

The intention was to provide the basis for classification during the visual inspection, as opposed to an automated method such as ICLabel.

We stated this clearly in the revised manuscript (Page 14 Lines 368-370).

(9) "The datasets were divided into 6.25 s long epochs corresponding to each trial." This is a bit inaccurate, as the trial also included some motor response task. Thus, I assume the 6.25 s are related to the visual stimulation.

We have modified the sentence accordingly (Page 15, Line 378).

(10) Figure 2. a & b. Just an esthetic suggestion: I would recommend removing the lines between the EC and EO conditions, as they suggest some longitudinal changes. Unless it is important to highlight the changes between EC and EO within each subject.

In fact, EC vs. EO was a within-subject factor with expected changes for the EEG and possible changes in the MRS parameters. To allow the reader to track changes due to EC vs. EO for individual subjects (rather than just comparing the change in the mean scores), we use lines.  

(11) Figure 3A: I would plot the same y-axis range for both groups to make it more comparable.

We have changed Figure 3A accordingly.

(12) " flattening of the intercept" replaces flattening, as it is too related to slope.

We have replaced “flattening” with “reduction” (Page 20, Line 517).

(13) The plotting of only the significant correlation between MRS measures and EEG measures seems to be rather selective reporting. For this type of exploratory analysis, I would recommend plotting all of the scatter plots and moving the entire exploratory analysis to the supplementary (as this provides the smallest evidence of the results).

We have made clear in the Methods (Page 16, Lines 415-426), Results and Discussion (page 24, Lines 644-645), as well as in the Supplementary material, that the reason for only reporting the significant correlation was that this correlation survived correction for multiple comparisons, while all other correlations did not. We additionally explicitly allude to the Supplementary Material where the plots for all correlations are shown (Results, Page 21, Lines 546-552).

(14) "Here, we speculate that due to limited structural plasticity after a phase of congenital blindness, the neural circuits of CC individuals, which had adapted to blindness after birth, employ available, likely predominantly physiological plasticity mechanisms (Knudsen, 1998; Mower et al., 1985; Röder et al., 2021), in order to re-adapt to the newly available visual excitation following sight restoration."

I don't understand the logic here. The CC individuals are congenitally blind, thus why should there be any physiological plasticity mechanism to adapt to blindness, if they were blind at birth?

With “adapt to blindness” we mean adaptation of a brain to an atypical or unexpected condition when taking an evolutionary perspective (i.e. the lack of vision). We have made this clear in the revised manuscript (Introduction, Page 4, Lines 111-114; Discussion, Page 23, Lines 584-591).

(15) "An overall reduction in Glx/GABA ratio would counteract the aforementioned adaptations to congenital blindness, e.g. a lower threshold for excitation, which might come with the risk of runaway excitation in the presence of restored visually-elicited excitation."

This could be tested by actually investigating the visual excitation by visual stimulation studies.

The visual stimulation condition in the EEG experiment of the present study found a higher aperiodic intercept in CC compared to SC individuals. Given the proposed link between the intercept and spontaneous neural firing (Manning et al., 2009), we interpreted the higher intercept in CC individuals as increased broadband neural firing during visual stimulation (Results Figure 3; Discussion Page 24, Lines 635-640). This idea is compatible with enhanced BOLD responses during an EO condition in CC individuals (Raczy et al., 2022). Future work should systematically manipulate visual stimulation to test this idea.

(16) As the authors also collected T1w images, the hypothesis of increased visual cortex thickness in CC. Was this investigated?

This hypothesis was investigated in a separate publication which included this subset of participants (Hölig et al., 2023), and found increased visual cortical thickness in the CC group. We refer to this publication, and related work (Feng et al., 2021) in the present manuscript.

(17) The entire discussion of age should be omitted, as the current data set is too small to assess age effects.

We have removed this section and just allude to the fact that we replicated typical age trends to underline the validity of the present data (Page 26, Lines 675-676).

(18) Table1: should include the age and the age at the time point of surgery.

We added age to the revised Table 1. We clarified that in CC individuals, duration of blindness is the same as age at the time point of surgery (Page 6, Line 163).

(19) Why no group comparisons of visual acuity are reported?

Lower visual acuity in CC than SC individuals is a well-documented fact.

We have now added the visual acuity plots for readers (Supplementary Material S1, referred to in the Methods, Page 5, Line 155) which highlight this common finding.

References (Recommendations to the Authors)

Adrian, E. D., & Matthews, B. H. C. (1934). The berger rhythm: Potential changes from the occipital lobes in man. Brain. https://doi.org/10.1093/brain/57.4.355

Coullon, G. S. L., Emir, U. E., Fine, I., Watkins, K. E., & Bridge, H. (2015). Neurochemical changes in the pericalcarine cortex in congenital blindness attributable to bilateral anophthalmia. Journal of Neurophysiology. https://doi.org/10.1152/jn.00567.2015

Feng, Y., Collignon, O., Maurer, D., Yao, K., & Gao, X. (2021). Brief postnatal visual deprivation triggers long-lasting interactive structural and functional reorganization of the human cortex. Frontiers in Medicine, 8, 752021. https://doi.org/10.3389/FMED.2021.752021/BIBTEX

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

Hölig, C., Guerreiro, M. J. S., Lingareddy, S., Kekunnaya, R., & Röder, B. (2023). Sight restoration in congenitally blind humans does not restore visual brain structure. Cerebral Cortex, 33(5), 2152–2161. https://doi.org/10.1093/CERCOR/BHAC197

Juchem, C., & Graaf, R. A. de. (2017). B0 magnetic field homogeneity and shimming for in vivo magnetic resonance spectroscopy. Analytical Biochemistry, 529, 17–29. https://doi.org/10.1016/j.ab.2016.06.003

Kurcyus, K., Annac, E., Hanning, N. M., Harris, A. D., Oeltzschner, G., Edden, R., & Riedl, V. (2018). Opposite Dynamics of GABA and Glutamate Levels in the Occipital Cortex during Visual Processing. Journal of Neuroscience, 38(46), 9967–9976. https://doi.org/10.1523/JNEUROSCI.1214-18.2018

Manning, J. R., Jacobs, J., Fried, I., & Kahana, M. J. (2009). Broadband shifts in local field potential power spectra are correlated with single-neuron spiking in humans. The Journal of Neuroscience : The Official Journal of the Society for Neuroscience, 29(43), 13613–13620. https://doi.org/10.1523/JNEUROSCI.2041-09.2009

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

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

Oeltzschner, G., Zöllner, H. J., Hui, S. C. N., Mikkelsen, M., Saleh, M. G., Tapper, S., & Edden, R. A. E. (2020). Osprey: Open-source processing, reconstruction & estimation of magnetic resonance spectroscopy data. Journal of Neuroscience Methods, 343, 108827. https://doi.org/10.1016/j.jneumeth.2020.108827

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

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

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Weaver, K. E., Richards, T. L., Saenz, M., Petropoulos, H., & Fine, I. (2013). Neurochemical changes within human early blind occipital cortex. Neuroscience. https://doi.org/10.1016/j.neuroscience.2013.08.004

eLife Assessment

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

Reviewer #1 (Public review):

Summary

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

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

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

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

Strengths of study

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

Limitations

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

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

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

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

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

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

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

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

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

The updated document has addressed this caveat.

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

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

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

This caveat has been addressed in the revised manuscript.

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

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

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

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

Comments on the latest version:

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

Reviewer #2 (Public review):

Summary:

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

Strengths:

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

Weaknesses:

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

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

Conclusions:

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

Reviewer #3 (Public review):

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

First of all, I would like to disclose that I am not an expert in congenital visual deprivation, nor in MRS. My expertise is in EEG (particularly in the decomposition of periodic and aperiodic activity) and statistical methods. Although the authors addressed some of the concerns of the previous version, major concerns and flaws remain in terms of methodological and statistical approaches along with the (over)interpretation of the results. Specific concerns include:

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

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

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

Several points require clarification or improvement:<br /> (4) Correlation Methods: The manuscript does not specify whether the reported correlation analyses are based on Pearson or Spearman correlation.<br /> (5) Confidence Intervals: Include confidence intervals for correlations to represent the uncertainty associated with these estimates.<br /> (6) Permutation Statistics: Given the small sample size, I recommend using permutation statistics, as these are exact tests and more appropriate for small datasets.<br /> (7) Adjusted P-Values: Ensure that reported Bonferroni corrected p-values (e.g., p > 0.999) are clearly labeled as adjusted p-values where applicable.<br /> (8) Figure 2C<br /> Figure 2C still lacks crucial information that the correlation between Glx/GABA ratio and visual acuity was computed solely in the control group (as described in the rebuttal letter). Why was this analysis restricted to the control group? Please provide a rationale.<br /> (9 3.4) Interpretation of Aperiodic Signal<br /> Relying on previous studies to interpret the aperiodic slope as a proxy for excitation/inhibition (E/I) does not make the interpretation more robust.<br /> (10) Additionally, the authors state:<br /> "We cannot think of how any of the exploratory correlations between neurophysiological measures and MRS measures could be accounted for by a difference e.g. in skull thickness."<br /> (11) This could be addressed directly by including skull thickness as a covariate or visualizing it in scatterplots, for instance, by representing skull thickness as the size of the dots.<br /> (12 3.5) Problems with EEG Preprocessing and Analysis<br /> Downsampling: The decision to downsample the data to 60 Hz "to match the stimulation rate" is problematic. This choice conflates subsequent spectral analyses due to aliasing issues, as explained by the Nyquist theorem. While the authors cite prior studies (Schwenk et al., 2020; VanRullen & MacDonald, 2012) to justify this decision, these studies focused on alpha (8-12 Hz), where aliasing is less of a concern compared of analyzing aperiodic signal. Furthermore, in contrast, the current study analyzes the frequency range from 1-20 Hz, which is too narrow for interpreting the aperiodic signal as E/I. Typically, this analysis should include higher frequencies, spanning at least 1-30 Hz or even 1-45 Hz (not 20-40 Hz).<br /> (13) Baseline Removal: Subtracting the mean activity across an epoch as a baseline removal step is inappropriate for resting-state EEG data. This preprocessing step undermines the validity of the analysis. The EEG dataset has fundamental flaws, many of which were pointed out in the previous review round but remain unaddressed. In its current form, the manuscript falls short of standards for robust EEG analysis. If I were reviewing for another journal, I would recommend rejection based on these flaws.<br /> (14) The authors mention:<br /> "The EEG data sets reported here were part of data published earlier (Ossandón et al., 2023; Pant et al., 2023)." Thus, the statement "The group differences for the EEG assessments corresponded to those of a larger sample of CC individuals (n=38) " is a circular argument and should be avoided."<br /> The authors addressed this comment and adjusted the statement. However, I do not understand, why not the full sample published earlier (Ossandón et al., 2023) was used in the current study?

eLife Assessment

This valuable study provides insights into the structure and function of bacterial contractile injection systems that are present in the cytoplasm of many Streptomyces strains. A convincing high-resolution model of the structure of extended forms of the cytoplasmic contractile injection system assembly from Streptomyces coelicolor is presented, with some investigation of the membrane protein CisA in attachment of the extended assembly to the inner face of the cytoplasmic membrane and the firing of the system. The work expands the current understanding of these diverse bacterial nanomachines.

Reviewer #1 (Public review):

Contractile Injection Systems (CIS) are versatile machines that can form pores in membranes or deliver effectors. They can act extra or intracellularly. When intracellular they are positioned to face the exterior of the cell and hence should be anchored to the cell envelope. The authors previously reported the characterization of a CIS in Streptomyces coelicolor, including significant information on the architecture of the apparatus. However, how the tubular structure is attached to the envelope was not investigated. Here they provide a wealth of evidence to demonstrate that a specific gene within the CIS gene cluster, cisA, encodes a membrane protein that anchors the CIS to the envelope. More specifically, they show that:

- CisA is not required for assembly of the structure but is important for proper contraction and CIS-mediated cell death<br /> - CisA is associated to the membrane (fluorescence microscopy, cell fractionation) through a transmembrane segment (lacZ-phoA topology fusions in E. coli)<br /> - Structural prediction of interaction between CisA and a CIS baseplate component<br /> - In addition they provide a high-resolution model structure of the >750-polypeptide Streptomyces CIS in its extended conformation, revealing new details of this fascinating machine, notably in the baseplate and cap complexes.

All the experiments are well controlled including trans-complemented of all tested phenotypes.

One important information we miss is the oligomeric state of CisA.

While it would have been great to test the interaction between CisA and Cis11, to perform cryo-electron microscopy assays of detergent-extracted CIS structures to maintain the interaction with CisA, I believe that the toxicity of CisA upon overexpression or upon expression in E. coli render these studies difficult and will require a significant amount of time and optimization to be performed. It is worth mentioning that this study is of significant novelty in the CIS field because, except for Type VI secretion systems, very few membrane proteins or complexes responsible for CIS attachment have been identified and studied.

Reviewer #2 (Public review):

Summary:

The overall question that is addressed in this study is how the S. coelicolor contractile injection system (CISSc) works and affects both cell viability and differentiation, which it has been implicated to do in previous work from this group and others. The CISSc system has been enigmatic in the sense that it is free-floating in the cytoplasm in an extended form and is seen in contracted conformation (i.e. after having been triggered) mainly in dead and partially lysed cells, suggesting involvement in some kind of regulated cell death. So, how do the structure and function of the CISSc system compare to those of related CIS from other bacteria, does it interact with the cytoplasmic membrane, how does it do that, and is the membrane interaction involved in the suggested role in stress-induced, regulated cell death? The authors address these questions by investigating the role of a membrane protein, CisA, that is encoded by a gene in the CIS gene cluster in S. coelicolor. Further, they analyse the structure of the assembled CISSc, purified from the cytoplasm of S. coelicolor, using single-particle cryo-electron microscopy.

Strengths:

The beautiful visualisation of the CIS system both by cryo-electron tomography of intact bacterial cells and by single-particle electron microscopy of purified CIS assemblies are clearly the strengths of the paper, both in terms of methods and results. Further, the paper provides genetic evidence that the membrane protein CisA is required for the contraction of the CISSc assemblies that are seen in partially lysed or ghost cells of the wild type. The conclusion that CisA is a transmembrane protein and the inferred membrane topology are well supported by experimental data. The cryo-EM data suggest that CisA is not a stable part of the extended form of the CISSc assemblies. These findings raise the question of what CisA does.

Weaknesses:

The investigations of the role of CisA in function, membrane interaction, and triggering of contraction of CIS assemblies, are important parts of the paper and are highlighted in the title. However, the experimental data provided to answer these questions appear partially incomplete and not as conclusive as one would expect.

The stress-induced loss of viability is only monitored with one method: an in vivo assay where cytoplasmic sfGFP signal is compared to FM5-95 membrane stain. Addition of a sublethal level of nisin lead to loss of sfGFP signal in individual hyphae in the WT, but not in the cisA mutant (similarly to what was previously reported for a CIS-negative mutant). Technically, this experiment and the example images that are shown give rise to some concern. Only individual hyphal fragments are shown that do not look like healthy and growing S. coelicolor hyphae. Under the stated growth conditions, S. coelicolor strains would normally have grown as dense hyphal pellets. It is therefore surprising that only these unbranched hyphal fragments are shown in Fig. 4ab. Further, S. coelicolor would likely be in a stationary phase when grown 48 h in the rich medium that is stated, giving rise to concern about the physiological state of the hyphae that were used for the viability assay. It would be valuable to know whether actively growing mycelium is affected in the same way by the nisin treatment, and also whether the cell death effect could be detected by other methods.

The model presented in Fig. 5 suggests that stress leads to a CisA-dependent attachment of CIS assemblies to the cytoplasmic membrane, and then triggering of contraction, leading to cell death. This model makes testable predictions that have not been challenged experimentally. Given that sublethal doses of nisin seem to trigger cell death, there appear to be possibilities to monitor whether activation of the system (via CisA?) indeed leads to at least temporally increased interaction of CIS with the membrane. Further, would not the model predict that stress leads to an increased number of contracted CIS assemblies in the cytoplasm? No clear difference in length of the isolated assemblies if Fig. S7 is seen between untreated and nisin-exposed cells, and also no difference between assemblies from WT and cisA mutant hyphae.

The interaction of CisA with the CIS assembly is critical for the model but is only supported by Alphafold modelling, predicting interaction between cytoplasmic parts of CisA and Cis11 protein in the baseplate wedge. An experimental demonstration of this interaction would have strengthened the conclusions.

The cisA mutant showed a similarly accelerated sporulation as was previously reported for CIS-negative strains, which supports the conclusion that CisA is required for function of CISSc. But the results do not add any new insights into how CIS/CisA affects the progression of the developmental life cycle and whether this effect has anything to do with the regulated cell death that is caused by CIS. The same applies to the effect on secondary metabolite production, with no further mechanistic insights added, except reporting similar effects of CIS and CisA inactivations.

Concluding remarks:<br /> The work will be of interest to anyone interested in contractile injection systems, T6SS, or similar machineries, as well for people working on the biology of streptomycetes. There is also a potential impact of the work in the understanding of how such molecular machineries could have been co-opted during evolution to become a mechanism for regulated cell death. However, this latter aspect remains still poorly understood. Even though this paper adds excellent new structural insights and identifies a putative membrane anchor, it remains elusive how the Streptomyces CIS may lead to cell death. It is also unclear what the advantage would be to trigger death of hyphal compartments in response to stress, as well as how such cell death may impact (or accelerate) the developmental progression. Finally, it is inescapable to wonder whether the Streptomyces CIS could have any role in protection against phage infection.

Reviewer #3 (Public review):

Summary:

In this work, Casu et al. have reported the characterization of a previously uncharacterized membrane protein CisA encoded in a non-canonical contractile injection system of Streptomyces coelicolor, CISSc, which is a cytosolic CISs significantly distinct from both intracellular membrane-anchored T6SSs and extracellular CISs. The authors have presented the first high-resolution structure of extended CISSc structure. It revealed important structural insights in this conformational state. To further explore how CISSc interacted with cytoplasmic membrane, they further set out to investigate CisA that was previously hypothesized to be the membrane adaptor. However, the structure revealed that it was not associated with CISSc. Using fluorescence microscope and cell fractionation assay, the authors verified that CisA is indeed a membrane-associated protein. They further determined experimentally that CisA had a cytosolic N-terminal domain and a periplasmic C-terminus. The functional analysis of cisA mutant revealed that it is not required for CISSc assembly but is essential for the contraction, as a result, the deletion significantly affects CISSc-mediated cell death upon stress, timely differentiation, as well as secondary metabolite production. Although the work did not resolve the mechanistic detail how CisA interacts with CISSc structure, it provides solid data and a strong foundation for future investigation toward understanding the mechanism of CISSc contraction, and potentially, the relation between the membrane association of CISSc, the sheath contraction and the cell death.

Strengths:

The paper is well-structured, and the conclusion of the study is supported by solid data and careful data interpretation was presented. The authors provided strong evidence on (1) the high-resolution structure of extended CISSc determined by cryo-EM, and the subsequent comparison with known eCIS structures, which sheds light on both its similarity and different features from other subtypes of eCISs in detail; (2) the topological features of CisA using fluorescence microscopic analysis, cell fractionation and PhoA-LacZα reporter assays, (3) functions of CisA in CISSc-mediated cell death and secondary metabolite production, likely via the regulation of sheath contraction.

Weaknesses:

The data presented are not sufficient to provide mechanistic details of CisA-mediated CISSc contraction, as authors are not able to experimentally demonstrate the direct interaction between CisA with baseplate complex of CISSc (hypothesized to be via Cis11 by structural modeling), since they could not express cisA in E. coli due to its potential toxicity. Therefore, there is a lack of biochemical analysis of direct interaction between CisA and baseplate wedge. In addition, there is no direct evidence showing that CisA is responsible for tethering CISSc to the membrane upon stress, and the spatial and temporal relation between membrane association and contraction remains unclear. Further investigation will be needed to address these questions in future.

Discussion:

Overall, the work provides a valuable contribution to our understanding on the structure of a much less understood subtype of CISs, which is unique compared to both membrane-anchored T6SSs and host-membrane targeting eCISs. Importantly, the work serves as a good foundation to further investigate how the sheath contraction works here. The work contributes to expanding our understanding of the diverse CIS superfamilies.

Author response:

We thank the editor and the three reviewers for the positive assessment and constructive feedback on how to improve our manuscript. We greatly appreciate that our work is considered valuable to the field, the recognition of the high-resolution model we presented, and the comments on our investigation of CisA’s role in the attachment and firing mechanism of the extended assembly. It is truly gratifying to know that our study contributes to expanding the current understanding of the biology of Streptomyces and the role of these functionally diverse and fascinating bacterial nanomachines.

We have provided specific responses to each reviewer's comments below. In summary, we intend to address the following requested revisions:

We will expand our bioinformatic analysis of CisA and provide additional information on the oligomeric state of CisA. We will also modify the text, figures, and figure legends to improve the clarity of our work and experimental procedures.

Some reviewer comments would require additional experimental work, some of which would involve extensive optimization of experimental conditions. Because both lead postdoctoral researchers involved in this work have now left the lab, we currently do not have the capability to perform additional experimental work.

Reviewer #1 (Public review):

Contractile Injection Systems (CIS) are versatile machines that can form pores in membranes or deliver effectors. They can act extra or intracellularly. When intracellular they are positioned to face the exterior of the cell and hence should be anchored to the cell envelope. The authors previously reported the characterization of a CIS in Streptomyces coelicolor, including significant information on the architecture of the apparatus. However, how the tubular structure is attached to the envelope was not investigated. Here they provide a wealth of evidence to demonstrate that a specific gene within the CIS gene cluster, cisA, encodes a membrane protein that anchors the CIS to the envelope. More specifically, they show that:

- CisA is not required for assembly of the structure but is important for proper contraction and CIS-mediated cell death

- CisA is associated to the membrane (fluorescence microscopy, cell fractionation) through a transmembrane segment (lacZ-phoA topology fusions in E. coli)

- Structural prediction of interaction between CisA and a CIS baseplate component<br /> - In addition they provide a high-resolution model structure of the >750-polypeptide Streptomyces CIS in its extended conformation, revealing new details of this fascinating machine, notably in the baseplate and cap complexes.

All the experiments are well controlled including trans-complemented of all tested phenotypes.

One important information we miss is the oligomeric state of CisA.

While it would have been great to test the interaction between CisA and Cis11, to perform cryo-electron microscopy assays of detergent-extracted CIS structures to maintain the interaction with CisA, I believe that the toxicity of CisA upon overexpression or upon expression in E. coli render these studies difficult and will require a significant amount of time and optimization to be performed. It is worth mentioning that this study is of significant novelty in the CIS field because, except for Type VI secretion systems, very few membrane proteins or complexes responsible for CIS attachment have been identified and studied.

We thank this reviewer for their highly supportive and positive comments on our manuscript. We are grateful for this reviewer’s recognition of the novelty of our study, particularly in the context of membrane proteins and complexes involved in CIS attachment.

We agree that further experimental evidence on the direct interaction between CisA and Cis11 would have strengthened our model of CisA function. However, as noted by this reviewer, this additional work is technically challenging and currently beyond the scope of this study.

We thank Reviewer #1 for suggesting discussing the potential oligomeric state of CisA. We will perform additional AlphaFold modelling of CisA and discuss the result of this analysis in the revised manuscript.

Reviewer #2 (Public review):

Summary:

The overall question that is addressed in this study is how the S. coelicolor contractile injection system (CISSc) works and affects both cell viability and differentiation, which it has been implicated to do in previous work from this group and others. The CISSc system has been enigmatic in the sense that it is free-floating in the cytoplasm in an extended form and is seen in contracted conformation (i.e. after having been triggered) mainly in dead and partially lysed cells, suggesting involvement in some kind of regulated cell death. So, how do the structure and function of the CISSc system compare to those of related CIS from other bacteria, does it interact with the cytoplasmic membrane, how does it do that, and is the membrane interaction involved in the suggested role in stress-induced, regulated cell death? The authors address these questions by investigating the role of a membrane protein, CisA, that is encoded by a gene in the CIS gene cluster in S. coelicolor. Further, they analyse the structure of the assembled CISSc, purified from the cytoplasm of S. coelicolor, using single-particle cryo-electron microscopy.

Strengths:

The beautiful visualisation of the CIS system both by cryo-electron tomography of intact bacterial cells and by single-particle electron microscopy of purified CIS assemblies are clearly the strengths of the paper, both in terms of methods and results. Further, the paper provides genetic evidence that the membrane protein CisA is required for the contraction of the CISSc assemblies that are seen in partially lysed or ghost cells of the wild type. The conclusion that CisA is a transmembrane protein and the inferred membrane topology are well supported by experimental data. The cryo-EM data suggest that CisA is not a stable part of the extended form of the CISSc assemblies. These findings raise the question of what CisA does.

We thank Reviewer #2 for the overall positive evaluation of our manuscript and the constructive criticism. 

Weaknesses:

The investigations of the role of CisA in function, membrane interaction, and triggering of contraction of CIS assemblies, are important parts of the paper and are highlighted in the title. However, the experimental data provided to answer these questions appear partially incomplete and not as conclusive as one would expect.

We acknowledge that some aspects of our work have not been fully answered. We believe that providing additional experimental data is currently beyond the scope of this study. To improve this study, we will modify the text and clarify experimental procedures and figures where possible in the revised version of our manuscript.

The stress-induced loss of viability is only monitored with one method: an in vivo assay where cytoplasmic sfGFP signal is compared to FM5-95 membrane stain. Addition of a sublethal level of nisin lead to loss of sfGFP signal in individual hyphae in the WT, but not in the cisA mutant (similarly to what was previously reported for a CIS-negative mutant). Technically, this experiment and the example images that are shown give rise to some concern. Only individual hyphal fragments are shown that do not look like healthy and growing S. coelicolor hyphae. Under the stated growth conditions, S. coelicolor strains would normally have grown as dense hyphal pellets. It is therefore surprising that only these unbranched hyphal fragments are shown in Fig. 4ab.

We thank Reviewer #2 for their thoughtful criticism regarding our stress-induced viability assay and the data presented in Figure 4. We acknowledge the importance of ensuring that the presented images should reflect the physiological state of S. coelicolor under the stated growth conditions and recognize that hyphal fragments shown in Figure 4 do not fully capture the typical morphology of S. coelicolor. As pointed out by this reviewer, S. coelicolor grows in large hyphal clumps when cultured in liquid media, making the quantification of fluorescence intensities in hyphae expressing cytoplasmic GFP and stained with the membrane dye FM5-95 particularly challenging. To improve the image analysis and quantification of GFP and FM5-95-fluorescent intensities across the three S. coelicolor strains (wildtype, cisA deletion mutant and the complemented cisA mutant), we vortexed the cell samples briefly before imaging to break up hyphal clumps, increasing hyphal fragments. The hyphae shown in our images were selected as representative examples across three biological replicates. 

Further, S. coelicolor would likely be in a stationary phase when grown 48 h in the rich medium that is stated, giving rise to concern about the physiological state of the hyphae that were used for the viability assay. It would be valuable to know whether actively growing mycelium is affected in the same way by the nisin treatment, and also whether the cell death effect could be detected by other methods.

The reasoning behind growing S. coelicolor for 48 h before performing the fluorescence-based viability assay was that we (DOI: 10.1038/s41564-023-01341-x ) and others (e.g.: DOI: 10.1038/s41467-023-37087-7 ) previously showed that the levels of CIS particles peak at the transition from vegetative to reproductive/stationary growth, thus indicating that CIS activity is highest during this growth stage. The obtained results in this manuscript are in agreement with our previous study, in which we showed a similar effect on the viability of wildtype versus cis-deficient S. coelicolor strains (DOI: 10.1038/s41564-023-01341-x ) using nisin, the protonophore CCCP and UV light, and supported by biological replicate experiments and appropriate controls. Furthermore, our results are in agreement with the findings reported in a complementary study by Vladimirov et al. (DOI: 10.1038/s41467-023-37087-7 ) that used a different approach (SYTO9/PI staining of hyphal pellets) to demonstrate that CIS-deficient mutants exhibit decreased hyphal death. We agree that it would be interesting to test if actively growing hyphae respond differently to nisin treatment, and such experiments will be considered in future work. 

Taken together, we believe that the results obtained from our fluorescence-based viability assay are consistent with data reported by others and provide strong experimental evidence that functional CIS mediate hyphal cell death. 

The model presented in Fig. 5 suggests that stress leads to a CisA-dependent attachment of CIS assemblies to the cytoplasmic membrane, and then triggering of contraction, leading to cell death. This model makes testable predictions that have not been challenged experimentally. Given that sublethal doses of nisin seem to trigger cell death, there appear to be possibilities to monitor whether activation of the system (via CisA?) indeed leads to at least temporally increased interaction of CIS with the membrane.

We thank this reviewer for their suggestions on how to test our model further. In the meantime, we have performed co-immunoprecipitation experiments using S. coelicolor cells that produced CisA-FLAG as bait and were treated with a sub-lethal nisin concentration for 0/15/45 min.  Mass spectrometry analysis of co-eluted peptides did not show the presence of CIS-associated peptides. While we cannot exclude the possibility that our experimental assay requires further optimization to successfully demonstrate a CisA-CIS interaction (e.g. optimization of the use of detergents to improve the solubilization of CisA from Streptomyces membrane, which is currently not an established method), an alternative and equally valid hypothesis is that the interaction between CIS particles and CisA is transient and therefore difficult to capture. We would like to mention that we did detect CisA peptides in crude purifications of CIS particles from nisin-stressed cells (Supplementary Table 2, manuscript: line 265/266), supporting our model that CisA associates with CIS particles in vivo.

Further, would not the model predict that stress leads to an increased number of contracted CIS assemblies in the cytoplasm? No clear difference in length of the isolated assemblies if Fig. S7 is seen between untreated and nisin-exposed cells, and also no difference between assemblies from WT and cisA mutant hyphae.

The reviewer is correct that there is no clear difference in length in the isolated CIS particles shown in Figure S7. This is in line with our results, which show that CisA is not required for the correct assembly of CIS particles and their ability to contract in the presence and absence of nisin treatment. The purpose of Figure S7 was to support this statement. We would like to note that the particles shown in Figure S7 were purified from cell lysates using a crude sheath preparation protocol, during which CIS particles generally contract irrespective of the presence or absence of CisA. Thus, we cannot comment on whether there is an increased number of contracted CIS assemblies in the cytoplasm of nisin-exposed cells. To answer this point, we would need to acquire additional cryo-electron tomograms (cyroET) of the different strains treated with nisin. We appreciate this reviewer's suggestions. However, cryoET is an extremely time and labour-intensive task, and given that we currently don’t know the exact dynamics of the CIS-CisA interaction following exogenous stress, we believe this experiment is beyond the scope of this work.

The interaction of CisA with the CIS assembly is critical for the model but is only supported by Alphafold modelling, predicting interaction between cytoplasmic parts of CisA and Cis11 protein in the baseplate wedge. An experimental demonstration of this interaction would have strengthened the conclusions.

We agree that direct experimental evidence of this interaction would have further strengthened the conclusions of our study, and we have extensively tried to provide additional experimental evidence. Unfortunately, due to the toxicity of CisA expression in E. coli and the transient nature of the interaction under our experimental conditions, we were unable to pursue direct biochemical or biophysical validation methods, such as co-purification or bacterial two-hybrid assays. While these challenges limited our ability to experimentally confirm the interaction, the AlphaFold predictions provided a valuable hypothesis and mechanistic insight into the role of CisA.

The cisA mutant showed a similarly accelerated sporulation as was previously reported for CIS-negative strains, which supports the conclusion that CisA is required for function of CISSc. But the results do not add any new insights into how CIS/CisA affects the progression of the developmental life cycle and whether this effect has anything to do with the regulated cell death that is caused by CIS. The same applies to the effect on secondary metabolite production, with no further mechanistic insights added, except reporting similar effects of CIS and CisA inactivations.

We thank this reviewer for their thoughtful feedback and for highlighting the connections between CisA, CIS function, and their effects on the developmental life cycle and secondary metabolite production in S. coelicolor. The main focus of this study was to provide further insight into how CIS contraction and firing are mediated in Streptomyces, and we used the analysis of accelerated sporulation and secondary metabolite production to assess the functionality of CIS in the presence or absence of CisA.

We agree that we still don’t fully understand the nature of the signals that trigger CIS contraction, but we do know that the production of CIS assemblies seems to be an integral part of the Streptomyces multicellular life cycle as demonstrated in two independent previous studies (DOI: 10.1038/s41564-023-01341-x and DOI: 10.1038/s41467-023-37087-7 ). We propose that the assembly and firing of Streptomyces CIS particles could present a molecular mechanism to sacrifice only a part of the mycelium to either prevent the spread of local cellular damage or to provide additional nutrients for the rest of the mycelium and delay the terminal differentiation into spores and affect the production of secondary metabolites.

We recognize the importance of understanding the regulation and mechanistic details underpinning the proposed CIS-mediated regulated cell death model. This will be further explored in future studies.

Concluding remarks:

The work will be of interest to anyone interested in contractile injection systems, T6SS, or similar machineries, as well for people working on the biology of streptomycetes. There is also a potential impact of the work in the understanding of how such molecular machineries could have been co-opted during evolution to become a mechanism for regulated cell death. However, this latter aspect remains still poorly understood. Even though this paper adds excellent new structural insights and identifies a putative membrane anchor, it remains elusive how the Streptomyces CIS may lead to cell death. It is also unclear what the advantage would be to trigger death of hyphal compartments in response to stress, as well as how such cell death may impact (or accelerate) the developmental progression. Finally, it is inescapable to wonder whether the Streptomyces CIS could have any role in protection against phage infection.

We thank Reviewer #2 for their supportive assessment of our work. In the revised manuscript, we will briefly discuss the impact of functional CIS assemblies on Streptomyces development. We previously tested if Streptomyces could defend against phages but have not found any experimental evidence to support this idea. The analysis of phage defense mechanisms is an underdeveloped area in Streptomyces research, partly due to the currently limited availability of a diverse phage panel.

Reviewer #3 (Public review):

Summary:

In this work, Casu et al. have reported the characterization of a previously uncharacterized membrane protein CisA encoded in a non-canonical contractile injection system of Streptomyces coelicolor, CISSc, which is a cytosolic CISs significantly distinct from both intracellular membrane-anchored T6SSs and extracellular CISs. The authors have presented the first high-resolution structure of extended CISSc structure. It revealed important structural insights in this conformational state. To further explore how CISSc interacted with cytoplasmic membrane, they further set out to investigate CisA that was previously hypothesized to be the membrane adaptor. However, the structure revealed that it was not associated with CISSc. Using fluorescence microscope and cell fractionation assay, the authors verified that CisA is indeed a membrane-associated protein. They further determined experimentally that CisA had a cytosolic N-terminal domain and a periplasmic C-terminus. The functional analysis of cisA mutant revealed that it is not required for CISSc assembly but is essential for the contraction, as a result, the deletion significantly affects CISSc-mediated cell death upon stress, timely differentiation, as well as secondary metabolite production. Although the work did not resolve the mechanistic detail how CisA interacts with CISSc structure, it provides solid data and a strong foundation for future investigation toward understanding the mechanism of CISSc contraction, and potentially, the relation between the membrane association of CISSc, the sheath contraction and the cell death.

Strengths:

The paper is well-structured, and the conclusion of the study is supported by solid data and careful data interpretation was presented. The authors provided strong evidence on (1) the high-resolution structure of extended CISSc determined by cryo-EM, and the subsequent comparison with known eCIS structures, which sheds light on both its similarity and different features from other subtypes of eCISs in detail; (2) the topological features of CisA using fluorescence microscopic analysis, cell fractionation and PhoA-LacZα reporter assays, (3) functions of CisA in CISSc-mediated cell death and secondary metabolite production, likely via the regulation of sheath contraction.

Weaknesses:

The data presented are not sufficient to provide mechanistic details of CisA-mediated CISSc contraction, as authors are not able to experimentally demonstrate the direct interaction between CisA with baseplate complex of CISSc (hypothesized to be via Cis11 by structural modeling), since they could not express cisA in E. coli due to its potential toxicity. Therefore, there is a lack of biochemical analysis of direct interaction between CisA and baseplate wedge. In addition, there is no direct evidence showing that CisA is responsible for tethering CISSc to the membrane upon stress, and the spatial and temporal relation between membrane association and contraction remains unclear. Further investigation will be needed to address these questions in future.

We thank Reviewer #3 for the supportive evaluation and constructive criticism of our study in the public and non-public review. We appreciate your recognition of the technical limitations of experimentally demonstrating a direct interaction between CisA and CIS baseplate complex, and we agree that further investigations in the future will hopefully provide a full mechanistic understanding of the spatiotemporal interaction of CisA and CIS particular and the subsequent CIS firing.

To further improve the manuscript, we will revise the text and clarify figures and figure legends as suggested in the non-public review.

Discussion:

Overall, the work provides a valuable contribution to our understanding on the structure of a much less understood subtype of CISs, which is unique compared to both membrane-anchored T6SSs and host-membrane targeting eCISs. Importantly, the work serves as a good foundation to further investigate how the sheath contraction works here. The work contributes to expanding our understanding of the diverse CIS superfamilies.

Thank you.

eLife Assessment

This is a valuable study and a promising development for the field of open-source microscopy for educational purposes. The strengths include the low cost of constructing the microscope, impressive performance and detailed resources including a dedicated website and YouTube channel. The claims are generally supported by solid evidence, however, the manuscript would be strengthened by inclusion of further details on standard performance metrics (e.g. signal to noise ratio etc.) compared to existing systems and further details and clarification on the microscope, construction and operation.

Reviewer #1 (Public review):

Summary:

Carter et al. present the eduWOSM imaging platform, a promising development in open-source microscopy for educational purposes. The paper outlines the construction and setup of this versatile microscope, demonstrating its capabilities through three key examples: single fluorophore tracking of tubulin heterodimers in gliding microtubules, 4D deconvolution imaging and tracking of chromosome movements in dividing human cells, and automated single-particle tracking in vitro and in live cells, with motion classified into sub-diffusive, diffusive, and super-diffusive behaviors.

The paper is well-written and could be strengthened by providing more empirical data on its performance, addressing potential limitations, and offering detailed insights into its educational impact. The project holds great potential and more discussion on long-term support and broader applications would provide a more comprehensive view of its relevance in different contexts.

Strengths:

(1) The eduWOSM addresses a crucial need in education, providing research-quality imaging at a lower cost (<$10k). The fact that it is open-source adds significant value, enabling broad accessibility even in under resourced areas.<br /> (2) There is availability of extensive resources, including a dedicated website, YouTube channel, and comprehensive tutorial guides to help users replicate the microscope.<br /> (3) The compact, portable, and stable design makes it easy to build multiple systems for use in diverse environments, including crowded labs and classrooms. This is further enhanced by the fact multiple kind of imaging experiments can be run on the system, from live imaging to super-resolution imaging.<br /> (4) The paper highlights the user-friendly nature of the platform, with the imaging examples in the paper being acquired by undergrad students.

Weaknesses:

(1) The paper mentions the microscope is suitable not just for education but even for research purposes. This claim needs validation through quantitative comparison to existing research-grade microscopes in terms of resolution, signal-to-noise ratio, and other key metrics. Adding more rigorous comparisons would solidify its credibility for research use, which would immensely increase the potential of the microscope.<br /> (2) The open-source microscope field is crowded with various options catering to hobby, educational, and research purposes (e.g., openFLexure, Flamingo, Octopi, etc.). The paper would benefit from discussing whether any aspects set the eduWOSM platform apart or fulfill specific roles that other microscopes do not.<br /> (3) While the eduWOSM platform is designed to be user-friendly, the paper would benefit from discussing whether the microscope can be successfully built and operated by users without direct help from the authors. It's important to know if someone with basic technical knowledge, relying solely on the provided resources (website, YouTube tutorials, and documentation), can independently assemble, calibrate, and operate the eduWOSM.<br /> (4) Ensuring long-term support and maintenance of the platform is crucial. The paper would benefit from addressing how the eduWOSM developers plan to support updates, improvements, or troubleshooting.

Reviewer #2 (Public review):

The main strength of this work is the impressive performance of a microscope assembled for a fraction of the cost of a commercial, turnkey system. The authors have created a very clever design that removes everything that is not essential. They show compelling time-lapse data looking at single molecules, tracking particles visible in brightfield mode, and looking at cell division with multiple labels in a live cell preparation.

The weaknesses of the paper include:<br /> (1) the lack of more comprehensive explanations of the microscope and what it takes to build and operate it.<br /> For example, the dimensions of the microscope, how samples are mounted, which lenses are compatible, and whether eduWOSMs have been built by groups other than the authors would be useful information.<br /> (2) the absence of more detailed descriptions of some of the experiments, such as frame rates and Z-stack information.<br /> (3) the lack of standardized measures of performance.<br /> For example, images of subresolution tetraspeck beads and measurements of PSF would provide estimates on resolution in XY, resolution in Z, axial chromatic aberrations and lateral chromatic aberrations. Repeating these measurements on different eduWOSMs will provide an idea of how reliably the performance can be achieved.<br /> If these issues were addressed, it would make it more likely that other groups could build and operate this system successfully.

Overall, the authors have designed and built an impressive system at low cost. Providing a bit more information in the manuscript would make it much more likely that other laboratories could replicate this design in their own environments.

Author response:

Both reviewers made thoughtful and constructive comments, suggesting improvements that we are keen to provide. The comments fall under 3 headings (1) Further validation of the design, regarding both optical performance and utility, for both education and research (2) Further description and facilitation of the build process and (3) Further description of future plans, in particular plans for dissemination and long-term support. We think these requirements will be best served by adding new content to our Github site and our YouTube channel. We will create this new content and provide a revised manuscript in which these materials are linked from our existing narrative.

eLife Assessment

The work presented in this paper provides an important insight into how early life experience shapes adult behavior in fruit bats. The authors raised juvenile bats either in an impoverished or enriched environment and studied their foraging behaviors. The evidence is convincing that bats raised in enriched environments are more active, bold, and exploratory, although further exploration of the data and clarification of the analysis would strengthened the evidence. The work will be of interest to ethologists and developmental psychologists.

Reviewer #1 (Public review):

Summary:

The authors show that early life experience of juvenile bats shape their outdoor foraging behaviors. They achieve this by raising juvenile bats either in an impoverished or enriched environment. They subsequently test the behavior of bats indoors and outdoors. The authors show that behavioral measures outdoors were more reliable in delineating the effect of early life experiences as the bats raised in enriched environments were more bold, active and exhibit higher exploratory tendencies.

Strengths:

The major strength of the study is providing a quantitative study of animal "personality" and how it is likely shaped by innate and environmental conditions. The other major strength is the ability to do reliable long term recording of bats in the outdoors giving researchers the opportunity to study bats in their natural habitat. To this point, the study also shows that the behavioral variables measured indoors do not correlate to that measured outdoors, thus providing a key insight into the importance of testing animal behaviors in their natural habitat.

Weaknesses:

It is not clear from the analysis presented in the paper how persistent those environmentally induced changes, do they remain with the bats till the end of their lives.

Reviewer #2 (Public review):

Summary:

The authors present a paper that attempts to tackle an important question, with potential impact far beyond the field of animal behavior research: what are the relative contributions of innate personality traits versus early life experience on individual behavior in the wild? The study, performed on Egyptian fruit bats that are caught in the wild and later housed in an outdoor colony, is solidly executed, and benefits greatly from a unique setup in which controlled laboratory experiments are combined with monitoring of individuals as they undertake undirected, free exploration of their natural environment.

The primary finding of the paper is that there is a strong effect of early life experience on behavior in the wild, where individual bats that were exposed to an enriched environment as juveniles later travelled farther and over greater distances when permitted to explore and forage ad libitum, as compared with individual bats who were subjected to a more impoverished environment. Meanwhile, no prominent effect of innate "personality", as assessed by indices of indoor foraging behavior early on, before the bats were exposed to the controlled environmental treatment, was observed on three metrics of outdoor foraging behavior. The authors conclude that the early environment plays a larger role than innate personality on the behavior of adult bats.

Strengths:

(1) Elegant design of experiments and impressive combination of methods<br /> Bats used in the experiment were taken from wild colonies in different geographical areas, but housed during the juvenile stage in a controlled indoor environment. Bats are tested on the same behavioral paradigm at multiple points in their development. Finally, the bats are monitored with GPS as they freely explore the area beyond the outdoor colony.

(2) Development of a behavioral test that yields consistent results across time<br /> The multiple-foraging box paradigm, in which behavioral traits such as overall activity, levels of risk-taking, and exploratoriness can be evaluated as creative, and suggestive of behavioral paradigms other animal behavior researchers might be able to use. It is especially useful, given that it can be used to evaluate the activity of animals seemingly at most stages of life, and not just in adulthood.

Weaknesses:

(1) Robustness and validity of personality measures<br /> Coming up with robust measures of "personality" in non-human animals is tricky. While this paper represents an important attempt at a solution, some of the results obtained from the indoor foraging paradigm raise questions as to the reliability of this task for assessing "personality".

(2) Insufficient exploitation of data<br /> Between the behavioral measures and the very multidimensional GPS data, the authors are in possession of a rich data set. However, I don't feel that this data has been adequately exploited for underlying patterns and relationships. For example, many more metrics could be extracted from the GPS data, which may then reveal correlations with early measures of personality or further underscore the role of the early environment. In addition, the possibility that these personality measures might in combination affect outdoor foraging is not explored.

(3) Interpretation of statistical results and definition of statistical models<br /> Some statistical interpretations may not be entirely accurate, particularly in the case of multiple regression with generalized linear models. In addition, some effects which may be present in the data are dismissed as not significant on the basis of null hypothesis testing.

Below I have organized the main points of critique by theme, and ordered subordinate points by order of importance:

(1) Assessing personality metrics and the indoor paradigm: While I applaud this effort and think the metrics used are justified, I see a few issues in the results as they are currently presented:<br /> (a) [Major] I am somewhat concerned that here, the foraging box paradigm is being used for two somewhat conflicting purposes: (1) assessing innate personality and (2) measuring changes in personality as a result of experience. If the indoor foraging task is indeed meant to measure and reflect both at the same time, then perhaps this can be made more explicit throughout the manuscript. In this circumstance, I think the authors could place more emphasis on the fact that the task, at later trials/measurements, begins to take on the character of a "composite" measure of personality and experience.

(b) [Major] Although you only refer to results obtained in trials 1 and 2 when trying to estimate "innate personality" effects, I am a little worried that the paradigm used to measure personality, i.e. the stable components of behavior, is itself affected by other factors such as age (in the case of activity, Fig. 1C3, S1C1-2), the environment (see data re trial 3), and experience outdoors (see data re trials 4/5).

Ideally, a study that aims to disentangle the role of predisposition from early-life experience would have a metric for predisposition that is relatively unchanging for individuals, which can stand as a baseline against a separate metric that reflects behavioral differences accumulated as a result of experience.

I would find it more convincing that the foraging box paradigm can be used to measure personality if it could be shown that young bats' behavior was consistent across retests in the box paradigm prior to any environmental exposure across many baseline trials (i.e. more than 2), and that these "initial settings" were constant for individuals. I think it would be important to show that personality is consistent across baseline trials 1 and 2. This could be done, for example, by reproducing the plots in Fig. 1C1-3 while plotting trial 1 against trial 2. (I would note here that if a significant, positive correlation were to be found (as I would expect) between the measures across trial 1 and 2, it is likely that we would see the "habituation effect" the authors refer to expressed as a steep positive slope on the correlation line (indicating that bold individuals on trial 1 are much bolder on trial 2).)

(c) Related to the previous point, it was not clear to me why the data from trial 2 (the second baseline trial) was not presented in the main body of the paper, and only data from trial 1 was used as a baseline.

In the supplementary figure and table, you show that the bats tended to exhibit more boldness and exploratory behavior, but fewer actions, in trial 2 as compared with trial 1. You explain that this may be due to habituation to the experimental setup, however, the precise motivation for excluding data from trial 2 from the primary analyses is not stated. I would strongly encourage the authors to include a comparison of the data between the baseline trials in their primary analysis (see above), combine the information from these trials to form a composite baseline against which further analyses are performed, or further justify the exclusion of data as a baseline.

(2) Comparison of indoor behavioral measures and outdoor behavioral measures<br /> Regarding the final point in the results, correlation between indoor personality on Trial 4 and outdoor foraging behavior: It is not entirely clear to me what is being tested (neither the details of the tests nor the data or a figure are plotted). Given some of the strong trends in the data - namely, (1) how strongly early environment seems to affect outdoor behavior, (2) how strongly outdoor experience affects boldness, measured on indoor behavior (Fig. 1D) - I am not convinced that there is no relationship, as is stated here, between indoor and outdoor behavior. If this conclusion is made purely on the basis of a p-value, I would suggest revisiting this analysis.

(3) Use of statistics/points regarding the generalized linear models<br /> While I think the implementation of the GLMM models is correct, I am not certain that the interpretation of the GLMM results is entirely correct for cases where multivariate regression has been performed (Tables 4s and S1, and possibly Table 3). (You do not present the exact equation they used for each model (this would be a helpful addition to the methods), therefore it is somewhat difficult to evaluate if the following critique properly applies, however...)

The "estimate" for a fixed effect in a regression table gives the difference in the outcome variable for a 1 unit increase in the predictor variable (in the case of numeric predictors) or for each successive "level" or treatment (in the case of categorical variables), compared to the baseline, the intercept, which reflects the value of the outcome variable given by the combination of the first value/level of all predictors. Therefore, for example, in Table 4a - Time spend outside: the estimate for Bat sex: male indicates (I believe) the difference in time spent outside for an enriched male vs. an enriched female, not, as the authors seem to aim to explain, the effect of sex overall. Note that the interpretation of the first entry, Environmental condition: impoverished, is correct. I refer the authors to the section "Multiple treatments and interactions" on p. 11 of this guide to evaluating contrasts in G/LMMS: https://bbolker.github.io/mixedmodels-misc/notes/contrasts.pdf

eLife Assessment

This valuable study presents findings linking prophage carriage to lifestyle regulation in the marine bacterium Shewanella fidelis, with potential implications for niche occupation within a host (Ciona robusta) and mediation of host immune responses. The study leverages a unique animal model system that offers distinct advantages in identifying select phenotypes to present generally solid evidence that supports findings relating to the impact of a prophage on host-microbe interaction. Understanding the role of integrated lysogenic phages in bacterial fitness, both within a host and in the environment, is a significant concept in bacterial eco-physiology, potentially contributing to the success of certain strains.

Reviewer #1 (Public review):

Summary:

The manuscript aims to elucidate the impact of a prophage within the genome of Shewanella fidelis on its interaction with the marine tunicate Ciona robusta. The authors made a deletion mutant of S. fidelis that lacks one of its two prophages. This mutant exhibited an enhanced biofilm phenotype, as assessed through crystal violet staining, and showed reduced motility. The authors examined the effect of prophage deletion on several genes that could modulate cyclic-diGMP levels. While no significant changes were observed under in vitro conditions, the gene for one protein potentially involved in cyclic-diGMP hydrolysis was overexpressed during microbe-host interactions. The mutant was retained more effectively within a one-hour timeframe, whereas the wild-type (WT) strain became more abundant after 24 hours. Fluorescence microscopy was used to visualize the localization patterns of the two strains, which appeared to differ. Additionally, a significant difference in the expression of one immune protein was noted after one hour, but this difference was not evident after 23 hours. An effect of VCBC-C addition on the expression of one prophage gene was also observed.

Strengths:

I appreciate how the authors integrate diverse expertise and methods to address questions regarding the impact of prophages on gut microbiome-host interactions. The chosen model system is appropriate, as it allows for high-throughput experimentation and the application of simple imaging techniques.

Weaknesses:

My primary concern is that the manuscript primarily describes observations without providing insight into the molecular mechanisms underlying the observed differences. It is particularly unclear how the presence of the prophage leads to the phenotypic changes related to bacterial physiology and host-microbe interactions. Which specific prophage genes are critical, or is the insertion at a specific site in the bacterial genome the key factor? While significant effects on bacterial physiology are reported under in vitro conditions, there is no clear attribution to particular enzymes or proteins. In contrast, when the system is expanded to include the tunicate, differences in the expression of a cyclic-diGMP hydrolase become apparent. Why do we not observe such differences under in vitro conditions, despite noting variations in biofilm formation and motility? Furthermore, given that the bacterial strain possesses two prophages, I am curious as to why the authors chose to target only one and not both.

Regarding the microbe-host interaction, it is not clear why the increased retention ability of the prophage deletion strain did not lead to greater cell retention after 24 hours, especially since no differences in the immune response were observed at that time point.

Concerning the methodological approach, I am puzzled as to why the authors opted for qPCR instead of transcriptomics or proteomics. The latter approaches could have provided a broader understanding of the prophage's impact on both the microbe and the host.

Reviewer #2 (Public review):

Summary:

In the manuscript, "Prophage regulation of Shewanella fidelis 3313 motility and biofilm formation: implications for gut colonization dynamics in Ciona robusta", the authors are experimentally investigating the idea that integrated viruses (prophages) within a bacterial colonizer of the host Ciona robusta affect both the colonizer and the host. They found a prophage within the Ciona robusta colonizing bacterium Shewanella fidelis 3313, which affected both the bacteria and host. This prophage does so by regulating the phosphodiesterase gene pdeB in the bacterium when the bacterium has colonized the host. The prophage also regulates the activity of the host immune gene VCBP-C during early bacterial colonization. Prophage effects on both these genes affect the precise localization of the colonizing bacterium, motility of the bacterium, and bacterial biofilm formation on the host. Interestingly, VCBP-C expression also suppressed a prophage structural protein, creating a tripartite feedback loop in this symbiosis. This is exciting research that adds to the emerging body of evidence that prophages can have beneficial effects not only on their host bacteria but also on how that bacteria interacts in its environment. This study establishes the evolutionary conservation of this concept with intriguing implications of prophage effects on tripartite interactions.

Strengths:

This research effectively shows that a prophage within a bacterium colonizing a model ascidian affects both the bacterium and the host in vivo. These data establish the prophage effects on bacterial activity and expand these effects to the natural interactions within the host animal. The effects of the prophage through deletion on a suite of host genes are a strength, as shown by striking microscopy.

Weaknesses:

Unfortunately, there are abundant negative data that cast some limitations on the interpretation of the data. That is, examining specific gene expression has its limitations, which could be avoided by global transcriptomics of the bacteria and the host during colonization by the prophage-containing and prophage-deleted bacteria (1 hour and 24 hours). In this way, the tripartite interactions leading to mechanism could be better established.

Impact:

The authors are correct to speculate that this research can have a significant impact on many animal microbiome studies, since bacterial lysogens are prevalent in most microbiomes. Screening for prophages, determining whether they are active, and "curing" the host bacteria of active prophages are effective tools for understanding the effects these mobile elements have on microbiomes. There are many potential effects of these elements in vivo, both positive and negative, this research is a good example of why this research should be explored.

Context:

The research area of prophage effects on host bacteria in vitro has been studied for decades, while these interactions in combination with animal hosts in vivo have been recent. The significance of this research shows that there could be divergent effects based on whether the study is conducted in vitro or in vivo. The in vivo results were striking. This is particularly so with the microscopy images. The benefit of using Ciona is that it has a translucent body which allows for following microbial localization. This is in contrast to mammalian studies where following microbial localization would either be difficult or near impossible.

Reviewer #3 (Public review):

In this manuscript, Natarajan and colleagues report on the role of a prophage, termed SfPat, in the regulation of motility and biofilm formation by the marine bacterium Shewanella fidelis. The authors investigate the in vivo relevance of prophage carriage by studying the gut occupation patterns of Shewanella fidelis wild-type and an isogenic SfPat- mutant derivative in a model organism, juveniles of the marine tunicate Ciona robusta. The role of bacterial prophages in regulating bacterial lifestyle adaptation and niche occupation is a relatively underexplored field, and efforts in this direction are appreciated.

While the research question is interesting, the work presented lacks clarity in its support for several major claims, and, at times, the authors do not adequately explain their data.

Major concerns:

(1) Prophage deletion renders the SfPat- mutant derivative substantially less motile and with a higher biofilm formation capacity than the WT (Fig. 2a-b). The authors claim the mutant is otherwise isogenic to the WT strain upon sequence comparison of draft genome sequences (I'll take the opportunity to comment here that GenBank accessions are preferable to BioSample accessions in Table 1). Even in the absence of secondary mutations, complementation is needed to validate functional associations (i.e., phenotype restoration). A strategy for this could be phage reintegration into the mutant strain (PMID: 19005496).

(2) The authors claim that the downshift in motility (concomitant with an upshift in biofilm formation) is likely mediated by the activity of c-di-GMP turnover proteins. Specifically, the authors point to the c-di-GMP-specific phosphodiesterase PdeB as a key mediator, after finding lower transcript levels for its coding gene in vivo (lines 148-151, Fig. 2c), and suggesting higher activity of this protein in live animals (!)(line 229). I have several concerns here:<br /> (2.1) Findings shown in Fig. 2a-b are in vitro, yet no altered transcript levels for pdeB were recorded (Fig. 2c). Why do the authors base their inferences only on in vivo data?<br /> (2.2) Somewhat altered transcript levels alone are insufficient for making associations, let alone solid statements. Often, the activity of c-di-GMP turnover proteins is local and/or depends on the activation of specific sensory modules - in the case of PdeB, a PAS domain and a periplasmic sensor domain (PMID: 35501424). This has not been explored in the manuscript, i.e., specific activation vs. global alterations of cellular c-di-GMP pools (or involvement of other proteins, please see below). Additional experiments are needed to confirm the involvement of PdeB. Gaining such mechanistic insights would greatly enhance the impact of this study.<br /> (2.3) What is the rationale behind selecting only four genes to probe the influence of the prophage on Ciona gut colonization by determining their transcript levels in vitro and in vivo? If the authors attribute the distinct behavior of the mutant to altered c-di-GMP homeostasis, as may be plausible, why did the authors choose those four genes specifically and not, for example, the many other c-di-GMP turnover protein-coding genes or c-di-GMP effectors present in the S. fidelis genome? This methodological approach seems inadequate to me, and the conclusions on the potential implication of PdeB are premature.

(3) The behavior of the WT strain and the prophage deletion mutant is insufficiently characterized. For instance, how do the authors know that the higher retention capacity reported for the WT strain with respect to the mutant (Fig. 3b) is not merely a consequence of, e.g., a higher growth rate? It would be worth investigating this further, ideally under conditions reflecting the host environment.

(4) Related to the above, sometimes the authors refer to "retention" (e.g., line 162) and at other instances to "colonization" (e.g., line 161), or even adhesion (line 225). These are distinct processes. The authors have only tracked the presence of bacteria by fluorescence labeling; adhesion or colonization has not been assessed or demonstrated in vivo. Please revise.

(5) The higher CFU numbers for the WT after 24 h (line 161) might also indicate a role of motility for successful niche occupation or dissemination in vivo. The authors could test this hypothesis by examining the behavior of, e.g., flagellar mutants in their in vivo model.

(6) The endpoint of experiments with a mixed WT-mutant inoculum (assumedly 1:1? Please specify) was set to 1 h, I assume because of the differences observed in CFU counts after 24 h. In vivo findings shown in Fig. 3c-e are, prima facie, somewhat contradictory. The authors report preferential occupation of the esophagus by the WT (line 223), which seems proficient from evidence shown in Fig. S3. Yet, there is marginal presence of the WT in the esophagus in experiments with a mixed inoculum (Fig. 3d) or none at all (Fig. 3e). Likewise, the authors claim preferential "adhesion to stomach folds" by the mutant strain (line 225), but this is not evident from Fig. 3e. In fact, the occupation patterns by the WT and mutant strain in the stomach in panel 3e appear to differ from what is shown in panel 3d. The same holds true for the claimed "preferential localization of the WT in the pyloric cecum," with Fig. 3d showing a yellow signal that indicates the coexistence of WT and mutant.

(7) In general, and especially for in vivo data, there is considerable variability that precludes drawing conclusions beyond mere trends. One could attribute such variability in vivo to the employed model organism (which is not germ-free), differences between individuals, and other factors. This should be discussed more openly in the main text and presented as a limitation of the study. Even with such intrinsic factors affecting in vivo measurements, certain in vitro experiments, which are expected, in principle, to yield more reproducible results, also show high variability (e.g., Fig. 5). What do the authors attribute this variability to?

(8) Line 198-199: Why not look for potential prophage excision directly rather than relying on indirect, presumptive evidence based on qPCR?

eLife Assessment

This fundamental study examines infection of the liver and hepatocytes during Mycobacterium tuberculosis infection using different systems including aerosol infection of mice and guinea pigs to demonstrate appreciable infection of the liver as well as the lung. The authors present convincing evidence that hepatocyte infection leads to metabolic dysfunction that promotes M. tuberculosis growth, in part potentially mediated by a nuclear receptor called PPARg. Overall, this is an interesting paper on an area of tuberculosis research which has been understudied, representing a significant advancement in the field.

Reviewer #1 (Public review):

Summary:

The authors showed the presence of Mtb in human liver biopsy samples of TB patients and reported that chronic infection of Mtb causes immune-metabolic dysregulation. Authors showed that Mtb replicates in hepatocytes in a lipid rich environment created by up regulating transcription factor PPARγ. Authors also reported that Mtb protects itself from anti-TB drugs by inducing drug metabolising enzymes.

Strengths:

It has been shown that Mtb induces storage of triacylglycerol in macrophages by induction of WNT6/ACC2 which helps in its replication and intracellular survival, however, creation of favorable replicative niche in hepatocytes by Mtb is not reported. It is known that Mtb infects macrophages and induces formation of lipid-laden foamy macrophages which eventually causes tissue destruction in TB patients. In a recent article it has been reported that "A terpene nucleoside from M. tuberculosis induces lysosomal lipid storage in foamy macrophages" that shows how Mtb manipulates host defense mechanisms for its survival. In this manuscript, authors reported the enhancement of lipid droplets in Mtb infected hepatocytes and convincingly showed that fatty acid synthesis and triacylglycerol formation is important for growth of Mtb in hepatocytes. The authors also showed the molecular mechanism for accumulation of lipid and showed that the transcription factor associated with lipid biogenesis, PPARγ and adipogenic genes were upregulated in Mtb infected cells.

The comparison of gene expression data between macrophages and hepatocytes by authors is important which indicates that Mtb modulates different pathways in different cell type as in macrophages it is related to immune response whereas, in hepatocytes it is related to metabolic pathways.

Authors also reported that Mtb residing in hepatocytes showed drug tolerance phenotype due to up regulation of enzymes involved in drug metabolism and showed that cytochrome P450 monooxygenase that metabolize rifampicin and NAT2 gene responsible for N-acetylation of isoniazid were up regulated in Mtb infected cells.

Weaknesses:

There are reports of hepatic tuberculosis in pulmonary TB patients especially in immune-compromised patients, therefore finding granuloma in human liver biopsy samples is not surprising.<br /> Mtb infected hepatic cells showed induced DME and NAT and this could lead to enhanced metabolism of drug by hepatic cells as a result Mtb in side HepG2 cells get exposed to reduced drug concentration and show higher tolerance to drug. The authors mentioned that " hepatocyte resident Mtb may display higher tolerance to rifampicin". In my opinion higher tolerance to drugs is possible only when DME of Mtb inside is up regulated or the target is modified. Although, in the end authors mentioned that drug tolerance phenotype can be better attributed to host intrinsic factors rather than Mtb efflux pumps. It may be better if the Drug tolerant phenotype section can be rewritten to clarify the facts.

Reviewer #2 (Public review):

The manuscript by Sarkar et al has demonstrated the infection of liver cells/hepatocytes with Mtb and the significance of liver cells in the replication of Mtb by reprogramming lipid metabolism during tuberculosis. Besides, the present study shows that similar to Mtb infection of macrophages (reviewed in Chen et al., 2024; Toobian et al., 2021), Mtb infects liver cells but with a greater multiplication owing to consumption of enhanced lipid resources mediated by PPARg that could be cleared by its inhibitors. The strength of the study lies in the clinical evaluation of the presence of Mtb in human autopsied liver samples from individuals with miliary tuberculosis and the presence of a clear granuloma-like structure. The interesting observation is of granuloma-like structure in liver which prompts further investigations in the field.

The modulation of lipid synthesis during Mtb infection, such as PPARg upregulation, appears generic to different cell types including both liver cells and macrophage cells. It is also known that infection affect PPARγ expression and activity in hepatocytes. It is also known that this can lead to lipid droplet accumulation in the liver and the development of fatty liver disease (as shown for HCV). This study is in a similar line for M.tb infection. As the liver is the main site for lipid regulation, the availability of lipid resources is greater and higher is the replication rate. In short, the observations from the study confirm the earlier studies with these additional cell types. It is known that higher the lipid content, the greater are Lipid Droplet-positive Mtb and higher is the drug resistance (Mekonnen et al., 2021). The DMEs of liver cells add further to the phenotype.

Reviewer #3 (Public review):

This manuscript by Sarkar et al. examines the infection of the liver and hepatocytes during M. tuberculosis infection. They demonstrate that aerosol infection of mice and guinea pigs leads to appreciable infection of the liver as well as the lung. Transcriptomic analysis of HepG2 cells showed differential regulation of metabolic pathways including fatty acid metabolic processing. Hepatocyte infection is assisted by fatty acid synthesis in the liver and inhibiting this caused reduced Mtb growth. The nuclear receptor PPARg was upregulated by Mtb infection and inhibition or agonism of its activity caused a reduction or increase in Mtb growth, respectively, supporting data published elsewhere about the role of PPARg in lung macrophage Mtb infection. Finally, the authors show that Mtb infection of hepatocytes can cause upregulation of enzymes that metabolize antibiotics, resulting in increased tolerance of these drugs by Mtb in the liver.

Overall, this is an interesting paper on an area of TB research where we lack understanding. However, some additions to the experiments and figures are needed to improve the rigor of the paper and further support the findings. Most importantly, although the authors show that Mtb can infect hepatocytes in vitro, they fail to describe how bacteria get from the lungs to the liver in an aerosolized infection. They also claim that "PPARg activation resulting in lipid droplets formation by Mtb might be a mechanism of prolonging survival within hepatocytes" but do not show a direct interaction between PPARg activation and lipid droplet formation and lipid metabolism, only that PPARg promotes Mtb growth. Thus, the correlations with PPARg appear to be there but causation, implied in the abstract and discussion, is not proven.

The human photomicrographs are important and overall well done (lung and liver from the same individuals is excellent). However, in lines 120-121, the authors comment on the absence of studies on the precise involvement of different cells in the liver. In this study there is no attempt to immunophenotype the nature of the cells harboring Mtb in these samples (esp. hepatocytes). Proving that hepatocytes specifically harbor the bacteria in these human samples would add significant rigor to the conclusions made.

Author response:

Reviewer #1 (Public review):

Summary:

The authors showed the presence of Mtb in human liver biopsy samples of TB patients and reported that chronic infection of Mtb causes immune-metabolic dysregulation. Authors showed that Mtb replicates in hepatocytes in a lipid rich environment created by up regulating transcription factor PPARγ. Authors also reported that Mtb protects itself from anti-TB drugs by inducing drug metabolising enzymes.

Strengths:

It has been shown that Mtb induces storage of triacylglycerol in macrophages by induction of WNT6/ACC2 which helps in its replication and intracellular survival, however, creation of favorable replicative niche in hepatocytes by Mtb is not reported. It is known that Mtb infects macrophages and induces formation of lipid-laden foamy macrophages which eventually causes tissue destruction in TB patients. In a recent article it has been reported that "A terpene nucleoside from M. tuberculosis induces lysosomal lipid storage in foamy macrophages" that shows how Mtb manipulates host defense mechanisms for its survival. In this manuscript, authors reported the enhancement of lipid droplets in Mtb infected hepatocytes and convincingly showed that fatty acid synthesis and triacylglycerol formation is important for growth of Mtb in hepatocytes. The authors also showed the molecular mechanism for accumulation of lipid and showed that the transcription factor associated with lipid biogenesis, PPARγ and adipogenic genes were upregulated in Mtb infected cells.

The comparison of gene expression data between macrophages and hepatocytes by authors is important which indicates that Mtb modulates different pathways in different cell type as in macrophages it is related to immune response whereas, in hepatocytes it is related to metabolic pathways.

Authors also reported that Mtb residing in hepatocytes showed drug tolerance phenotype due to up regulation of enzymes involved in drug metabolism and showed that cytochrome P450 monooxygenase that metabolize rifampicin and NAT2 gene responsible for N-acetylation of isoniazid were up regulated in Mtb infected cells.

We thank the reviewer for the positive feedback and for highlighting the strengths of our study.

Weaknesses:

There are reports of hepatic tuberculosis in pulmonary TB patients especially in immune-compromised patients, therefore finding granuloma in human liver biopsy samples is not surprising.

Mtb infected hepatic cells showed induced DME and NAT and this could lead to enhanced metabolism of drug by hepatic cells as a result Mtb in side HepG2 cells get exposed to reduced drug concentration and show higher tolerance to drug. The authors mentioned that " hepatocyte resident Mtb may display higher tolerance to rifampicin". In my opinion higher tolerance to drugs is possible only when DME of Mtb inside is up regulated or the target is modified. Although, in the end authors mentioned that drug tolerance phenotype can be better attributed to host intrinsic factors rather than Mtb efflux pumps. It may be better if the Drug tolerant phenotype section can be rewritten to clarify the facts.

We agree that several case studies regarding liver infection in pulmonary TB patients have been reported in the literature, however this report is the first comprehensive study that establishes hepatocytes to be a favourable niche for Mtb survival and growth.

Drug tolerance is a phenomenon that is exhibited by the bacteria and in the course of host-pathogen interactions, can be influenced by both intrinsic (bacterial) and extrinsic (host-mediated) factors. Multiple examples of tolerance being attributed to host driven factors can be found in literature (PMID 32546788, PMID: 28659799, PMID: 32846197). Our studies demonstrate that Mtb infected hepatocytes create a drug tolerant environment by modulating the expression of Drug modifying enzymes (DMEs) in the hepatocytes.

As suggested by the reviewer we will rewrite the drug tolerant phenotype section.

Reviewer #2 (Public review):

The manuscript by Sarkar et al has demonstrated the infection of liver cells/hepatocytes with Mtb and the significance of liver cells in the replication of Mtb by reprogramming lipid metabolism during tuberculosis. Besides, the present study shows that similar to Mtb infection of macrophages (reviewed in Chen et al., 2024; Toobian et al., 2021), Mtb infects liver cells but with a greater multiplication owing to consumption of enhanced lipid resources mediated by PPARg that could be cleared by its inhibitors. The strength of the study lies in the clinical evaluation of the presence of Mtb in human autopsied liver samples from individuals with miliary tuberculosis and the presence of a clear granuloma-like structure. The interesting observation is of granuloma-like structure in liver which prompts further investigations in the field.

The modulation of lipid synthesis during Mtb infection, such as PPARg upregulation, appears generic to different cell types including both liver cells and macrophage cells. It is also known that infection affect PPARγ expression and activity in hepatocytes. It is also known that this can lead to lipid droplet accumulation in the liver and the development of fatty liver disease (as shown for HCV). This study is in a similar line for M.tb infection. As the liver is the main site for lipid regulation, the availability of lipid resources is greater and higher is the replication rate. In short, the observations from the study confirm the earlier studies with these additional cell types. It is known that higher the lipid content, the greater are Lipid Droplet-positive Mtb and higher is the drug resistance (Mekonnen et al., 2021). The DMEs of liver cells add further to the phenotype.

We thank the reviewer for emphasizing on the strengths of our study and how it can lead to further investigations in the field.

Reviewer #3 (Public review):

This manuscript by Sarkar et al. examines the infection of the liver and hepatocytes during M. tuberculosis infection. They demonstrate that aerosol infection of mice and guinea pigs leads to appreciable infection of the liver as well as the lung. Transcriptomic analysis of HepG2 cells showed differential regulation of metabolic pathways including fatty acid metabolic processing. Hepatocyte infection is assisted by fatty acid synthesis in the liver and inhibiting this caused reduced Mtb growth. The nuclear receptor PPARg was upregulated by Mtb infection and inhibition or agonism of its activity caused a reduction or increase in Mtb growth, respectively, supporting data published elsewhere about the role of PPARg in lung macrophage Mtb infection. Finally, the authors show that Mtb infection of hepatocytes can cause upregulation of enzymes that metabolize antibiotics, resulting in increased tolerance of these drugs by Mtb in the liver.

Overall, this is an interesting paper on an area of TB research where we lack understanding. However, some additions to the experiments and figures are needed to improve the rigor of the paper and further support the findings. Most importantly, although the authors show that Mtb can infect hepatocytes in vitro, they fail to describe how bacteria get from the lungs to the liver in an aerosolized infection. They also claim that "PPARg activation resulting in lipid droplets formation by Mtb might be a mechanism of prolonging survival within hepatocytes" but do not show a direct interaction between PPARg activation and lipid droplet formation and lipid metabolism, only that PPARg promotes Mtb growth. Thus, the correlations with PPARg appear to be there but causation, implied in the abstract and discussion, is not proven.

The human photomicrographs are important and overall, well done (lung and liver from the same individuals is excellent). However, in lines 120-121, the authors comment on the absence of studies on the precise involvement of different cells in the liver. In this study there is no attempt to immunophenotype the nature of the cells harboring Mtb in these samples (esp. hepatocytes). Proving that hepatocytes specifically harbor the bacteria in these human samples would add significant rigor to the conclusions made.

We thank the reviewer for nicely summarizing our manuscript.

Our study establishes the involvement of liver and hepatocytes in pulmonary TB infection in mice. Understanding the mechanism of bacterial dissemination from the lung to the liver in aerosol infections demands a detailed separate study.

Figure 6E and 6F shows how PPARγ agonist and antagonist modulate (increase and decrease respectively) bacterial growth in hepatocytes (further supported by the CFU data in Supplementary Figure 9B). Again, the number of lipid droplets in hepatocytes increase and decrease with the application of PPARγ agonist and antagonist respectively as shown in Figure 6G and 6H. Collectively, these studies provide strong evidence that PPARγ activation leads to more lipid droplets that support better Mtb growth.

We thank the reviewer for finding our human photomicrographs convincing. In the manuscript, we provide evidence for the direct involvement of the hepatocytes (and liver) in Mtb infection. We perform detailed immunophenotyping of hepatocyte cells in the mice model with ASPGR1 (asialoglycoprotein receptor 1) and in the revised version of record, we will further stain the infected hepatocytes with anti-albumin antibody.

eLife Assessment

This important theoretical study examines the possibility of encoding genomic information in a collective of short overlapping strands (e.g., the Virtual Circular Genome (VCG) model). The study presents solid theoretical arguments, simulations and comparisons to experimental data to point at potential features and limitations of such distributed collective encoding of information. The work should be of relevance to colleagues interested in molecular information processing and to those interested in pre-Central Dogma or prebiotic models of self-replication.

Reviewer #1 (Public review):

Summary:

This is an interesting theoretical study examining the viability of Virtual Circular Genome (VCG) model, a recently proposed scenario of prebiotic replication in which a relatively long sequence is stored as a collection of its shorter subsequences (and their compliments). It was previously pointed out that VCG model is prone to so-called sequence scrambling which limits the overall length of such a genome. In the present paper, additional limitations are identified. Specifically, it is shown that VCG is well replicated when the oligomers are elongated by sufficiently short chains from "feedstock" pool. However, ligation of oligomers from VCG itself results in a high error rate. I believe the research is of high quality and well written. However, the presentation could be improved and the key messages could be clarified.

(1) It is not clear from the paper whether the observed error has the same nature as sequence scrambling<br /> (2) The authors introduce two important lengths LS1 and LS2 only in the conclusions and do not explain enough which each of them is important. It would make sense to discuss this early in the manuscript.<br /> (3) It is not entirely clear why specific length distribution for VCG oligomers has to be assumed rather than emerged from simulations.<br /> (4) Furthermore, the problem has another important length, L0 that is never introduced or discussed: a minimal hybridization length with a lifetime longer than the ligation time. From the parameters given, it appears that L0 is sufficiently long (~10 bases). In other words, it appears that the study is done is a somewhat suboptimal regime: most hybridization events do not lead to a ligation. Am I right in this assessment? If that is the case, the authors might want to explore another regime, L0<br /> Strengths:

High-quality theoretical modeling of an important problem is implemented.

Weaknesses:

The conclusions are somewhat convoluted and could be presented better.

Reviewer #2 (Public review):

Summary:

This important theoretical and computational study by Burger and Gerland attempts to set environmental, compositional, kinetic, and thermodynamic constraints on the proposed virtual circular genome (VCG) model for the early non-enzymatic replication of RNA. The authors create a solid kinetic model using published kinetic and thermodynamic parameters for non-enzymatic RNA ligation and (de)hybridization, which allows them to test a variety of hypotheses about the VCG. Prominently, the authors find that the length (longer is better) and concentration (intermediate is better) of the VCG oligos have an outsized impact on the fidelity and yield of VCG production with important implications for future VCG design. They also identify that activation of only RNA monomers, which can be achieved using environmental separation of the activation and replication, can relax the constraints on the concentration of long VCG component oligos by avoiding the error-prone oligo-oligo ligation. Finally, in a complex scenario with multiple VCG oligo lengths, the authors demonstrate a clear bias for the extension of shorter oligos compared to the longer ones. This effect has been observed experimentally (Ding et al., JACS 2023) but was unexplained rigorously until now. Overall, this manuscript will be of interest to scientists studying the origin of life and the behavior of complex nucleic acid systems.

Strengths:

- The kinetic model is carefully and realistically created, enabling the authors to probe the VCG thoroughly.<br /> - Fig. 6 outlines important constraints for scientists studying the origin of life. It supports the claim that the separation of activation and replication chemistry is required for efficient non-enzymatic replication. One could easily imagine a scenario where activation of molecules occurs, followed by their diffusion into another environment containing protocells that encapsulate a VCG. The selective diffusion of activated monomers across protocell membranes would then result in only activated monomers being available to the VCG, which is the constraint outlined in this work. The proposed exclusive replication by monomers also mirrors the modern biological systems, which nearly exclusively replicate by monomer extension.<br /> - Another strength of the work is that it explains why shorter oligos extend better compared to the long ones in complex VCG mixtures. This point is independent of the activation chemistry used (it simply depends on the kinetics and thermodynamics of RNA base-pairing) so it should be very generalizable.

Weaknesses:

- Most of the experimental work on the VCG has been performed with the bridged 2-aminoimidazolium dinucleotides, which are not featured in the kinetic model of this work. Oher studies by Szostak and colleagues have demonstrated that non-enzymatic RNA extension with bridged dinucleotides have superior kinetics (Walton et al. JACS 2016, Li et al. JACS 2017), fidelity (Duzdevich et al. NAR 2021), and regioselectivity (Giurgiu et al. JACS 2017) compared to activated monomers, establishing the bridged dinucleotides as important for non-enzymatic RNA replication. Therefore, the omission of these species in the kinetic model presented here can be perceived as problematic. The major claim that avoidance of oligo ligations is beneficial for VCGs may be irrelevant if bridged dinucleotides are used as the extending species, because oligo ligations (V + V in this work) are kinetically orders of magnitude slower than monomer extensions (F + V in this work) (Ding et al. NAR 2022). Formally adding the bridged dinucleotides to the kinetic model is likely outside of the scope of this work, but perhaps the authors could test if this should be done in the future by simply increasing the rate of monomer extension (F + V) to match the bridged dinucleotide rate without changing rate of V + V ligation?<br /> - The kinetic and thermodynamic parameters for oligo binding appear to be missing two potentially important components. First, base-paired RNA strands that contain gaps where an activated monomer or oligo can bind have been shown to display significantly different kinetics of ligation and binding/unbinding than complexes that do not contain such gaps (see Prywes et al. eLife 2016, Banerjee et al. Nature Nanotechnology 2023, and Todisco et al. JACS 2024). Would inclusion of such parameters alter the overall kinetic model? Second, it has been shown that long base-paired RNA can tolerate mismatches to an extent that can result in monomer ligation to such mismatched duplexes (see Todisco et al. NAR 2024). Would inclusion of the parameters published in Todisco et al. NAR 2024 alter the kinetic model significantly?

eLife Assessment

Using a TN-seq based approach, the authors identified the genetic determinants of drug tolerance in M. abscessus. Since M. abscessus is resistant to multiple antibiotics, the study is valuable in generating new knowledge linking antibiotic tolerance with ROS in this non-tuberculosis mycobacterial (NTM) species. However, the study is incomplete due to a need for more validation of the Tn-seq data, inconsistency with the clinical strains, and insufficient experiments confirming the role of ROS detoxification in drug tolerance.

Reviewer #1 (Public review):

Summary:

Persistence is a phenomenon by which genetically susceptible cells are able to survive exposure to high concentrations of antibiotics. This is especially a major problem when treating infections caused by slow growing mycobacteria such as M. tuberculosis and M. abscessus. Studies on the mechanisms adopted by the persisting bacteria to survive and evade antibiotic killing can potentially lead to faster and more effective treatment strategies.

To address this, in this study, the authors have used a transposon mutagenesis based sequencing approach to identify the genetic determinants of antibiotic persistence in M. abscessus. To enrich for persisters they employed conditions, that have been reported previously to increase persister frequency - nutrient starvation, to facilitate genetic screening for this phenotype. M.abs transposon library was grown in nutrient rich or nutrient depleted conditions and exposed to TIG/LZD for 6 days, following which Tn-seq was carried out to identify genes involved in spontaneous (nutrient rich) or starvation-induced conditions. About 60% of the persistence hits were required in both the conditions. Pathway analysis revealed enrichment for genes involved in detoxification of nitrosative, oxidative, DNA damage and proteostasis stress. The authors then decided to validate the findings by constructing deletions of 5 different targets (pafA, katG, recR, blaR, Mab_1456c) and tested the persistence phenotype of these strains. Rather surprisingly only 2 of the 5 hits (katG and pafA) exhibited a persistence defect when compared to wild type upon exposure to TIG/LZD and this was complemented using an integrative construct. The authors then investigated the specificity of delta-katG susceptibility against different antibiotic classes and demonstrated increased killing by rifabutin. The katG phenotype was shown to be mediated through the production of oxidative stress which was reverted when the bacterial cells were cultured under hypoxic conditions. Interestingly, when testing the role of katG in other clinical strains of Mab, the phenotype was observed only in one of the clinical strains demonstrating that there might be alternative anti-oxidative stress defense mechanisms operating in some clinical strains.

Strengths:

While the role of ROS in antibiotic mediated killing of mycobacterial cells have been studied to some extent, this paper presents some new findings with regards to genetic analysis of M. abscessus susceptibility, especially against clinically used antibiotics, which makes it useful. Also, the attempts to validate their observations in clinical isolates is appreciated.

Weaknesses:

- Fig. 3 - 5 of the hits from the transposon screen were reconstructed as clean deletion strains and tested for persistence. However, only 1 (katG) gave a strong and 1 (Mab_1456c) exhibited a minor defect. Two of the clones did not show any persistence phenotype (blaR and recR) and one (pafA) showed a minor phenotype, however it was not clear if this difference was really relevant as the mutant exhibited differences at Day 0, prior to the addition of antibiotics. Considering these results from the validation, the conclusion would be that the Tn-seq approach to screen persistence defects is not reliable and is more likely to result in misses than hits.

- Fig 3 - Why is there such a huge difference in the extent of killing of the control strain in media, when exposed to TIG/LZD, when compared to Fig. 1C and Fig. 4. In Fig. 1C, M. abs grown in media decreases by >1 log by Day 3 and >4 log by Day 6, whereas in Fig. 3, the bacterial load decreases by <1 log by Day 3 and <2 log by Day 6. This needs to be clarified, if the experimental conditions were different, because if comparing to Fig. 1C data then the katG mutant strain phenotype is not very different.

Reviewer #2 (Public review):

Summary:

The work set out to better understand the phenomenon of antibiotic persistence in mycobacteria. Three new observations are made using the pathogenic Mycobacterium abscessus as an experimental system: phenotypic tolerance involves suppression of ROS, protein synthesis inhibitors can be lethal for this bacterium, and levofloxacin lethality is unaffected by deletion of catalase, suggesting that this quinolone does not kill via ROS.

Strengths:

The ROS experiments are supported in three ways: measurement of ROS by a fluorescent probe, deletion of catalase increases lethality of selected antibiotics, and a hypoxia model suppresses antibiotic lethality. A variety of antibiotics are examined, and transposon mutagenesis identifies several genes involved in phenotypic tolerance, including one that encodes catalase. The methods are adequate for making these statements.

Weaknesses:

The work can be improved in two major ways. First, word-choice decisions could better conform to the published literature. Alternatively, novel definitions could be included. In particular, the data support the concept of phenotypic tolerance, not persistence. Second, two of the novel observations could be explored more extensively to provide mechanistic explanations for the phenomena.

Overall impact: Showing that ROS accumulation is suppressed during phenotypic tolerance, while expected, adds to the examples of the protective effects of low ROS levels. Moreover, the work, along with a few others, extends the idea of antibiotic involvement with ROS to mycobacteria. These are field-solidifying observations.

Reviewer #3 (Public review):

Summary:

The manuscript demonstrates that starvation induces persister formation in M. abscesses. They also utilized Tn-Seq for the identification of genes involved in persistence. They identified the role of catalase-peroxidase KatG in preventing death from translation inhibitors Tigecycline and Linezolid. They further demonstrated that a combination of these translation inhibitors leads to the generation of ROS in PBS-starved cells.

Strengths:

The authors used high-throughput genomics-based methods for identification of genes playing a role in persistence.

Weaknesses:

The findings could not be validated in clinical strains.

eLife Assessment

This work describes a valuable method, SICKO, for real-time longitudinal quantification of bacterial colonization in the gut of individual C. elegans. The authors present convincing evidence to support the validity of the approach. SICKO provides an experimental framework that will enable progress in our understanding of host-microbe interactions.

Reviewer #1 (Public review):

Summary:

The imaging pipeline presented in this paper is a useful tool for visualizing and dynamically tracking bacterial colony formation at the individual worm level, enabling the study of microbiome colonization's association with host physiology, including lifespan, infection severity, and genetic mutations in real-time. This technique allows for certain biological information to be obtained that was previously missed such as pmk-1 mutants exhibiting a higher rate of colonization by E. coli OP50 than wild-type animals. Overall, this platform could be of interest to many labs studying C. elegans interactions with their microbiome and with bacterial pathogens.

Strengths:

This platform allows for unbiased quantifications of microbe colonization of bacteria at scale. This is particularly important in a field studying dynamic responses or potentially more subtle or variable phenotypes.

Platform could be adapted for multiple uses or potentially other species of nematodes for evolutionary comparisons.

The platform allows researchers to correlate bacterial colonization with predicted lifespan.

Weaknesses:

Platform will require optimization for any given bacteria species which restricts its ease of use for researchers that won't regularly be studying the same bacteria.

Requires the bacteria to be genetically tractable so cannot be easily adapted to microbes that do not have established ways of expressing GFP or other reporters.

This platform requires the use of relatively older adult animals that are more prone to larger gut colonies of bacteria. Thus, studies using this platform are restricted to studying older populations.

The relationship between bacterial colonization and host lifespan requires further investigation. The current SICKO platform and experimentation cannot fully address whether animals in poorer health are more susceptible to colonization, or whether colonization casually contributes to a decline in health. Furthermore, while such effects are statistically significant their effect size in some cases is modest.

Reviewer #2 (Public review):

Summary:

In this manuscript, Espejo et al describe a method, SICKO, that allows for long-term longitudinal examination of bacterial colonization in the gut of C. elegans. SICKO utilizes a well-plate format where single worms are housed in each well with a small NGM pad surrounded by an aversive palmitic acid barrier to prevent worms from fleeing the well. The main benefit of this method is that it captures longitudinal data across individual worms with the ability to capture tens to hundreds of worms at once. The output data of SICKO in the heatmap is also very clear and robustly shows bacterial colonization in the gut across a large sample size, which is far superior to the current gold standard of imaging 10-20 worms in a cross-sectional matter at various timepoints of aging. They then provide a few examples of how this method can be applied to understand how colonization correlates with animal health.

Strengths:

-The method presented in this manuscript is sure to be of great utility to the host-pathogen field of C. elegans. The method also allows for utilization of large sample sizes and a way to present highly transparent data, both of which are excellent for promoting rigor and reproducibility of science.<br /> -The manuscript also does a great job in describing the limitations of the system, which is always appreciated.<br /> -The methods section for the SICKO data analysis pipeline and the availability of the code on Github are strong pluses.

Weaknesses:

-There are minor weaknesses in the methods that could be addressed relatively easily by expanding the explanation of how to set up the individual worm chambers (see comment 1 below).

I am making all my comments and suggestions to the reviewers public, as I believe these comments can be useful to the general readership as well. Comment 1 is important to make the methods more accessible and comment 2 is important to make the data presentation more accessible to a broader audience. However, comments 3-4 are things/suggestions that should be considered by the authors and future users of SICKO for interpretation of all the data presented in the manuscript.

(1) The methods section needs to be described in more detail. Considering that this is a methods development paper, more detailed explanation is required to ensure that readers can actually adapt these experiments into their labs.<br /> (a) What is the volume of lmNGM in each well?<br /> (b) Recommended volume of bacteria to seed in each well?<br /> (c) A file for the model for the custom printed 3D adaptor should be provided.<br /> (d) There should be a bit more detail on how the chambers should be assembled with all the components. After reading this, I am not sure I would be able to put the chamber together myself.<br /> (e) What is the recommended method to move worms into individual wells? Manual picking? Pipetting in a liquid?<br /> (f) Considering that a user-defined threshold is required (challenging for non-experienced users), example images should be provided on what an acceptable vs. nonacceptable threshold would look like.

(2) The output data in 1e is very nice - it is a very nice and transparent plot, which I like a lot. However, since the data is complex, a supplemental figure to explain the data better would be useful to make it accessible for a broader audience. For example, highlighting a few rows (i.e., individual worms) and showing the raw image data for each row would be useful. What I mean is that it would be useful to show what does the worm actually look like for a "large colony size" or "small colony size"? What is the actual image of the worm that represents the yellow (large), versus dark blue (small), versus teal (in the middle)? And also the transition from dark blue to yellow would also be nice to be shown. This can probably also just be incorporated into Fig. 1d by just showing what color each of those worm images from day 1 to day 8 would represent in the heat map (although I still think a dedicated supplemental figure where you highlight a few rows and show matching pictures for each row in image files would be better).

(3) I am not sure that doing a single-time point cross-sectional data is a fair comparison since several studies do multi-timepoint cross-sectional studies (e.g., day 1, day 5, day 9). This is especially true for using only day 1 data - most people do gut colonization assays at later timepoints since the gut barrier has been shown to break down at older ages, not day 1. The data collected by SICKO is done every day across many individuals worms and is clearly superior to this type of cross-sectional data (even with multiple timepoints), and I think this message would be further strengthened by comparing it directly to cross-sectional data collected across more than 1 timepoint of aging.

(4) The authors show that SICKO can detect differences in wild-type vs. pmk-1 loss of function and between OP50 and PA14. However, these are very dramatic conditions that conventional methods can easily detect. I would think that the major benefit of SICKO over conventional methods is that it can detect subtle differences that cross-sectional methods would fail to visualize. It might be useful to see how well SICKO performs for these more subtle effects (e.g., OP50 on NGM vs. bacteria-promoting media; OP50 vs. HT115; etc.).<br /> (a) Similar to the above comment, the authors discuss how pmk-1 has colonization-independent effects on host-pathogen interactions. Maybe using a more direct approach to affect colonization (e.g., perturbing gut actin function like act-5) would be better.

eLife Assessment

This useful paper systematically evaluates B-cell receptor (BCR) repertoires across tumors, tumor-draining lymph nodes, and peripheral blood in patients with melanoma, lung adenocarcinoma, and colorectal cancer. It investigates the interplay between the tumor microenvironment and immune responses, revealing differences in BCR clonotype maturity, hypermutation, and spatial distribution. The study highlights the heterogeneity in immune responses and provides solid insights into the potential of tumor-infiltrating B cells for therapeutic applications, despite limitations in patient cohort size and sequencing methodology.

Reviewer #3 (Public Review):

In multiple cancers, the key roles of B cells are emerging in the tumor microenvironment (TME). The authors of this study appropriately introduce that B cells are relatively under-characterised in the TME and argue correctly that it is not known how the B cell receptor (BCR) repertoires across tumor, lymph node and peripheral blood relate. The authors therefore supply a potentially useful study evaluating the tumor, lymph node and peripheral blood BCR repertoires and site-to-site as well as intra-site relationships. The authors employ sophisticated analysis techniques, although the description of the methods is incomplete.

Major strengths:

(1) The authors provide a unique analysis of BCR repertoires across tumor, dLN, and peripheral blood. The work provides useful insights into inter- and intra-site BCR repertoire heterogeneity. While patient-to-patient variation is expected, the findings with regard to intra-tumor and intra-dLN heterogeneity with the use of fragments from the same tissue are of importance, contribute to the understanding of the TME, and will inform future study design.

(2) A particular strength of the study is the detailed CDR3 physicochemical properties analysis which leads the authors to observations that suggest a less-specific BCR repertoire of TIL-B compared to circulating B cells.

Comments on revisions:

Your efforts in addressing concerns related to methodological details, narrative clarity, and data representation are commendable. The expanded descriptions of Fig. 1A and the experimental design, as well as the restructuring of the discussion, have greatly enhanced the manuscript's clarity and coherence.

Author response:

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

Reviewer #3:

Concerns and comments on current version:

The revision has improved the manuscript but, in my opinion, remains inadequate. While most of my requested changes have been made, I do not see an expansion of Fig1A legend to incorporate more details about the analysis. Lacking details of methodology was a concern from all reviewers.

To address this concern, we expanded Fig.1A legend, and also significantly expanded the text describing experimental design, to also include the description of the data analysis approach.

“BCR repertoires libraries were obtained using the 5’-RACE (Rapid Amplification of cDNA Ends) protocol as previously described21 and sequenced with 150+150 bp read length. This approach allowed us to achieve high coverage for the obtained libraries (Table S1) to reveal information on clonal composition, CDR-H3 properties, IgM/IgG/IgA isotypes and somatic hypermutation load within CDR-H3. For B cell clonal lineage reconstruction and phylogenetic analysis, however, 150+150 bp read length is suboptimal because it does not cover V-gene region outside CDR-H3, where hypermutations also occur. Therefore, to verify our conclusions based on the data obtained by 150+150 bp sequencing (“short repertoires”), for some of our samples we also generated BCR libraries by IG RNA Multiplex protocol (See Materials and Methods) and sequenced them at 250+250 bp read length (“long repertoires”). Libraries obtained by this protocol cover V gene sequence starting from CDR-H1 and capture most of the hypermutations in the V gene. Conclusions about clonal lineage phylogeny were drawn only when they were corroborated by “long repertoire” analysis.

For BCR repertoire reconstruction from sequencing data, we first performed unique molecular identifier (UMI) extraction and error correction (reads/UMI threshold = 3 for 5`RACE and 4 for IG Multiplex libraries). Then, we used MIXCR58 software to assemble reads into clonotypes, determine germline V, D, and J genes, isotypes, and find the boundaries of target regions, such as CDR-H3. Only

UMI counts, and not read counts, were used for quantitative analysis. Clonotypes derived from only one UMI were excluded from the analysis of individual clonotype features but were used to analyze clonal lineages and hypermutation phylogeny, where sample size was crucial. Samples with 50 or less clonotypes left after preprocessing were excluded from the analysis.”

Similarly, the 'fragmented' narrative was a concern of all reviewers. These matters have not been dealt with adequately enough - there are parts of the manuscript which remain fragmented and confusing.

Unfortunately, the reviewers do not give us a hint as to which parts of the text are the most problematic in their opinion. We identified the parts describing physicochemical properties of CDR3s, Intratumoral heterogeneity and Intra-LN heterogeneity as the most problematic, and edited these parts significantly. Also, we significantly edited the Discussion section (please see the Comparison file for details). Other parts sections were also edited to improve readability and clarity.

The narrative and analysis does not explain how the plasma cell bias has been dealt with adequately and in fact is simply just confusing. There is a paragraph at the beginning of the discussion re the plasma cell bias, which should be re-written to be clearer and moved to have a prominent place early in the results. Why are these results not properly presented? They are key for interpretation of the manuscript. Furthermore, the sorted plasma cell sequencing analysis also has only been performed on two patients.

In response to this concern, we moved the section describing plasma cell bias in the bulk BCR repertoires to the main text.

Another issue is that some disease cohorts are entirely composed of patients with metastasis, some without but metastasis is not mentioned. Metastasis has been shown to impact the immune landscape.

Intrinsic heterogeneity of the cohort is indeed one of the weaknesses of our work, which could negatively impact the statistical significance of our results and, as a consequence, mask certain observations or make them less statistically significant. We mention this in the discussion section. It should not, in our understanding, lead to any false conclusions. We did not, however, pool data from primary and metastatic tumor samples, and all tumor samples that we mention are primary tumors.

The following part of a sentence was added to the discussion:

“...which could negatively impact the statistical significance of our results and, as a consequence, mask certain observations or make them less statistically significant.”

A reviewer brought up a concern about the overlap analysis and I also asked for an explanation on why this F2 metric was chosen. Part of the rebuttal argues that another metric was explored showing similar results, thus the conclusion reached is reasonable. Remarkably, these data are not only omitted from the manuscript, but are not even provided for the reviewers.

We did not intend to conceal any data from the reviewers, and we now added the panel for D metric to the S1 figure. We would also like to point out that the panel describing R metric for repertoire overlaps (a measure of similarity of overlapping clonotype frequencies), was included in the first version of the S2 Figure (now S1 Figure), and it also showed a similar trend. We hope that now the data are fully conclusive.

This manuscript certainly includes some interesting and useful work. Unfortunately, a comprehensive re-write was required to make the work much clearer and easier to understand and this has not been realized.

Again, we thank the reviewers for their thorough evaluation, and hopefully we could make the text clearer in the second reviewed version.

eLife Assessment

The paper presents a streamlined new approach for functional validation of genes known to underlie fragile bone disorders in a relatively high throughput, using CRISPR-mediated knockouts and a number of phenotypic assessments in zebrafish. Convincing data demonstrate the feasibility and validity of this approach, which presents an important tool for rapid functional validation of candidate gene(s) associated with heritable bone diseases identified from genetic studies.

Reviewer #1 (Public review):

Summary:

In this work, a screening platform is presented for rapid and cost-effective screening of candidate genes involved in Fragile Bone Disorders. The authors validate the approach of using crispants, generating FO mosaic mutants, to evaluate the function of specific target genes in this particular condition. The design of the guide RNAs is convincingly described, while the effectiveness of the method is evaluated to 60% to 92% of the respective target genes being presumably inactivated. Thus, injected F0 larvae can be directly used to investigate the consequences of this inactivation.

Skeletal formation is then evaluated at 7dpf and 14dpf, first using a transgenic reporter line revealing fluorescent osteoblasts, second using alizarin-red staining of mineralized structures. In general, it appears that the osteoblast-positive areas are more often affected in the crispants compared to the mineralized areas, an observation that appears to correlate with the observed reduced expression of bglap, a marker for mature osteoblasts, and the increased expression of col1a1a in more immature osteoblasts.

Finally, the injected fish (except two lines that revealed a high mortality) are also analyzed at 90dpf, using alizarin red staining and micro-CT analysis, revealing an increased incidence of skeletal deformities in the vertebral arches, fractures, as well as vertebral fusions and compressions for all crispants except those for daam2. Finally, the Tissue Mineral Density (TMD) as determined by micro-CT is proposed as an important marker for investigating genes involved in osteoporosis.<br /> Taken together, this manuscript is well presented, the data are clear and well analyzed, and the methods well described. It makes a compelling case for using the crispant technology to screen the function of candidate genes in a specific condition, as shown here for bone disorders.

Strengths:

Strengths are the clever combination of existing technologies from different fields to build a screening platform. All the required methods are comprehensively described.

Weaknesses:

One may have wished to bring one or two of the crispants to the stage of bona fide mutants, to confirm the results of the screening, however, this is done for some of the tested genes as laid out in the discussion.

Comments on latest version:

All my issues were resolved.

Reviewer #2 (Public review):

Summary:

More and more genes and genetic loci are being linked to bone fragility disorders like osteoporosis and osteogenesis imperfecta through GWAS and clinical sequencing. In this study, the authors seek to develop a pipeline for validating these new candidate genes using crispant screening in zebrafish. Candidates were selected based on GWAS bone density evidence (4 genes) or linkage to OI cases plus some aspect of bone biology (6 genes). NGS was performed on embryos injected with different gRNAs/Cas9 to confirm high mutagenic efficacy, and off-target cutting was verified to be low. Bone growth, mineralization, density, and gene expression levels were carefully measured and compared across crispants using a battery of assays at three different stages.

Strengths:

(1) The pipeline would be straightforward to replicate in other labs, and the study could thus make a real contribution towards resolving the major bottleneck of candidate gene validation.

(2) The study is clearly written and extensively quantified.

(3) The discussion attempts to place the phenotypes of different crispant lines into the context of what is already known about each gene's function.

(4) There is added value in seeing the results for the different crispant lines side by side for each assay.

(5) Caveats to the interpretability of crispant data and limitations of their gene-focused analyses and RT-PCR assays are discussed.

Weaknesses:

(1) The study uses only well-established methods and is strategy-driven rather question/hypothesis-driven. This is in line with the researchers' primary goal of developing a workflow for rapid in vivo functional screening of candidate genes. However, this means that less attention is paid to what the results obtained for a given gene may mean regarding potential disease mechanisms, and how contradictions with prior reports of mouse or fish null mutant phenotypes might be explained.

(2) Normalization to body size was not performed. Measurements of surface area covered by osteoblasts or mineralized bone (Fig. 1) are typically normalized to body size - especially in larvae and juvenile fish - to rule out secondary changes due to delayed or accelerated overall growth. This was not done here; the authors argue that "variations in growth were considered as part of the phenotypic outcome." This is reasonable, but because standard length was reported only for fish at 90 dpf (not significantly different in any line), the reader is not given the opportunity to consider whether earlier differences in, e.g. surface area covered by osteoblasts at 14 dpf, could be accounted for by delayed or accelerated overall growth. Images in Figure S5 were not taken at the same magnification, further confounding this effort.

Comments on latest version:

The authors have largely addressed my comments by making changes to the text.

However, in response to one of my original comments ("It would be helpful to note the grouping of candidates into OI vs. BMD GWAS throughout the figures"), they added a sentence to this effect to the legends. However, because two of the lines were larval-lethal, the legends to Figs. S6-8 are now incorrect in referring to ten genes when only eight mutants are shown.

Reviewer #3 (Public review):

The manuscript describes the use of CRISPR gene editing coupled with phenotyping mosaic zebrafish larvae to characterize functions of genes implicated in heritable fragile bone disorders (FBDs). Authors targeted six high-confident candidate genes implicated in severe recessive forms of FBDs and four Osteoporosis GWAS-implicated genes and observe varied developmental phenotypes across all crispants, in addition to adult skeletal phenotypes. While the study lacks insight on underlying mechanisms that contribute to disease phenotypes, a major strength of the paper is the streamlined method that produced significant phenotypes for all candidate genes tested. It also represents a significant increase in number of candidate genes tested using their crispant approach beyond the single mutant that was previously published.

One weakness was the variability of developmental phenotypes, addressed by authors in the Discussion. This might be a product of maternal transcripts not targeted by CRISPR or genetic compensation, which authors have not fully explored. Overall, the paper was well-written and easy to read.

Comments on latest version:

The authors have addressed many concerns in this revision. Figure 1 and Table 2 are much improved.

While details of orthologous gene expression profiles of target genes is a welcome addition, other features of target genes remain unaddressed. For example, do genes with maternally deposited transcript exhibit dampened phenotypes? Or does genetic compensation impact certain genes more than others? Since authors state that the study represents a methods paper, it will be important for users to understand the caveats of gene selection to effectively implement and interpret results of the approach.

Author response:

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

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this work, a screening platform is presented for rapid and cost-effective screening of candidate genes involved in Fragile Bone Disorders. The authors validate the approach of using crispants, generating FO mosaic mutants, to evaluate the function of specific target genes in this particular condition. The design of the guide RNAs is convincingly described, while the effectiveness of the method is evaluated to 60% to 92% of the respective target genes being presumably inactivated. Thus, injected F0 larvae can be directly used to investigate the consequences of this inactivation.

Skeletal formation is then evaluated at 7dpf and 14dpf, first using a transgenic reporter line revealing fluorescent osteoblasts, and second using alizarin-red staining of mineralized structures. In general, it appears that the osteoblast-positive areas are more often affected in the crispants compared to the mineralized areas, an observation that appears to correlate with the observed reduced expression of bglap, a marker for mature osteoblasts, and the increased expression of col1a1a in more immature osteoblasts.

Finally, the injected fish (except two lines that revealed high mortality) are also analyzed at 90dpf, using alizarin red staining and micro-CT analysis, revealing an increased incidence of skeletal deformities in the vertebral arches, fractures, as well as vertebral fusions and compressions for all crispants except those for daam2. Finally, the Tissue Mineral Density (TMD) as determined by micro-CT is proposed as an important marker for investigating genes involved in osteoporosis.

Taken together, this manuscript is well presented, the data are clear and well analyzed, and the methods are well described. It makes a compelling case for using the crispant technology to screen the function of candidate genes in a specific condition, as shown here for bone disorders.

Strengths:

Strengths are the clever combination of existing technologies from different fields to build a screening platform. All the required methods are comprehe Zebrafish tanks_13062024nsively described.

We would like to thank the reviewer for highlighting the strengths of our paper.  

Weaknesses:

One may have wished to bring one or two of the crispants to the stage of bona fide mutants, to confirm the results of the screening, however, this is done for some of the tested genes as laid out in the discussion.

We thank the reviewer for their comment. We would like to point out that indeed similar phenotypes have been observed in existing models, as mentioned in the discussion section.

Reviewer #2 (Public review):

Summary:

More and more genes and genetic loci are being linked to bone fragility disorders like osteoporosis and osteogenesis imperfecta through GWAS and clinical sequencing. In this study, the authors seek to develop a pipeline for validating these new candidate genes using crispant screening in zebrafish. Candidates were selected based on GWAS bone density evidence (4 genes) or linkage to OI cases plus some aspect of bone biology (6 genes). NGS was performed on embryos injected with different gRNAs/Cas9 to confirm high mutagenic efficacy and off-target cutting was verified to be low. Bone growth, mineralization, density, and gene expression levels were carefully measured and compared across crispants using a battery of assays at three different stages.

Strengths:

(1) The pipeline would be straightforward to replicate in other labs, and the study could thus make a real contribution towards resolving the major bottleneck of candidate gene validation.

(2) The study is clearly written and extensively quantified.

(3) The discussion attempts to place the phenotypes of different crispant lines into the context of what is already known about each gene's function.

(4) There is added value in seeing the results for the different crispant lines side by side for each assay.

We would like to thank the reviewer for highlighting the strengths of our paper.  

Weaknesses:

(1) The study uses only well-established methods and is strategy-driven rather than question/hypothesis-driven.

We thank the reviewer for this correct remark. The mayor aim of this study was to establish a workflow for rapid in vivo functional screening of candidate genes across a broad range of FBDs. 

(2) Some of the measurements are inadequately normalized and not as specific to bone as suggested:

(a) The measurements of surface area covered by osteoblasts or mineralized bone (Figure 1) should be normalized to body size. The authors note that such measures provide "insight into the formation of new skeletal tissue during early development" and reflect "the quantity of osteoblasts within a given structure and [is] a measure of the formation of bone matrix." I agree in principle, but these measures are also secondarily impacted by the overall growth and health of the larva. The surface area data are normalized to the control but not to the size/length of each fish - the esr1 line in particular appears quite developmentally advanced in some of the images shown, which could easily explain the larger bone areas. The fact that the images in Figure S5 were not all taken at the same magnification further complicates this interpretation.

We thank the reviewer for this detailed and insightful remark. We agree with the reviewer and recognize that the results may be influenced by size differences. However, we do not normalize for size, as variations in growth were considered as part of the phenotypic outcome. This consideration has been addressed in the discussion section.

Line 335-338: ‘Although the measurements of osteoblast-positive and mineralized surface areas may be influenced by size differences among some of the crispants, normalization to size parameters was not conducted, as variations in growth were considered integral to the phenotypic outcome.’

Line 369: ‘Phenotypic variability in these zebrafish larvae can be attributed to several factors, including crispant mosaicism, allele heterogeneity, environmental factors, differences in genomic background and development, and slightly variable imaging positioning.’

(b) Some of the genes evaluated by RT-PCR in Figure 2 are expressed in other tissues in addition to bone (as are the candidate genes themselves); because whole-body samples were used for these assays, there is a nonzero possibility that observed changes may be rooted in other, non-skeletal cell types.

We thank the reviewer for this valuable comment. We acknowledge that the genes assessed by RT-PCR are expressed in other tissues beyond bone. This consideration has been addressed in the discussion section.

Line 362-365: “However, it is important to note that the genes evaluated by RT-PCR are not exclusively expressed in bone tissue. Since whole-body samples were used for expression analysis, there is a possibility that the observed changes in gene expression may be influenced by other non-skeletal cell types”.

(3) Though the assays evaluate bone development and quality at several levels, it is still difficult to synthesize all the results for a given gene into a coherent model of its requirement.

We appreciate the reviewer’s  remark. We acknowledge that the results for the larval stages exhibit variability, making it challenging to synthesize them into a coherent model. However, it is important to emphasize that all adult crispant consistently display a skeletal phenotype. Consequently, the feasibility and reproducibility of this screening method are primarily focusing on the adult stages. This consideration has been addressed in the discussion section of the manuscript.

Line 391-399: ‘In adult crispants, the skeletal phenotype was generally more penetrant. All crispants showed malformed arches, a majority displayed vertebral fractures and fusions and some crispants exhibited distinct quantitative variations in vertebral body measurements. This confirmed the role of the selected genes in skeletal development and homeostasis and their involvement in skeletal disease and established the crispant approach as a valid approach for rapidly providing in vivo gene function data to support candidate gene identification.’

(4) Several additional caveats to crispant analyses are worth noting:

(a) False negatives, i.e. individual fish may not carry many (or any!) mutant alleles. The crispant individuals used for most assays here were not directly genotyped, and no control appears to have been used to confirm successful injection. The authors therefore cannot rule out that some individuals were not, in fact, mutagenized at the loci of interest, potentially due to human error. While this doesn't invalidate the results, it is worth acknowledging the limitation.

We thank the reviewer for this valuable remark. We recognize the fact that working with crispants has certain limitations, including the possibility that some individuals may carry few or no mutant alleles. To address this issue, we use 10 individual crispants during the larval stage and 5 during the adult stage. Although some individuals may lack the mutant alleles, using multiple fish helps reduce the risk of false negatives.

Furthermore, we perform NGS analysis on pools of 10 embryos from the same injection clutch as the fish used in the various assays to assess the indel efficiency. While there remains a possibility of false negatives, the overall indel efficiency, as indicated by our NGS analysis,  is high (>90%), thereby reducing the likelihood of having crispants with very low indel efficiency. We included this in the discussion.

Line 387-390: ‘While there remains a possibility of false negatives, the overall indel efficiency, as indicated by our NGS analysis,  is high (>90%), thereby reducing the likelihood of having crispants with very low indel efficiency.’

(b) Many/most loci identified through GWAS are non-coding and not easily associated with a nearby gene. The authors should discuss whether their coding gene-focused pipeline could be applied in such cases and how that might work.

The authors thank the reviewer for this insightful comment. Our study is focused on strong candidate genes rather than non-coding variants. We recognize that the use of this workflow poses challenges for analyzing non-coding variants, which represents a limitation of the crispant approach. We have addressed this issue in the discussion section of the manuscript.

Line 131: ‘Gene-based’

Line 453: ‘Gene-based’

Line 311-314: ‘It is important to note that this study focused on candidate genes for osteoporosis, not on the role of specific variants identified in GWAS studies. Non-coding variants for instance, which are often identified in GWAS studies,  present significant challenges in terms of functional validation and interpretation.’

Reviewer #3 (Public review):

Summary:

The manuscript "Crispant analysis in zebrafish as a tool for rapid functional screening of disease-causing genes for bone fragility" describes the use of CRISPR gene editing coupled with phenotyping mosaic zebrafish larvae to characterize functions of genes implicated in heritable fragile bone disorders (FBDs). The authors targeted six high-confident candidate genes implicated in severe recessive forms of FBDs and four Osteoporosis GWAS-implicated genes and observed varied developmental phenotypes across all crispants, in addition to adult skeletal phenotypes.

A major strength of the paper is the streamlined method that produced significant phenotypes for all candidate genes tested.

We would like to thank the reviewer for highlighting the strengths of our paper.  

A major weakness is a lack of new insights into underlying mechanisms that may contribute to disease phenotypes, nor any clear commonalities across gene sets. This was most evident in the qRT-PCR analysis of select skeletal developmental genes, which all showed varied changes in fold and direction, but with little insight into the implications of the results.

We thank the reviewer for this insightful remark. We want to emphasize that this study focusses on establishing a new screening method for candidate genes involved in FBDs, rather than investigating the underlying mechanisms contributing to disease phenotypes. However, to investigate the underlying mechanisms in these crispants, the creation of bona fide mutants is necessary. We have included this consideration in the discussion.

Furthermore, we acknowledge that the results for the larval stages exhibit variability, which can complicate the interpretation of these findings. This is particularly true for the RT-PCR analysis, where whole-body samples were used, raising the possibility that other tissues may influence the expression results. Therefore, our primary focus is on the adult stages, as all crispants display a skeletal phenotype at this age. We have elaborated on this point in the discussion.

Line 462-463: ‘Moreover, to explore the underlying mechanisms contributing to disease phenotypes, it is essential to establish stable knockout mutants derived from the crispants’.

Line 391-399: ‘In adult crispants, the skeletal phenotype was generally more penetrant. All crispants showed malformed arches, a majority displayed vertebral fractures and fusions and some crispants exhibited distinct quantitative variations in vertebral body measurements. This confirmed the role of the selected genes in skeletal development and homeostasis and their involvement in skeletal disease and established the crispant approach as a valid approach for rapidly providing in vivo gene function data to support candidate gene identification.’

Ultimately, the authors were able to show their approach is capable of connecting candidate genes with perturbation of skeletal phenotypes. It was surprising that all four GWAS candidate genes (which presumably were lower confidence) also produced a result.

We appreciate the reviewer’s comment. We would like to direct attention to the discussion section, where we offer a possible explanation for the observation that all four GWAS candidate genes produce a skeletal phenotype.

Line 460-410: 'The more pronounced and earlier phenotypes in these zebrafish crispants are most likely attributed to the quasi knock-out state of the studied genes, while more common less impactful variants in the same genes result in typical late-onset osteoporosis (Laine et al., 2013) . This phenomenon is also observed in knock-out mouse models for these genes (Melville et al., 2014)(Coughlin et al., 2019).’

These authors have previously demonstrated that crispants recapitulate skeletal phenotypes of stable mutant lines for a single gene, somewhat reducing the novelty of the study.

We thank the reviewer for this comment and appreciate their concern. We have indeed demonstrated that crispants can recapitulate the skeletal phenotypes observed in stable mutant lines for the osteoporosis gene LRP5. However, we would like to highlight that the current study represents the first large-scale screening of candidate genes associated with bone disorders, including genes related to both OI and osteoporosis. We have included this information in both the abstract and the discussion

Line 60-62: ‘We advocate for a novel comprehensive approach that integrates various techniques and evaluates distinct skeletal and molecular profiles across different developmental and adult stages.’

Line 456-457: ‘While this work represents a pioneering effort in establishing a screening platform for skeletal diseases, it offers opportunities for future improvement and refinement.’

Recommendations for the authors:

Reviewer #1 (Recommendations for the authors):

(1) Figure 1a: what does the differential shading of the bone elements represent? Explain in the legend.

The differential shading doesn't represent anything specific. It's simply used to enhance the visual appeal and to help distinguish between the different structures. We removed the shading in the figure.

(2) Supplementary Figures 2-5: should the numbering of these figures be also in order of appearance in the text? I understand that the authors prefer to associate the transgenic and the alizarin red-stained specimens, however, the reading would be easier that way.

We changed this accordingly.

(3) Lines 275-276: "no significant differences in standard length (Figure 4a)": should be Figure 4b.

The suggested changes are incorporated in the manuscript.

Line 276-277: ‘Among the eight crispants that successfully matured into adulthood, none exhibited significant differences in standard length and head size (n=5 fish per crispant) (Figure 4b).’

(4) Line 277 "larger eye diameter": should be Figure 4b.

The suggested changes are incorporated in the manuscript.

Line 378: ‘However, esr1 crispants were observed to have notably larger eye diameters (Figure 4b).’

(5) Line 280: "no obvious abnormalities were detected (Figure 4b,c)": should be Figure 4a, c. Note that the authors may reconsider the a, b, c numbering in Figure 4 by inverting a and b.

The suggested changes are incorporated in the manuscript.

Line 278-281: ‘All these crispants demonstrated various abnormalities in the caudal part of the vertebral column such as fusions, compressions, fractures, or arch malformations, except for daam2 crispants where no obvious abnormalities were detected (Figure 4a,c; Supplementary Figure 6).’

(6) Table 2: This table, which recapitulates all the results presented in the manuscript, is in the end the centerpiece of the work. It is however difficult to read in its present form. Three suggestions:

- Transpose it such that each gene has its own column, and the lines give the results for the different measurements

- Place the measurements that result in "ns" for all crispants at the end (bottom) of the table.

- Maybe bring the measurements at 7dpf, 14dpf, and 90 dpf together.

We agree with the reviewer and have added a new table where we transposed the data. However, we chose not to place the measurements that resulted in 'ns' for all crispants at the end of the table, as we believe it is important to track the evolution of the phenotype over time. Where possible, we have grouped the measurements for 7 dpf and 14 dpf together.

Reviewer #2 (Recommendations for the authors):

(1) It would help to justify why these particular area measurements are appropriate for this set of candidate genes, which were selected based on putative links to bone quality rather than bone development.

The selected methods are among the most commonly used to evaluate bone phenotypes. They are straightforward to reproduce, as well as cost- and time-effective. The strength of this approach lies in its use of simple, reproducible techniques that form the foundation for characterizing bone development.  Although the candidate genes were chosen based on their putative links to bone quality, early skeletal phenotypes can already be observed during bone development.

The mineralized surface area of the total head and specific head structures was selected to evaluate the degree of mineralization in early skeletal development, as mineralization is a direct indicator of bone formation. Additionally, the osteoblast-positive surface areas were measured to provide insight into the formation of new skeletal tissue during early development. Osteoblasts, as active bone-forming cells, are essential for understanding bone growth and the dynamics of skeletal phenotypes.

Examples in the manuscript:

Line 212-214: ‘The osteoblast-positive areas in both the total head and the opercle were then quantified to gain insight into the formation of new skeletal tissue during early development.’

Line 221-223: ‘Subsequently, Alizarin Red S (ARS) staining was conducted on the same 7 and 14 dpf crispant zebrafish larvae in order to evaluate the degree of mineralization in the early skeletal structures.’

(2) Reword: The opercle bone is the earliest forming bone of the opercular series, and appears to be what the authors are referring to as the "operculum" at 7-14 dpf. The operculum is the larger structure (gill cover) in which the opercle is embedded. It would be more accurate to simply refer to the opercle at these stages.

We agree with this comment and changed the text accordingly.

(3) Define BMD and TMD at first usage.

BMD and TMD are now defined in the manuscript.

Line 41-43: ‘Six genes associated with severe recessive forms of Osteogenesis Imperfecta (OI) and four genes associated with bone mineral density (BMD), a key osteoporosis indicator, identified through genome-wide association studies (GWAS) were selected.’

Line 286-288: ‘For each of the vertebral centra, the length, tissue mineral density (TMD), volume, and thickness were determined and tested for statistical differences between groups using a regression-based statistical test (Supplementary Figure 7).’

(4) It would be helpful to note the grouping of candidates into OI vs. BMD GWAS throughout the figures.

We agree with this comment and added this to all figure legends.

‘The first four genes are associated with the pathogenesis of osteoporosis, while the last six are linked to osteogenesis imperfecta’

Reviewer #3 (Recommendations for the authors):

Major points:

(1) For the Results, it would be useful to the Reader to justify the selection of human candidate genes and their associated zebrafish orthologs to model skeletal functions. For example, what are variants identified from human studies, and do they impact functional domains? Are these domains and/or proteins conserved between humans/zebrafish? Is there evidence of skeletal expression in humans/zebrafish?

Supplementary Table 4 lists the selected human candidate genes with reported mutations and/or polymorphisms associated with both skeletal and non-skeletal phenotypes. The table also includes additional findings from studies in mice and zebrafish. An extra column was now added to indicate gene conservation between human and zebrafish. We consulted UniProt (https://www.uniprot.org) and ZFIN (https://zfin.org) to assess the skeletal expression of these genes in human and zebrafish. All genes showed expression in the trabecular bone and/or bone marrow in humans, as well as in bone elements in zebrafish. We added this in the discussion.

Line 309: ‘All selected genes show skeletal expression in both human and zebrafish.’

Supplemental table 4 legend: ‘The conservation between human and zebrafish is reported in the last column.’

As part of this, some version of Supplementary Table 4 might be included as a main display to introduce the targeted genes, ideally separated by rare (recessive OI) vs. common disease (osteoporosis). In the case of common disease and GWAS hits, how did authors narrow in on candidate genes (which often have Mbp-scale associated regions spanning multiple genes)? Further, what is the evidence that the mechanism of action of the GWAS variant is haploinsufficiency modeled by their crispant zebrafish?

We have kept Supplementary Table 4 in the supplementary material but have referred to it earlier in the manuscript’s introduction. Consequently, the table has been renumbered from ‘Supplementary Table 4’  to ‘Supplementary Table 1’.

The selection of genes potentially involved in the pathogenesis of osteoporosis is based on the data from the GWAS catalog, which annotates SNPs using the Ensemble mapping pipeline. The available annotation on their online search interface includes any Ensemble genes to which a SNP maps, or the closest upstream and downstream gene within a 50kb window. Four genes were selected for this screening method based on the criteria outlined in the results section. In this study, we aim to evaluate the general involvement of specific genes in bone metabolism, rather than to model a specific variant.

Line 135-136 and 309-311: ‘An overview of the selected genes with observed mutant phenotypes in human, mice and zebrafish is provided in Supplementary Table 1.’

(2) Using the crispant approach does not impact maternally-deposited RNAs that would dampen early developmental phenotypes. Considering the higher variability in larval phenotypes, perhaps the maternal effect plays a role. The authors might investigate developmental expression profiles of their genes using existing RNA-seq datasets such as from White et al (doi: 10.7554/eLife.30860).

We thank the reviewer for this comment and agree with the possibility that maternally-deposited RNAs might have an impact on early developmental phenotypes. We included this in the discussion.

Line 369-372: ‘Phenotypic variability in these zebrafish larvae can be attributed to several factors, including crispant mosaicism, allele heterogeneity, environmental factors, differences in genomic background and development, maternally-deposited RNAs, and slightly variable imaging positioning.’

(3) While making comparisons within a clutch of mutant vs scrambled control is crucial, it is also important to ensure phenotypes are not specific to a single clutch. Do phenotypes remain consistent across different crosses/clutches?

Yes, phenotypes remain consistent across different crosses and clutches. We included images from a second clutch in the Supplementary material (Supplementary Figure 8) and refereed to it in the discussion.

Line 394-397: ‘Additionally, these skeletal malformations were consistently observed in a second clutch of crispants (Supplementary Figure 8), underscoring the reproducibility of these phenotypic features across independent clutches.’

(4) Understanding that antibodies may not exist for many of the selected genes for zebrafish, authors should verify haploinsufficiency using an RT-qPCR of targeted genes in crispants vs. controls.

We appreciate the reviewer’s suggestion to use RT-qPCR to examine expression levels of the targeted genes in crispants. However, previous experience suggests that relying on RNA expression to verify haploinsufficiency in zebrafish can be challenging. In zebrafish KO mutants, RT-qPCR often still detects gene transcripts, potentially due to incomplete nonsense-mediated decay (NMD) of the mutated mRNA, which may allow residual expression even in the absence of functional protein. As a more definitive approach, we prefer to use antibodies to confirm haploinsufficiency at the protein level. However, as the reviewer noted, generating and applying specific antibodies in zebrafish remains challenging.

(5) Please indicate how parametric vs. non-parametric statistical tests were selected for datasets.

We initially selected the parametric unpaired t-test, assuming the data were normally distributed with similar variances between groups. We verified the assumption of equal variances using the F-test, which was not significant across all assays. However, we did not assess the normality of the data directly, meaning we cannot confirm the normality assumption required for the t-test. Given this, we have opted to use the non-parametric Mann-Whitney U test, which does not require assumptions of normality, to ensure the robustness of our statistical analyses. We changed the Figures, the figure legends and the text accordingly.

(6) In the figures and tables, I recommend adding notation showing the grouping of the first four genes as GWAS osteoporosis, the next three genes as osteoblast differentiation, the next two genes as bone mineralization, and the final gene as collagen transport to orient the reader. One might expect there to be a clustering of phenotypic outcomes based on the selection of genes, and it would be easier to follow this. This would be particularly useful to include in Table 2.

Our primary objective is to assess the feasibility and reproducibility of the crispant screen rather than performing an in-depth pathway analysis or categorizing genes by biological processes. For this purpose, we have organized candidate genes based on their relevance to osteoporosis and Osteogenesis Imperfecta, without subdividing them further. We have clarified this focus in the figure legends, as suggested in an earlier recommendation.

(7) For Figure 1, consider adding a smaller zoomed version of 1a embedded in each sub-figure with each measured element highlighted to improve readability.

We agree with this comment and changed the figure accordingly.

Minor points:

(1) Table 2 could be simplified to improve readability. The headers have redundancies across columns with varied time points and could be merged.

The suggested changes are incorporated in the manuscript (see earlier comment about this).

(2) "BMD" is not defined in the Abstract. This is a personal preference, but there were numerous abbreviations in the text that made it difficult to follow at times.

The suggested changes are incorporated in the manuscript (see earlier comment about this).

eLife Assessment

This manuscript describes important findings on a rhizobial effector, its cleavage, and legume receptors involved in symbiosis. The evidence supporting the main claims is solid, though some conclusions would benefit from additional investigation. The findings have potential implications beyond bacterial interactions with plants.

Reviewer #1 (Public review):

Bacterial effectors that interfere with the inner molecular workings of eukaryotic host cells are of great biological significance across disciplines. On the one hand they help us to understand the molecular strategies that bacteria use to manipulate host cells. On the other hand they can be used as research tools to reveal molecular details of the intricate workings of the host machinery that is relevant for the interaction/defence/symbiosis with bacteria. The authors investigate the function and biological impact of a rhizobial effector that interacts with and modifies, and curiously is modified by, legume receptors essential for symbiosis. The molecular analysis revealed a bacterial effector that cleaves a plant symbiosis signaling receptor to inhibit signaling and the host counterplay by phosphorylation via a receptor kinase. These findings have potential implications beyond bacterial interactions with plants.

Bao and colleagues investigated how rhizobial effector proteins can regulate the legume root nodule symbiosis. A rhizobial effector is described to directly modify symbiosis-related signaling proteins, altering the outcome of the symbiosis. Overall, the paper presents findings that will have a wide appeal beyond its primary field.

Out of 15 identified effectors from Sinorhizobium fredii, they focus on the effector NopT, which exhibits proteolytic activity and may therefore cleave specific target proteins of the host plant. They focus on two Nod factor receptors of the legume Lotus japonicus, NFR1 and NFR5, both of which were previously found to be essential for the perception of rhizobial nod factor, and the induction of symbiotic responses such as bacterial infection thread formation in root hairs and root nodule development (Madsen et al., 2003, Nature; Tirichine et al., 2003; Nature). The authors present evidence for an interaction of NopT with NFR1 and NFR5. The paper aims to characterize the biochemical and functional consequences of these interactions and the phenotype that arises when the effector is mutated.

Evidence is presented that in vitro NopT can cleave NFR5 at its juxtamembrane region. NFR5 appears also to be cleaved in vivo. and NFR1 appears to inhibit the proteolytic activity of NopT by phosphorylating NopT. When NFR5 and NFR1 are ectopically over-expressed in leaves of the non-legume Nicotiana benthamiana, they induce cell death (Madsen et al., 2011, Plant Journal). Bao et al., found that this cell death response is inhibited by the coexpression of nopT. Mutation of nopT alters the outcome of rhizobial infection in L. japonicus. These conclusions are well supported by the data.

The authors present evidence supporting the interaction of NopT with NFR1 and NFR5. In particular, there is solid support for cleavage of NFR5 by NopT (Figure 3) and the identification of NopT phosphorylation sites that inhibit its proteolytic activity (Figure 4C). Cleavage of NFR5 upon expression in N. benthamiana (Figure 3A) requires appropriate controls (inactive mutant versions) that have been provided, since Agrobacterium as a closely rhizobia-related bacterium might increase defense related proteolytic activity in the plant host cells.

Key results from N. benthamiana appear consistent with data from recombinant protein expression in bacteria. For the analysis in the host legume L. japonicus transgenic hairy roots were included. To demonstrate that the cleavage of NFR5 occurs during the interaction in plant cells the authors build largely on western blots. Regardless of whether Nicotiana leaf cells or Lotus root cells are used as the test platform, the Western blots indicate that only a small proportion of NFR5 is cleaved when co-expressed with nopT, and most of the NFR5 persists in its full-length form (Figures 3A-D). It is not quite clear how the authors explain the loss of NFR5 function (loss of cell death, impact on symbiosis), as a vast excess of the tested target remains intact. It is also not clear why a large proportion of NFR5 is unaffected by the proteolytic activity of NopT. This is particularly interesting in Nicotiana in the absence of Nod factor that could trigger NFR1 kinase activity.

Comments on latest version:

The presentation of the figures and the language has greatly improved and the specific mistakes pointed out in the last review have been corrected. I especially appreciate the new images used to illustrate the observed mutant phenotypes, which are much clearer and easier to understand. The pictures used to illustrate the mutant phenotypes seem to be of more comparable root regions than before. Overall, the requested changes have been implemented, with some exceptions described below.

• Figure 1: New representative images are shown for BAX1 and CERK1. These pictures are more consistent with the phenotype seen in other treatments, but since the data has not changed, I presume the data from leaf discs (where the leaf discs for these treatments looked very different) previously shown is still included. The criteria for what was considered cell death is in my opinion still not described in the legend. The cell death/total ratio has been added for all leaf discs, as requested.<br /> • Figure 2: the discussion of the figure now emphasizes direct protein interaction. There is still no size marker in 2D or a description of size in the figure legend, making it difficult to compare the result to Figure 3. If I understand the rebuttal comments correctly, there are other bands on the blot, including non-specific bands. This does not negate the need to include the full blot as a supplemental figure to show cleaved NFR5 as well as other bands. I do not see any other clarifications on this subject in the manuscript.<br /> • Figure 5: From the pictures, it is now easier to understand what is meant by "infection foci". Although there is no description in the methods of how these were distinguished from infection threads, I believe the images are clear enough.<br /> • Figure 6: The changes in the discussion are appreciated, but panel E still misrepresents the evidence in the paper, as from the drawing it still seems that the cleaved NFR5 is somehow directly responsible for suppressing infection when this was not shown

Reviewer #2 (Public review):

Summary:

This manuscript presents data demonstrating NopT's interaction with Nod Factor Receptors NFR1 and NFR5 and its impact on cell death inhibition and rhizobial infection. The identification of a truncated NopT variant in certain Sinorhizobium species adds an interesting dimension to the study. These data try to bridge the gaps between classical Nod-factor-dependent nodulation and T3SS NopT effector-dependent nodulation in legume-rhizobium symbiosis. Overall, the research provides interesting insights into the molecular mechanisms underlying symbiotic interactions between rhizobia and legumes.

Strengths:

The manuscript nicely demonstrates NopT's proteolytic cleavage of NFR5, regulated by NFR1 phosphorylation, promoting rhizobial infection in L. japonicus. Intriguingly, authors also identify a truncated NopT variant in certain Sinorhizobium species, maintaining NFR5 cleavage but lacking NFR1 interaction. These findings bridge the T3SS effector with the classical Nod-factor-dependent nodulation pathway, offering novel insights into symbiotic interactions.

Weaknesses:

(1) In the previous study, when transiently expressed NopT alone in Nicotiana tobacco plants, proteolytically active NopT elicited a rapid hypersensitive reaction. However, this phenotype was not observed when expressing the same NopT in Nicotiana benthamiana (Figure 1A). Conversely, cell death and a hypersensitive reaction were observed in Figure S8. This raises questions about the suitability of the exogenous expression system for studying NopT proteolysis specificity.

(2) NFR5 Loss-of-function mutants do not produce nodules in the presence of rhizobia in lotus roots, and overexpression of NFR1 and NFR5 produces spontaneous nodules. In this regard, if the direct proteolysis target of NopT is NFR5, one could expect the NGR234's infection will not be very successful because of the Native NopT's specific proteolysis function of NFR5 and NFR1. Conversely, in Figure 5, authors observed the different results.

(3) In Figure 6E, the model illustrates how NopT digests NFR5 to regulate rhizobia infection. However, it raises the question of whether it is reasonable for NGR234 to produce an effector that restricts its own colonization in host plants.

(4) The failure to generate stable transgenic plants expressing NopT in Lotus japonicus is surprising, considering the manuscript's claim that NopT specifically proteolyzes NFR5, a major player in the response to nodule symbiosis, without being essential for plant development.

Comments on revised version:

This version has effectively addressed most of my concerns. However, one key issue remains unresolved regarding the mechanism of NopT in regulating nodule symbiosis. Specifically, the explanation of how NopT catabolizes NFR5 to regulate symbiosis is still not convincing within the current framework of plant-microbe interaction, where plants are understood to genetically control rhizobial colonization.

While alternative regulatory mechanisms in plant-microbe interactions are plausible, the notion that the NRG234-secreted effector NopT could reduce its own infection by either suppressing plant immunity or degrading the symbiosis receptor remains unsubstantiated. I believe further revisions are needed in the discussion section to more clearly address and clarify these findings and any lingering uncertainties.

Author response:

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

eLife Assessment

This valuable study reveals how a rhizobial effector protein cleaves and inhibits a key plant receptor for symbiosis signaling, while the host plant counters by phosphorylating the effector. The molecular evidence for the protein-protein interaction and modification is solid, though biological evidence directly linking effector cleavage to rhizobial infection is incomplete. With additional functional data, this work could have implications for understanding intricate plant-microbe dynamics during mutualistic interactions.

Thank you for this positive comment. Our data strongly support the view that NFR5 cleavage by NopT impairs Nod factor signaling resulting in reduced rhizobial infection. However, other mechanisms may also have an effect on the symbiosis, as NopT targets other proteins in addition to NFR5. In our revised manuscript version, we discuss the possibility that negative NopT effects on symbiosis could be due to NopT-triggered immune responses. As mentioned in our point-by-point answers to the Reviewers, we included additional data into our manuscript. We would also like to point out that we are generally more cautious in our revised version in order to avoid over-interpreting the data obtained.

Public Reviews:

Reviewer #1 (Public Review):

Bacterial effectors that interfere with the inner molecular workings of eukaryotic host cells are of great biological significance across disciplines. On the one hand they help us to understand the molecular strategies that bacteria use to manipulate host cells. On the other hand they can be used as research tools to reveal molecular details of the intricate workings of the host machinery that is relevant for the interaction/defence/symbiosis with bacteria. The authors investigate the function and biological impact of a rhizobial effector that interacts with and modifies, and curiously is modified by, legume receptors essential for symbiosis. The molecular analysis revealed a bacterial effector that cleaves a plant symbiosis signaling receptor to inhibit signaling and the host counterplay by phosphorylation via a receptor kinase. These findings have potential implications beyond bacterial interactions with plants.

Thank you for highlighting the broad significance of rhizobial effectors in understanding legume-rhizobia interactions. We fully agree with your assessment and have expanded our Discussion (and Abstract) regarding the potential implications of our findings beyond bacterial interactions with plants. We mention the prospect of developing specific kinase-interacting proteases to fine-tune cellular signaling processes in general.

Bao and colleagues investigated how rhizobial effector proteins can regulate the legume root nodule symbiosis. A rhizobial effector is described to directly modify symbiosis-related signaling proteins, altering the outcome of the symbiosis. Overall, the paper presents findings that will have a wide appeal beyond its primary field.

Out of 15 identified effectors from Sinorhizobium fredii, they focus on the effector NopT, which exhibits proteolytic activity and may therefore cleave specific target proteins of the host plant. They focus on two Nod factor receptors of the legume Lotus japonicus, NFR1 and NFR5, both of which were previously found to be essential for the perception of rhizobial nod factor, and the induction of symbiotic responses such as bacterial infection thread formation in root hairs and root nodule development (Madsen et al., 2003, Nature; Tirichine et al., 2003; Nature). The authors present evidence for an interaction of NopT with NFR1 and NFR5. The paper aims to characterize the biochemical and functional consequences of these interactions and the phenotype that arises when the effector is mutated.

Thank you for your positive feedback.  We have now emphasized the interdisciplinary significance of our work in the Introduction and Discussion of our revised manuscript. We highlight how the insights gained from our study can contribute to a better understanding of microbial interactions with eukaryotic hosts in general, and hope that our findings could benefit future research in the fields of pathogenesis, immunity, and symbiosis.

We appreciate your detailed summary of our work, which is focused on NopT and its interaction with Nod factor receptors. To ensure that the readers can easily follow the rationale behind our work, we have included a more detailed explanation of how NopT was identified to target Nod factor receptors. In particular, we now better describe the test system (Nicotiana benthamiana cells co-expressing NFR1/NFR5 with a given effector of Sinorhizobium fredii NGR234). In addition, we provide now a more thorough background on the roles of NFR1 and NFR5 in symbiotic signaling and refer to the two Nature papers from 2003 on NFR1 and NFR5 (Madsen et al., 2003; Radutoiu et al., 2003).

Evidence is presented that in vitro NopT can cleave NFR5 at its juxtamembrane region. NFR5 appears also to be cleaved in vivo. and NFR1 appears to inhibit the proteolytic activity of NopT by phosphorylating NopT. When NFR5 and NFR1 are ectopically over-expressed in leaves of the non-legume Nicotiana benthamiana, they induce cell death (Madsen et al., 2011, Plant Journal). Bao et al., found that this cell death response is inhibited by the coexpression of nopT. Mutation of nopT alters the outcome of rhizobial infection in L. japonicus. These conclusions are well supported by the data.

We appreciate your recognition of the robustness of our conclusions. In the context of your comments, we made the following improvements to our manuscript:

We included a more detailed description of the experimental conditions under which the cleavage of NFR5 by NopT was observed in vitro and in vivo. Furthermore, additional experiments were added to strengthen the evidence for NFR5 cleavage by NopT (Fig 3, S3, S6, and S14).

We provided more comprehensive data on the phosphorylation of NopT by NFR1, including phosphorylation assays (Fig. 4) and mass spectrometry results (Fig. S7 and Table S1). These data provide additional information on the mechanism by which NFR1 inhibits the proteolytic activity of NopT.

We expanded the discussion on the cell death response induced by ectopic expression of NFR1 and NFR5 in Nicotiana benthamiana. We also included further details from Madsen et al. (2011) to contextualize our findings within the known literature.

We believe that these additions and clarifications have improved the significance and impact of our study.

The authors present evidence supporting the interaction of NopT with NFR1 and NFR5. In particular, there is solid support for cleavage of NFR5 by NopT (Figure 3) and the identification of NopT phosphorylation sites that inhibit its proteolytic activity (Figure 4C). Cleavage of NFR5 upon expression in N. benthamiana (Figure 3A) requires appropriate controls (inactive mutant versions) that have been provided, since Agrobacterium as a closely rhizobia-related bacterium, might increase defense related proteolytic activity in the plant host cells.

We appreciate your recognition of the importance of appropriate controls in our experimental design. In response to your comments, we revised our manuscript to ensure that the figures and legends provide a clear description of the controls used. We also included a more detailed description of our experimental design at several places. In particular, we have highlighted the use of the protease-dead version of NopT as a control (NopT^C93S). Therefore, NFR5-GFP cleavage in N. benthamiana clearly depended on protease activity of NopT and not on Agrobacterium (Fig. 3A). In the revised text, we are now more cautious in our wording and don’t conclude at this stage that NopT proteolyzes NFR5. However, our subsequent experiments, including in vitro experiments, clearly show that NopT is able to proteolyze NFR5.

We are convinced that these changes have improved the quality of our work.

Key results from N. benthamiana appear consistent with data from recombinant protein expression in bacteria. For the analysis in the host legume L. japonicus transgenic hairy roots were included. To demonstrate that the cleavage of NFR5 occurs during the interaction in plant cells the authors build largely on western blots. Regardless of whether Nicotiana leaf cells or Lotus root cells are used as the test platform, the Western blots indicate that only a small proportion of NFR5 is cleaved when co-expressed with nopT, and most of the NFR5 persists in its full-length form (Figures 3A-D). It is not quite clear how the authors explain the loss of NFR5 function (loss of cell death, impact on symbiosis), as a vast excess of the tested target remains intact. It is also not clear why a large proportion of NFR5 is unaffected by the proteolytic activity of NopT. This is particularly interesting in Nicotiana in the absence of Nod factor that could trigger NFR1 kinase activity.

Thank you for your comments regarding the cleavage of NFR5 by NopT and its functional implications. We acknowledge that our immunoblots indicate only a relatively small proportion of  the NFR5 cleavage product.  Possible explanations could be as follows:

(1) The presence of full-length NFR5 does not preclude a significant impact of NopT on function of NFR5, as NopT is able to bind to NFR5. In other words, the NopT-NFR5 and NopT-NFR1 interactions at the plasmamembrane might influence the function of the NFR1/NFR5 receptor without proteolytic cleavage of NFR5. In fact, protease-dead NopT^C93S expressed in NGR234Δ_nopT_ showed certain effects in L. japonicus (less infection foci were formed compared to NGR234Δ_nopT_ Fig. 5E).  In this context, it is worth mentioning that the non-acylated NopT^C93S (Fig. 1B) and not_USDA257 (Fig. 6B) proteins were unable to suppress NFR1/NFR5-induced cell death in N. benthamina, but this could be explained by the lack of acylation and altered subcellular localization.

(2) The cleaved NFR5 fraction, although small, may be sufficient to disrupt signaling pathways, leading to the observed phenotypic changes  (loss of cell death in N. benthamiana; altered infection in L. japonicus).

(3) The used expression systems produce high levels of proteins in the cell. This may not reflect the natural situation in L. japonicus cells.

(4) Cellular conditions could impair cleavage of NFR5 by NopT.  Expression of proteins in E. coli may partially result in formation of protein aggregates (inactive NopT; NFR5 resistant to proteolysis).

(5) In N. benthamiana co-expressing NFR1/NFR5, the NFR1 kinase activity is constitutively active (i.e., does not require Nod factors), suggesting an altered protein conformation of the receptor complex, which may influence the proteolytic susceptibility of NFR5.

(6) The proteolytic activity of NopT may be reduced by the interaction of NopT with other proteins such as NFR1, which phosphorylates NopT and inactivates its protease activity.

In our revised manuscript version, we provide now quantitative data for the efficiency of NFR5 cleavage by NopT in different expression systems used (Supplemental Fig.  14).  We have also improved our Discussion in this context. Future research will be necessary to better understand loss of NFR5 function by NopT. 

It is also difficult to evaluate how the ratios of cleaved and full-length protein change when different versions of NopT are present without a quantification of band strengths normalized to loading controls (Figure 3C, 3D, 3F). The same is true for the blots supporting NFR1 phosphorylation of NopT (Figure 4A).

Thank you for pointing out this. Following your suggestions, we quantified the band intensities for cleaved and full-length NFR5 in our different expression systems (N. benthamiana, L. japonicus and E. coli). The protein bands were normalized to loading controls. The data are shown in the new Supplemental Fig. 14. Similarly, the bands of immunoblots supporting phosphorylation of NopT by NFR1 were quantified. The data on band intensities are shown in Fig.  4B of our revised manuscript. These improvements provide a clearer understanding of how the ratios of cleaved to full-length proteins change in different protein expression systems, and to which extent NopT was phosphorylated by NFR1.

Nodule primordia and infection threads are still formed when L. japonicus plants are inoculated with ∆nopT mutant bacteria, but it is not clear if these primordia are infected or develop into fully functional nodules (Figure 5). A quantification of the ratio of infected and non-infected nodules and primordia would reveal whether NopT is only active at the transition from infection focus to thread or perhaps also later in the bacterial infection process of the developing root nodule.

Thank you for highlighting this aspect of our study. In response to your comment, we have conducted additional inoculation experiments with L. japonicus plants inoculated with NGR234 and NGR234_ΔnopT_ mutant. The new data are shown in Fig 5A, 5E, and 5G. However, we could not find any uninfected nodules (empty) nodules when roots were inoculated with these strains and mention this observation in the Results section of our revised manuscript.

Reviewer #2 (Public Review):

Summary:

This manuscript presents data demonstrating NopT's interaction with Nod Factor Receptors NFR1 and NFR5 and its impact on cell death inhibition and rhizobial infection. The identification of a truncated NopT variant in certain Sinorhizobium species adds an interesting dimension to the study. These data try to bridge the gaps between classical Nod-factor-dependent nodulation and T3SS NopT effector-dependent nodulation in legume-rhizobium symbiosis. Overall, the research provides interesting insights into the molecular mechanisms underlying symbiotic interactions between rhizobia and legumes.

Strengths:

The manuscript nicely demonstrates NopT's proteolytic cleavage of NFR5, regulated by NFR1 phosphorylation, promoting rhizobial infection in L. japonicus. Intriguingly, authors also identify a truncated NopT variant in certain Sinorhizobium species, maintaining NFR5 cleavage but lacking NFR1 interaction. These findings bridge the T3SS effector with the classical Nod-factor-dependent nodulation pathway, offering novel insights into symbiotic interactions.

Weaknesses:

(1) In the previous study, when transiently expressed NopT alone in Nicotiana tobacco plants, proteolytically active NopT elicited a rapid hypersensitive reaction. However, this phenotype was not observed when expressing the same NopT in Nicotiana benthamiana (Figure 1A). Conversely, cell death and a hypersensitive reaction were observed in Figure S8. This raises questions about the suitability of the exogenous expression system for studying NopT proteolysis specificity.

We appreciate your attention to these plant-specific differences. Previous studies showed that NopT expressed in tobacco (N. tabacum) or in specific Arabidopsis ecotypes (with PBS1/RPS5 genes) causes rapid cell death (Dai et al. 2008; Khan et al. 2022). Khan et al. 2022 reported recently that cell death does not occur in N. benthamiana unless the leaves were transformed with PBS1/RPS5 constructs. Our data shown in Fig. S15 confirm these findings. As cell death (effector triggered immunity) is usually associated with induction of plant protease activities, we considered N. tabacum and A. thaliana plants as not suitable for testing NFR5 cleavage by NopT. In fact, no NopT/NFR5 experiments were not performed with these plants in our study.  In response to your comment, we now better describe the N. benthamiana expression system and cite the previous articles_. Furthermore,  We have revised the Discussion section to better emphasize effector-induced immunity in non-host plants and the negative effect of rhizobial effectors during symbiosis. Our revisions certainly provide a clearer understanding of the advantages and limitations of the _N.  benthamiana expression system.

(2) NFR5 Loss-of-function mutants do not produce nodules in the presence of rhizobia in lotus roots, and overexpression of NFR1 and NFR5 produces spontaneous nodules. In this regard, if the direct proteolysis target of NopT is NFR5, one could expect the NGR234's infection will not be very successful because of the Native NopT's specific proteolysis function of NFR5 and NFR1. Conversely, in Figure 5, authors observed the different results.

Thank you for this comment, which points out that we did not address this aspect precisely enough in the original manuscript version.  We improved our manuscript and now write that nfr1 and nfr5 mutants do not produce nodules (Madsen et al., 2003; Radutoiu et al., 2003) and that over-expression of either NFR1 or NFR5 can activate NF signaling, resulting in formation of spontaneous nodules in the absence of rhizobia (Ried et al., 2014). In fact, compared to the nopT knockout mutant NGR234_ΔnopT_, wildtype NGR234 (with NopT) is less successful in inducing infection foci in root hairs of L. japonicus (Fig. 5). With respect to formation of nodule primordia, we repeated our inoculation experiments with NGR234_ΔnopT_ and wildtype NGR234 and also included a nopT over-expressing NGR234 strain into the analysis. Our data clearly showed that nodule primordium formation was negatively affected by NopT. The new data are shown in Fig. 5 of our revised version. Our data show that NGR234's infection is not really successful, especially when NopT is over-expressed. This is consistent  with our observations that NopT targets Nod factor receptors in L. japonicus and inhibits NF signaling (NIN promoter-GUS experiments). Our findings indicate that NopT is an “Avr effector” for L. japonicus.  However, in other host plants of NGR234, NopT possesses a symbiosis-promoting role (Dai et al. 2008; Kambara et al. 2009). Such differences could be explained by different NopT targets in different plants (in addition to Nod factor receptors), which may influence the outcome of the infection process. Indeed, our work shows hat NopT can interact with various kinase-dead LysM domain receptors, suggesting a role of NopT in suppression or activation of plant immunity responses depending on the host plant. We discuss such alternative mechanisms in our revised manuscript version and emphasize the need for further investigation to elucidate the precise mechanisms underlying the observed infection phenotype and the role of NopT in modulating symbiotic signaling pathways. In this context, we would also like to mention the two new figures of our manuscript which are showing (i) the efficiency of NFR5 cleavage by NopT in different expression systems, (ii) the interaction between NopT^C93S and His-SUMO-NFR5^JM-GFP, and (iii) cleavage of His-SUMO-NFP^JM-GFP by NopT (Supplementary Figs. S8 and S9).

(3) In Figure 6E, the model illustrates how NopT digests NFR5 to regulate rhizobia infection. However, it raises the question of whether it is reasonable for NGR234 to produce an effector that restricts its own colonization in host plants.

Thank you for mentioning this point. We are aware of the possible paradox that the broad-host-range strain NGR234 produces an effector that appears to restrict its infection of host plants. As mentioned in our answer to the previous comment, NopT could have additional functions beyond the regulation of Nod factor signaling. In our revised manuscript version, we have modified our text as follows:

(1) We mention the potential evolutionary aspects of NopT-mediated regulation of rhizobial infection and discuss the possibility that interactions between NopT and Nod factor receptors may have evolved to fine-tune Nod factor signaling to avoid rhizobial hyperinfection in certain host legumes.

(2) We also emphasize that the presence of NopT may confer selective advantages in other host plants than L. japonicus due to interactions with proteins related to plant immunity. Like other effectors, NopT could suppress activation of immune responses (suppression of PTI) or cause effector-triggered immunity (ETI) responses, thereby modulating rhizobial infection and nodule formation. Interactions between NopT and proteins related to the plant immune system may represent an important evolutionary driving force for host-specific nodulation and explain why the presence of NopT in NGR234 has a negative effect on symbiosis with L. japonicus but a positive one with other legumes.

(4) The failure to generate stable transgenic plants expressing NopT in Lotus japonicus is surprising, considering the manuscript's claim that NopT specifically proteolyzes NFR5, a major player in the response to nodule symbiosis, without being essential for plant development.

We also thank for this comment. We have revised the Discussion section of our manuscript and discuss now our failure to generate stable transgenic L. japonicus plants expressing NopT. We observed that the protease activity of NopT in aerial parts of L. japonicus had a negative effect on plant development, whereas NopT expression in hairy roots was possible. Such differences may be explained by different NopT substrates in roots and aerial parts of the plant. In this context, we also discuss our finding that NopT not only cleaves NFR5 but is also able to proteolyze other proteins of L. japonicus such as LjLYS11, suggesting that NopT not only suppresses Nod factor signaling, but may also interfere with signal transduction pathways related to plant immunity. We speculate that, depending on the host legume species, NopT could suppress PTI or induce ETI, thereby modulating rhizobial infection and nodule formation.

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors):

Overall the text and figure legends must be double-checked for correctness of scientific statements. The few listed here are just examples. There are more that are potentially damaging the perception by the readers and thus the value of the manuscript.

The nopT mutant leads to more infections. In line 358 the statement: "...and the proteolysis of NFR5 are important for rhizobial infection", is wrong, as the infection works even better without it. It is, according to my interpretation of the results, important for the regulation of infection. Sounds a small difference, but it completely changes the meaning.

We appreciate your thorough review and have taken the opportunity to correct this error. Following your suggestions, we carefully rephrased the whole text and figure legends to ensure that the scientific statements accurately reflect the findings of our study. We are convinced that these changed have increased the value of this study.

In line 905 the authors state that NopTC indicates the truncated version of NopT after autocleavage by releasing about 50 a.a. at its N-terminus.

They do not analyse this cleavage product to support this claim. So better rephrase.

According to Dai et al. (2008), NopT expressed in E. coli is autocleaved. The N-terminal sequence GCCA obtained by Edman sequencing suggests that NopT was cleaved between M49 and G50.  We improved our manuscript and now write:

(1) “A previous study has shown that NopT is autocleaved at its N-terminus to form a processed protein that lacks the first 49 amino acid residues (Dai et al., 2008)”

(2) “However, NopT^ΔN50, which is similar to autocleaved NopT, retained the ability to interact with NFR5 but not with NFR1 (Fig. S2D).”.

In line 967: "Both NopT and NopTC after autocleavage exert proteolytic activities" This is confusing as it was suggested earlier that NopTc is a product of the autocleavage. There is no indication of another round of NopTc autocleavage or did I miss something?

Thank you for bringing this inaccuracy to our attention. There is no second round of NopT autocleavage. We have corrected the text and write: “NopT and not^C (autocleaved NopT) proteolytically cleave NFR5 at the juxtamembrane domain to release the intracellular domain of NFR5”

Given the amount of work that went into the research, the presentation of the figures should be considerably improved. For example, in Figure 3F the mutant is not correctly annotated. In figure 5 the term infection foci and IT occur but it is not explained in the legend what these are, where they can be seen in the figure and how the researchers discriminated between the two events.

In general, the labeling of the figure panels should be improved to facilitate the understanding. For example, in Figure 3 the panels switch between different host plant systems. The plant could be clarified for each panel to aid the reader. The asterisks are not in line with the signal that is supposed to be marked. And so on. I strongly advise to improve the figures.

Thank you for your valuable suggestions. We acknowledge the importance of clear and informative figure presentation to enhance the understanding of our research findings. In response to your comments, we made a comprehensive revision of the figures to address the mentioned issues:

(1) We corrected annotations of the mutant in Figure 3F to accurately represent the experimental conditions.

(2) We revised the legend of Figure 5 and provide clear explanations of the terms "infection foci" and "IT" (infection threads) in the Methods section.

(3) We improved the labeling of figure panels and improved the writing of the figure legend specifying the protein expression system (N. benthamiana, L. japonicus and E. coli, respectively). . We ensured that the asterisks indicating statistically significant results are properly aligned.

Furthermore, we carefully reviewed each figure to enhance clarity and readability, including optimizing font size and line thickness. Captions and annotations were also revised.

Figure 1

• To verify that the lack of observed cell death is not linked to differential expression levels, an expression control Western blot is essential. In the expression control Western blot given in the supplemental materials (Supplemental fig. 1E), NFR5 is not visible in the first lane.

We appreciate your comments on the control immunoblot which were made to verify the presence of NFR1, NFR5 and NopT in N. benthamiana.  However, as shown in Supplemental Fig. 1E, the intact NFR5 could not be immuno-detected when co-expressed with NFR1 and NopT. To ensure co-expression of NFR1/NFR5, A. tumefaciens carrying a binary vector with both NFR1 and NFR5 was used. In the revised version, we modified the figure legend accordingly and also included a detailed description of the procedure at lines 165-166

• Labeling of NFR1/LjNFR1 should be kept consistent between the text and the figures. Currently, the text refers to both NFR1 and LjNFR1 and figures are labelled NFR1. The same is true for NFR5.

Thank you for pointing out this inconsistency. We revised our manuscript and use now consistently NFR1 and NFR5 without a prefix to avoid any confusions.

• A clearer description of how cell death was determined would be useful. In the selected pictures in panel D, leaves coexpressing nopT with Bax1 or Cerk1 appear very different from the pictures selected for NopM and AVr3a/R3a.

We agree that a clearer description of our cell death experiments with N. benthamiana was necessary. We have re-worded the figure legend to provide more detailed information on the criteria used for assessing cell death. Additionally, we show now our images at higher resolution.

• In panel D, the "Death/Total" ratio is only shown for leaf discs where nopT was coexpressed with the cell-death triggering proteins. Including the ratio for leaf discs where only the cell-death triggering protein (without nopT ) was expressed would make the figure more clear.

Thank you for this suggestion. To provide a more comprehensive comparison, we included the "Cell death/Total" ratio for all leaf disc images shown in Fig. 1D. 

Figure 2:

• A: Split-YFP is not ideal as evidence for colocalization because of the chemical bond formed between the YFP fragments that may lead to artificial trapping/accumulation outside the main expression domains. Overall, the authors should revise if this figure aims to show colocalization or interaction. In the current text, both terms are used, but these are different interpretations.

We appreciate your concern regarding the use of Split-YFP for colocalization analysis. We carefully reviewed the figure and corresponding text to ensure clarity in the interpretation of the results. The primary aim of this figure was to explore protein-protein interactions rather than strict colocalization. Protein-protein interactions have also been validated by other experiments of our work. We have revised the text accordingly and no longer emphasize on “co-localization”.

• Given the focus on proteolytic activity in this paper, all blots need to be clearly labeled with size markers, and it would be good to include a supplemental figure with all other bands produced in the Western blot, regardless of their size. Without this, the results in panel 2D seem inconsistent with results presented in figure 3A, since NFR5 does not appear to be cleaved in the Western blot in 2D, but 3A shows cleavage when the same proteins (with different tags) are coexpressed in the same system.

Thank you for bringing up this point. We ensured that all immunoblots are clearly labeled with size markers in our revised manuscript. We also carefully checked the consistency of the results presented in Figures 2D and Figure 3A and included appropriate clarifications in the revised manuscript. In Figure 2D, we show the bands at around 75 kD  (multi-bands would be detected below, including cleaved NFR5 by NopT, but also other non-specific bands).

Figure 3:

• In panel E, NopTC93S cannot cleave His-Sumo-NFR5JM-GFP, but it would be interesting to also show if NopTC93S can bind the NFR5JM fragment. It would also be useful to see this experiment done with the JM of NFP.

Thank you for the suggestion. We agree that investigating the binding of NopT^C93S to the NFR5^JM fragment provides valuable insights into the interaction between NopT and NFR5. In our revised version, we show in the new Supplemental Fig. S4 that NopT interacts with NFR5JM and cleaves NFP^JM. The Results section has been modified accordingly.

• The panels in this figure require better labeling. In many panels, asterisks are misplaced relative to the bands they should highlight, and not all blots have size markers or loading controls.

Thank you for bringing this to our attention. We carefully reviewed the labeling of all panels in Figure 3 to ensure accuracy and clarity. We ensured that asterisks are correctly placed in the figures. We also included size markers and loading controls to improve the quality of the shown immunoblots.

• Since there is no clear evidence in this figure that the smear in the blot in panel C is phosphorylated NopT, it is recommended to provide a less interpretative label on the blot, and explain the label in the text.

We appreciate your suggestion regarding the labeling of the blot in panel C of Fig. 3. We revised the label and provided a less interpretative designation in Fig. 3C. We also rephrased the figure legend and the text in the Results section as recommended.

Figure 4

• In B, a brief introduction in the text to the function of the Zn-phostag would make the figure easier to understand for more readers.

Thank you for the suggestion. We agree and have provided a brief explanation in the Results section: “On such gels, a Zn²⁺-Phos-tag bound phosphorylated protein migrates slower than its unbound nonphosphorylated form. Furthermore, we have included the reference (Kato & Sakamoto, 2019) into the Methods section.

Figure 5:

• Change "Scar bar" to "Scale bar" in the figure captions

Thank you for spotting that typo. We have corrected it.

• Correct the references to the figures in the text

We carefully reviewed the Figure 5 and made corresponding corrections to improve the quality of our manuscript Please check line 394-451.

• It should be clarified what was quantified as "infection foci" (C, F, G)

We revised the legend of Figure 5 and provide now explanations of the terms "infection foci" and "IT" (infection threads) in the Methods section.  Please check line 399-451.

• It is recommended to use pictures that are from the same region of the plant root (the susceptible zone). The pictures in panel A appear to be from different regions, since the density of root hairs is different.

Thank you for bringing this to our attention. We ensured that the images selected for panel A were from the same region of the plant root to guarantee consistency and accuracy of the comparison.

• Panel G should be labeled so it is clearer that nopT is being expressed in L. japonicus transgenic roots.

We have labeled this panel more clearly to help the reader understand that nopT was expressed in transgenic L. japonicus roots.

• Panel F is missing statistical tests for ITs

We apologize and have included the results of our statistical tests for ITs.

Figure 6:

• The model presented in panel E misrepresents the role of NFR5 according to the results in the paper. From the evidence presented, it is not clear if the observed rhizobial infection phenotype is due to reduced abundance of full-length NFR5, or if the cleaved NFR5 fragment is suppressing infection. Additionally, S. fredii should not be drawn so close to the plasma membrane, since the bacteria are located outside the cell wall when the T3SS is active.

We appreciate your comment which helps us to improve the interpretation of our results. We agree that the model should accurately reflect the uncertainties regarding the role of NFR5. We revised the model (positioning of S. fredii etc.) and write in the Discussion:

“NopT impairs the function of the NFR1/NFR5 receptor complex. Cleavage of NFR5 by NopT reduces its protein levels. Possible inhibitory effects of NFR5 cleavage products on NF signaling are unknown but cannot be excluded.”

Reviewer #2 (Recommendations For The Authors):

(1) Some minor weaknesses need addressing: In Figure 5A, the root hair density in the two images appears significantly different. Are these images representative of each treatment?

We appreciate your attention to detail and the importance of ensuring that the images in Figure 5A are representative. We carefully reviewed our image selection process and confirm that the shown images are indeed representative of each treatment group. In our revised version, we show additional images and also improved the text in the figure legend. Furthermore, we performed additional GUS staining tests and the new data are shown in Fig 5A abd 5B.

(2) Additionally, please ensure consistency in the format of genotype names throughout the manuscript. For instance, in Line 897, "Italy" should be used in place of "N. benthamiana."

We thank you for pointing out the format of genotype names and corrected our manuscript as requested.

eLife Assessment

Given a great need for novel human model systems to study small cell lung cancer (SCLC), the authors describe an important pre-clinical model with broad potential for the study of how genetic perturbations or drug treatments alter SCLC tumor growth, metastasis, and response to therapy. For the major finding, the authors provide convincing evidence that RB/TP53 suppression coupled with MYC overexpression in an ES cell-derived model system results in aggressive and metastatic SCLC. However, the impact of the work would have been increased with the inclusion of a broader set of genetic perturbations, such as over-expression of MYCL, to better model major SCLC phenotypes. The new model described will be of significant interest to researchers studying lung cancer.

Reviewer #1 (Public review):

Summary:

The authors introduced their previous paper with the concise statement that "the relationships between lineage-specific attributes and genotypic differences of tumors are not understood" (Chen et al., JEM 2019, PMID: 30737256). For example, it is not clear why combined loss of RB1 and TP53 is required for tumorigenesis in SCLC or other aggressive neuroendocrine (NE) cancers, or why the oncogenic mutations in KRAS or EGFR that drive NSCLC tumorigenesis are found so infrequently in SCLC. This is the main question addressed by the previous and current papers.

One approach to this question is to identify a discrete set of genetic/biochemical manipulations that are sufficient to transform non-malignant human cells into SCLC-like tumors. One group reported transformation of primary human bronchial epithelial cells into NE tumors through a complex lentiviral cocktail involving inactivation of pRB and p53 and activation of AKT, cMYC and BCL2 (PARCB) (Park et al., Science 2018, PMID: 30287662). The cocktail previously reported by Chen and colleagues to transform human pluripotent stem-cell (hPSC)-derived lung progenitors (LPs) into NE xenografts was more concise: DAPT to inactivate NOTCH signaling combined with shRNAs against RB1 and TP53. However, the resulting RP xenografts lacked important characteristics of SCLC. Unlike SCLC, these tumors proliferated slowly and did not metastasize, and although small subpopulations expressed MYC or MYCL, none expressed NEUROD1.

MYC is frequently amplified or expressed at high levels in SCLC, and here, the authors have tested whether inducible expression of MYC could increase the resemblance of their hPSC-derived NE tumors to SCLC. These RPM cells (or RPM T58A with stabilized cMYC) engrafted more consistently and grew more rapidly than RP cells, and unlike RP cells, formed liver metastases when injected into the renal capsule. Gene expression analyses reveled that RPM tumor subpopulations expressed NEUROD1, ASCL1 and/or YAP1.

The hPSC-derived RPM model is a major advance over the previous RP model. This may become a powerful tool for understanding SCLC tumorigenesis and progression and for discovering gene dependencies and molecular targets for novel therapies. However, the specific role of cMYC in this model needs to be clarified.

Recommended Revision:

cMYC can drive proliferation, tumorigenesis or apoptosis in a variety of lineages depending on concurrent mutations. For example, in the Park et al., study, normal human prostate cells could be reprogrammed to form adenocarcinoma-like tumors by activation of cMYC and AKT alone, without manipulation of TP53 or RB1. In their previous manuscript, the authors carefully showed the role of each molecular manipulation in NE tumorigenesis. DAPT was required for NE differentiation of LPs to PNECs, shRB1 was required for expansion of the PNECs, and shTP53 was required for xenograft formation. cMYC expression could influence each of these steps, and importantly, could render some steps dispensable. For example, shRB1 was previously necessary to expand the DAPT-induced PNECs, as neither shTP53 nor activation of KRAS or EGFR had no effect on this population, but perhaps cMYC overexpression could expand PNECs even in the presence of pRB, or even induce LPs to become PNECs without DAPT. Similarly, both shRB1 and shTP53 were necessary for xenograft formation, but maybe not if cMYC is overexpressed. If a molecular hallmark of SCLC, such as loss of RB1 or TP53, has become dispensable with the addition of cMYC, this information is critically important in interpreting this as a model of SCLC tumorigenesis.

To interpret the role of cMYC expression in hPSC-derived RPM tumors, we need to know what this manipulation does without manipulation of pRB, p53 or NOTCH, alone or in combination. There are 7 relevant combinations that should be presented in this manuscript: (1) cMYC alone in LPs, (2) cMYC + DAPT, (3) cMYC + shRB1, (4) cMYC + DAPT + shRB1, (5) cMYC + shTP53, (6) cMYC + DAPT + shTP53, and (7) cMYC + shRB1 + shTP53. Wild-type cMYC is sufficient; further exploration with the T58A mutant would not be necessary.

Please present the effects of these combinations on LP differentiation to PNECs, expansion of PNECs as well as other lung cells, xenograft formation and histology, and xenograft growth rate and capacity for metastasis. If this could be clarified experimentally, and the results discussed in the context of other similar approaches such as the Park et al., paper, this study would be a major addition to the field.

Reviewer #3 (Public review):

This revision and the accompanying rebuttal indicates the authors want to publish their studies without providing several of the reviewer requested additional experiments (such as determining the impact of other Myc family members on metastatic behavior and expression characteristics compared to overexpression of c-Myc), and determining whether the tumors were responsive or not to standard clinically used therapies. Their argument is the author team has moved on to other endeavors, it is important to communicate their findings to the research field, and they have indicated these issues in the Discussion. All of these things are reasonable. However, there two things that would help. The first is to have the authors clearly state in the Discussion section "Limitations of the current study" and then list these out. In the current format the indication that the authors recognize the "limitations" is not clearly stated. An example - of such a limitation is how well their model now provides a human SCLC like tumor that metastasizes. We know that in patients SCLC is widely metastatic, but in SCLC patient derived xenografts with subcutaneous injection that is not seen, so if their model now generated widely metastatic behavior like that seen in patients, this report and the associated resources would be a significant advance to the field. However, their data shows that using their model the subcutaneous tumors don't metastasize, and even with renal capsule models metastases are not common and do not go to important sites (e.g. brain). Second, a major reason for publishing this paper is that their model system would be available as a resource for the field to study. However, I could not find in the paper or the Methods section any statement as to the availability of this presumable important resource. If the resources will not be easily available in a format that others can readily study (e.g. with instructions on how to handle the cells which would seem to be more complicated than other patient derived SCLC models) then of course the value of this paper to the field as a whole is dramatically reduced. I would assume the authors want their model to be used by other investigators and thus a clear statement of model availability and how to routinely handle their model is important to include in their manuscript.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review): 

Summary: 

The authors introduced their previous paper with the concise statement that "the relationships between lineage-specific attributes and genotypic differences of tumors are not understood" (Chen et al., JEM 2019, PMID: 30737256). For example, it is not clear why combined loss of RB1 and TP53 is required for tumorigenesis in SCLC or other aggressive neuroendocrine (NE) cancers, or why the oncogenic mutations in KRAS or EGFR that drive NSCLC tumorigenesis are found so infrequently in SCLC. This is the main question addressed by the previous and current papers. 

One approach to this question is to identify a discrete set of genetic/biochemical manipulations that are sufficient to transform non-malignant human cells into SCLC-like tumors. One group reported the transformation of primary human bronchial epithelial cells into NE tumors through a complex lentiviral cocktail involving the inactivation of pRB and p53 and activation of AKT, cMYC, and BCL2 (PARCB) (Park et al., Science 2018, PMID: 30287662). The cocktail previously reported by Chen and colleagues to transform human pluripotent stem-cell (hPSC)-derived lung progenitors (LPs) into NE xenografts was more concise: DAPT to inactivate NOTCH signaling combined with shRNAs against RB1 and TP53. However, the resulting RP xenografts lacked important characteristics of SCLC. Unlike SCLC, these tumors proliferated slowly and did not metastasize, and although small subpopulations expressed MYC or MYCL, none expressed NEUROD1. 

MYC is frequently amplified or expressed at high levels in SCLC, and here, the authors have tested whether inducible expression of MYC could increase the resemblance of their hPSC-derived NE tumors to SCLC. These RPM cells (or RPM T58A with stabilized cMYC) engrafted more consistently and grew more rapidly than RP cells, and unlike RP cells, formed liver metastases when injected into the renal capsule. Gene expression analyses revealed that RPM tumor subpopulations expressed NEUROD1, ASCL1, and/or YAP1. 

The hPSC-derived RPM model is a major advance over the previous RP model. This may become a powerful tool for understanding SCLC tumorigenesis and progression and for discovering gene dependencies and molecular targets for novel therapies. However, the specific role of cMYC in this model needs to be clarified. 

cMYC can drive proliferation, tumorigenesis, or apoptosis in a variety of lineages depending on concurrent mutations. For example, in the Park et al., study, normal human prostate cells could be reprogrammed to form adenocarcinoma-like tumors by activation of cMYC and AKT alone, without manipulation of TP53 or RB1. In their previous manuscript, the authors carefully showed the role of each molecular manipulation in NE tumorigenesis. DAPT was required for NE differentiation of LPs to PNECs, shRB1 was required for expansion of the PNECs, and shTP53 was required for xenograft formation. cMYC expression could influence each of these steps, and importantly, could render some steps dispensable. For example, shRB1 was previously necessary to expand the DAPT-induced PNECs, as neither shTP53 nor activation of KRAS or EGFR had no effect on this population, but perhaps cMYC overexpression could expand PNECs even in the presence of pRB, or even induce LPs to become PNECs without DAPT. Similarly, both shRB1 and shTP53 were necessary for xenograft formation, but maybe not if cMYC is overexpressed. If a molecular hallmark of SCLC, such as loss of RB1 or TP53, has become dispensable with the addition of cMYC, this information is critically important in interpreting this as a model of SCLC tumorigenesis.  

The reviewer’s suggestion may be possible; indeed, in a recent report from our group (Gardner EE, et al., Science 2024) we have shown, using genetically engineered mouse modeling coupled with lineage tracing, that the cMyc oncogene can selectively expand Ascl1+ PNECs in the lung.

We agree with the reviewer that not having a better understanding of the individual components necessary and/or sufficient to transform hESC-derived LPs is an important shortcoming of this current work. However, we would like to stress three important points about the comments:  1) tumors were reviewed and the histological diagnoses were certified by a practicing pulmonary pathologist at WCM (our co-author, C. Zhang); 2 )the observed  transcriptional programs were consistent with primary human SCLC; and 3) RB1-proficient SCLC is now recognized as a rare presentation of SCLC (Febrese-Aldana CA, et al., Clin. Can. Res. 2022. PMID: 35792876).

To interpret the role of cMYC expression in hPSC-derived RPM tumors, we need to know what this manipulation does without manipulation of pRB, p53, or NOTCH, alone or in combination. Seven relevant combinations should be presented in this manuscript: (1) cMYC alone in LPs, (2) cMYC + DAPT, (3) cMYC + shRB1, (4) cMYC + DAPT + shRB1, (5) cMYC + shTP53, (6) cMYC + DAPT + shTP53, and (7) cMYC + shRB1 + shTP53. Wildtype cMYC is sufficient; further exploration with the T58A mutant would not be necessary. 

We respectfully disagree that an interrogation of the differences between the phenotypes produced by wildtype and Myc(T58A) would not be informative. (Our view is confirmed by the second reviewer; see below.)    It is well established that Myc gene or protein dosage can have profound effects on in vivo phenotypes (Murphy DJ, et al., Cancer Cell 2008. PMID: 19061836). The “RPM” model of variant SCLC developed by Trudy Oliver’s lab relied on the conditional T58A point mutant of cMyc, originally made by Rob Wechsler-Reya. While we do not discuss the differences between Myc and Myc(T58A), it is nonetheless important to present our results with both the WT and mutant MYC constructs, as we are aware of others actively investigating differences between them in GEMM models of SCLC tumor development.

We agree with the reviewer about the virtues of trying to identify the effects of individual gene manipulations; indeed our original paper (Chen et al., J. Expt. Med. 2019), describing the RUES2derived model of SCLC did just that, carefully dissecting events required to transform LPs towards a SCLC-like state. The central  purpose of the current study was to determine the effects of adding cMyc on the behavior of weakly tumorigenic SCLC-like cells cMyc.  Presenting data with these two alleles to seek effects of different doses of MYC protein seems reasonable.

This reviewer considers that there should be a presentation of the effects of these combinations on LP differentiation to PNECs, expansion of PNECs as well as other lung cells, xenograft formation and histology, and xenograft growth rate and capacity for metastasis. If this could be clarified experimentally, and the results discussed in the context of other similar approaches such as the Park et al., paper, this study would be a major addition to the field.  

Reviewer #2 (Public Review): 

Summary: 

Chen et al use human embryonic stem cells (ESCs) to determine the impact of wildtype MYC and a point mutant stable form of MYC (MYC-T58A) in the transformation of induced pulmonary neuroendocrine cells (PNEC) in the context of RB1/P53 (RP) loss (tumor suppressors that are nearly universally lost in small cell lung cancer (SCLC)). Upon transplant into immune-deficient mice, they find that RP-MYC and RP-MYC-T58A cells grow more rapidly, and are more likely to be metastatic when transplanted into the kidney capsule, than RP controls. Through single-cell RNA sequencing and immunostaining approaches, they find that these RPM tumors and their metastases express NEUROD1, which is a transcription factor whose expression marks a distinct molecular state of SCLC. While MYC is already known to promote aggressive NEUROD1+ SCLC in other models, these data demonstrate its capacity in a human setting that provides a rationale for further use of the ESC-based model going forward. Overall, these findings provide a minor advance over the previous characterization of this ESC-based model of SCLC published in Chen et al, J Exp Med, 2019. 

We consider the findings more than a “minor” advance in the development of the model, since any useful model for SCLC would need to form aggressive and metastatic tumors.

The major conclusion of the paper is generally well supported, but some minor conclusions are inadequate and require important controls and more careful analysis. 

Strengths:

(1) Both MYC and MYC-T58A yield similar results when RP-MYC and RP-MYCT58A PNEC ESCs are injected subcutaneously, or into the renal capsule, of immune-deficient mice, leading to the conclusion that MYC promotes faster growth and more metastases than RP controls. 

(2) Consistent with numerous prior studies in mice with a neuroendocrine (NE) cell of origin (Mollaoglu et al, Cancer Cell, 2017; Ireland et al, Cancer Cell, 2020; Olsen et al, Genes Dev, 2021), MYC appears sufficient in the context of RB/P53 loss to induce the NEUROD1 state. Prior studies also show that MYC can convert human ASCL1+ neuroendocrine SCLC cell lines to a NEUROD1 state (Patel et al, Sci Advances, 2021); this study for the first time demonstrates that RB/P53/MYC from a human neuroendocrine cell of origin is sufficient to transform a NE state to aggressive NEUROD1+ SCLC. This finding provides a solid rationale for using the human ESC system to better understand the function of human oncogenes and tumor suppressors from a neuroendocrine origin. 

Weaknesses:

(1) There is a major concern about the conclusion that MYC "yields a larger neuroendocrine compartment" related to Figures 4C and 4G, which is inadequately supported and likely inaccurate. There is overwhelming published data that while MYC can promote NEUROD1, it also tends to correlate with reduced ASCL1 and reduced NE fate (Mollaoglu et al, Cancer Cell, 2017; Zhang et al, TLCR, 2018; Ireland et al, Cancer Cell, 2020; Patel et al, Sci Advances, 2021). Most importantly, there is a lack of in vivo RP tumor controls to make the proper comparison to judge MYC's impact on neuroendocrine identity. RPM tumors are largely neuroendocrine compared to in vitro conditions, but since RP control tumors (in vivo) are missing, it is impossible to determine whether MYC promotes more or less neuroendocrine fate than RP controls. It is not appropriate to compare RPM tumors to in vitro RP cells when it comes to cell fate. Upon inspection of the sample identity in S1B, the fibroblast and basal-like cells appear to only grow in vitro and are not well represented in vivo; it is, therefore, unclear whether these are transformed or even lack RB/P53 or express MYC. Indeed, a close inspection of Figure S1B shows that RPM tumor cells have little ASCL1 expression, consistent with lower NE fate than expected in control RP tumors. 

We would like to clarify two points related to the conclusions that we draw about MYC’s ability to promote an increase in the neuroendocrine fraction in hESC-derived cultures:  1) The comparisons in Figures 4C were made between cells isolated in culture following the standard 50 day differentiation protocol, where, following generation of LPs around day 25, MYC was added to the other factors previously shown to enrich for a PNEC phenotype (shRB1, shTP53, and DAPT). Therefore, the argument that MYC increased the frequency of “neuroendocrine cells” (which we define by a gene expression signature) is a reasonable conclusion in the system we are using; and 2) following injection of these cells into immunocompromised mice, an ASCL1-low / NEUROD1-high presentation is noted (Supplemental Figures 1F-G). In the few metastases that we were able use to sequence bulk RNA, there is an even more pronounced increase in expression of NEUROD1 with a decrease in ASCL1.

Some confusion may have arisen from our previous characterization of neuroendocrine (NE) cells using either ASCL1 or NEUROD1 as markers. To clarify, we have now designated cells positive for ASCL1 as classical NE cells and those positive for NEUROD1 as the NE variant. According to this revised classification, our findings indicate that MYC expression leads to an increase in the NEUROD1+ NE variant and a decrease in ASCL1+ classical NE cells. This adjustment has been reflected on the results section titled, “Inoculation of the renal capsule facilitates metastasis of the RUES2-derived RPM tumors” of the manuscript.  

From the limited samples in hand, we compared the expression of ASCL1 and NEUROD1 in the weakly tumorigenic hESC RP cells after successful primary engraftment into immunocompromised mice. As expected, the RP tumors were distinguished by the lack of expression of NEUROD1, compared to levels observed in the RPM tumors.

In addition, since MYC appears to require Notch signaling to induce  NE fate (cf Ireland et al), the presence of DAPT in culture could enrich for NE fate despite MYC's presence. It's important to clarify in the legend of Fig 4A which samples are used in the scRNA-seq data and whether they were derived from in vitro or in vivo conditions (as such, Supplementary Figure S1B should be provided in the main figure). Given their conclusion is confusing and challenges robustly supported data in other models, it is critical to resolve this issue properly. I suspect when properly resolved, MYC actually consistently does reduce NE fate compared to RP controls, even though tumors are still relatively NE compared to completely distinct cellular identities such as fibroblasts.

We have clarified the source of tumor sequencing data and the platform (single cell or bulk) in Figure 4 and Supplemental Figure 1. To reiterate – the RNA sequencing results from paired metastatic and primary tumors from the RPM model are derived from bulk RNA;  the single cell RNA data in RP or RPM datasets are from cells in culture.  These distinctions are clarified in the legend to Supplemental Figure 1.

(2) The rigor of the conclusions in Figure 1 would be strengthened by comparing an equivalent number of RP animals in the renal capsule assay, which is n = 6 compared to n = 11-14 in the MYC conditions.

As we did not perform a power calculation to determine a sample size required to draw a level of statistical significance from our conclusions, this comment is not entirely accurate. Our statistical rigor was limited by the availability of samples from the RP tumor model.

(3) Statistical analysis is not provided for Figures 2A-2B, and while the results are compelling, may be strengthened by additional samples due to the variability observed. 

We acknowledge that the cohorts are relatively small but we have added statistical comparisons in Figure 2B. 

(4a) Related to Figure 3, primary tumors and liver metastases from RPM or RPM-T58A-expressing cells express NEUROD1 by immunohistochemistry (IHC) but the putative negative controls (RP) are not shown, and there is no assessment of variability from tumor to tumor, ie, this is not quantified across multiple animals. 

The results of H&E and IF staining for ASCL1, NEUROD1, CGRP, and CD56 in negative control (RP tumors) are presented in the updated Figure 3F-G.

(4b) Relatedly, MYC has been shown to be able to push cells beyond NEUROD1 to a double-negative or YAP1+ state (Mollaoglu et al, Cancer Cell, 2017; Ireland et al, Cancer Cell, 2020), but the authors do not assess subtype markers by IHC. They do show subtype markers by mRNA levels in Fig 4B, and since there is expression of ASCL1, and potentially expression of YAP1 and POU2F3, it would be valuable to examine the protein levels by IHC in control RP vs. RPM samples.

YAP1 positive SCLC is still somewhat controversial, so it is not clear what value staining for YAP1 offers beyond showing the well-established markers, ASCL1 and NEUROD1.  

(5) Given that MYC has been shown to function distinctly from MYCL in SCLC models, it would have raised the impact and value of the study if MYC was compared to MYCL or MYCL fusions in this context since generally, SCLC expresses a MYC family member. However, it is quite possible that the control RP cells do express MYCL, and as such, it would be useful to show. 

We now include Supplemental Figure S2 to illustrate four important points raised by this reviewer and others:  1) expression of MYC family members in the merged dataset (RP and RPM) is low or undetectable in the basal/fibroblast cultures; 2) MYC does have a weak correlation with EGFP in the neuroendocrine cluster when either WT MYC or T58A MYC is overexpressed; 3) MYCL and MYCN are detectable, but at low levels compared to CMYC; and 4) Expression of  ASCL1 is anticorrelated with MYC expression across the merged single cell datasets using RP and RPM models.

Reviewer #3 (Public Review): 

Summary: 

The authors continue their study of the experimental model of small cell lung cancer (SCLC) they created from human embryonic stem cells (hESCs) using a protocol for differentiating the hESCs into pulmonary lineages followed by NOTCH signaling inactivation with DAPT, and then knockdown of TP53 and RB1 (RP models) with DOX inducible shRNAs. To this published model, they now add DOX-controlled activation of expression of a MYC or T58A MYC transgenes (RPM and RPMT58A models) and study the impact of this on xenograft tumor growth and metastases. Their major findings are that the addition of MYC increased dramatically subcutaneous tumor growth and also the growth of tumors implanted into the renal capsule. In addition, they only found liver and occasional lung metastases with renal capsule implantation. Molecular studies including scRNAseq showed that tumor lines with MYC or T58A MYC led surprisingly to more neuroendocrine differentiation, and (not surprisingly) that MYC expression was most highly correlated with NEUROD1 expression. Of interest, many of the hESCs with RPM/RPMT58A expressed ASCL1. Of note, even in the renal capsule RPM/RPMT58A models only 6/12 and 4/9 mice developed metastases (mainly liver with one lung metastasis) and a few mice of each type did not even develop a renal sub capsule tumor. The authors start their Discussion by concluding: " In this report, we show that the addition of an efficiently expressed transgene encoding normal or mutant human cMYC can convert weakly tumorigenic human PNEC cells, derived from a human ESC line and depleted of tumor suppressors RB1 and TP53, into highly malignant, metastatic SCLC-like cancers after implantation into the renal capsule of immunodeficient mice.". 

Strengths: 

The in vivo study of a human preclinical model of SCLC demonstrates the important role of c-Myc in the development of a malignant phenotype and metastases. Also the role of c-Myc in selecting for expression of NEUROD1 lineage oncogene expression. 

Weaknesses: 

There are no data on results from an orthotopic (pulmonary) implantation on generation of metastases; no comparative study of other myc family members (MYCL, MYCN); no indication of analyses of other common metastatic sites found in SCLC (e.g. brain, adrenal gland, lymph nodes, bone marrow); no studies of response to standard platin-etoposide doublet chemotherapy; no data on the status of NEUROD1 and ASCL1 expression in the individual metastatic lesions they identified. 

We have acknowledged from the outset that our study has significant limitations, as noted by this reviewer, and we explained in our initial letter of response why we need to present this limited, but still consequential, story at this time. 

In particular, while we have attempted orthotopic transplantations of RPM tumor cells into NSG mice (by tail vein or intra-pulmonary injection, or intra-tracheal instillation of tumor cells), these methods were not successful in colonizing the lung. Additionally, we have compared the efficacy of platinum/etoposide to that of removing DOX in established RPM subcutaneous tumors, but we chose not to include these data as we lacked a chemotherapy responsive tumor model, and thus could not say with confidence that the chemotherapeutic agants were active and that the RPM models were truly resistant to standard SCLC chemotherapy. In a discussion about other metastatic sites, we have now included the following text: 

“In animals administered DOX, histological examinations showed that approximately half developed metastases in distant organs, including the liver or lung (Figure 1D). No metastases were observed in the bone, brain, or lymph nodes. For a more detailed assessment, future studies could employ more sensitive imaging methods, such as luciferase imaging.”

Recommendations for the authors:

Reviewer #2 (Recommendations For The Authors): 

Technical points related to Major Weakness #1: 

For Figure 4: Cells were enriched for EGFP-high cells only, under the hypothesis that cells with lower EGFP may have silenced expression of the integrated vector. Since EGFP is expressed only in the shRB1 construct, selection for high EGFP may inadvertently alter/exclude heterogeneity within the transformed population for the other transgenes (shP53, shMYC/MYC-T58A). Can authors include data to show the expression of MYC/MYC T58A in EGFP-high v -med v-low cells? MYC levels may alter the NEdifferentiation status of tumor cells. 

Please now refer to Supplemental Figure S2.

Related to the appropriateness of the methods for Figure 4C, the authors state, "We performed differential cluster abundance analysis after accounting for the fraction of cells that were EGFP+". If only EGFP+ cells were accounted for in the analysis for 4C, the majority of RP cells in the "Neuroendocrine differentiated" cluster would not be included in the analysis (according to EGFP expression in Fig S1A-B), and therefore inappropriately reduce NE identity compared to RPM samples that have higher levels of EGFP. 

There is no consideration or analysis of cell cycling/proliferation until after the conclusion is stated. Yet, increased proliferation of MYC-high vs MYC-low cultures would enhance selection for more tumors (termed "NE-diff") than non-tumors (basal/fibroblast) in 2D cultures. 

The expression of MYC itself isn't assessed for this analysis but assumed, and whether higher levels of MYC/MYC-T58A may be present in EGFP+ tumor cells that are in the NE-low populations isn't clear. Can MYC-T58A/HA also be included in the reference genome? 

We did not include an HA tag in our reference transcriptome. For [some] answers to this and other related questions, please refer to Supplemental Figure S2.

Reviewer #3 (Recommendations For The Authors): 

(1) The experiments are all technically well done and clearly presented and represent a logical extension exploring the role of c-Myc in the hESC experimental model system. 

We appreciate this supportive comment!

(2) It is of great interest that both the initial RP model only forms "benign" tumors and that with the addition of a strong oncogene like c-myc, where expression is known to be associated with a very bad prognosis in SCLC, that while one gets tumor formation there are still occasional mice both for subcutaneous and renal capsule test sites that don't get tumors even with the injection of 500,000 RPM/RPMT58A cells. In addition, of the mice that do form tumors, only ~50% exhibit metastases from the renal sub-capsule site. The authors need to comment on this further in their Discussion. To me, this illustrates both how incredibly resistant/difficult it is to form metastases, thus indicating the need for other pathways to be activated to achieve such spread, and also represents an opportunity for further functional genomic tests using their preclinical model to systematically attack this problem. Obvious candidate genes are those recently identified in genetically engineered mouse models (GEMMs) related to neuronal behavior. In addition, we already know that full-fledged patient-derived SCLC when injected subcutaneously into immune-deprived mice don't exhibit metastases - thus, while the hESC RPM result is not surprising, it indicates to me the power of their model (logs less complicated genetically than a patient SCLC) to sort through a mechanism that would allow metastases to develop from subcutaneous sites. The authors can point these things out in their Discussion section to provide a "roadmap" for future research. 

Although we remain mindful of the relatively small cohorts we have studied, the thrust of Reviewer #3’s comments is now included in the Discussion. And there is, of course, a lot more to do, and it has taken several years already to get to this point. Additional information about the prolonged gestation of this project and about the difficulties of doing more in the near future was described in our initial response to reviewers/Editor, included near the start of this letter.    

(3) I will state the obvious that this paper would be much more valuable if they had compared and contrasted at least one of the myc family members (MYCL or MYCN) with the CMYC findings whatever the results would be. Most SCLC patients develop metastases, and most of their tumors don't express high levels of CMYC (and often use MYCL). In any event, as the authors Discuss, this will be an important next stage to test.

We have acknowledged and explained the limitations of the work in several ways. Further, we were unaware of the relationship between metastases and the expression of MYC and MYCL1 noted by the reviewer; we will look for confirmation of this association in any future studies, although we have not encountered it in current literature.

(4) Their assays for metastases involved looking for anatomically "gross" lesions. While that is fine, particularly given that the "gross" lesions they show in figures are actually pretty small, we still need to know if they performed straightforward autopsies on mice and looked for other well-known sites of metastases in SCLC patients besides liver and lung - namely lymph nodes, adrenal, bone marrow, and brain. I would guess these would probably not show metastatic growth but with the current report, we don't know if these were looked for or not. Again, while this could be a "negative" result, the paper's value would be increased by these simple data. Let's assume no metastases are seen, then the authors could further strengthen the case for the value of their hESC model in systematically exploring with functional genomics the requirements to achieve metastases to these other sites.

We have included descriptions of what we found and didn’t find at other potential sites of metastasis in the results section, with the following sentences: 

“In animals administered DOX, histological examinations showed that approximately half developed metastases in distant organs, including the liver or lung (Figure 1D). No metastases were observed in the bone, brain, or lymph nodes. For a more detailed assessment, future studies could employ more sensitive imaging methods, such as luciferase imaging.”

(5) Related to this, we have no idea if the mice that developed liver metastases (or the one mouse with lung metastasis) had more than one metastatic site. They will know this and should report it. Again, my guess is that these were isolated metastases in each mouse. Again, they can indicate the value of their model in searching for programs that would increase the number of the various organs. 

We appreciate the suggestion. We observed that one of the mice developed metastatic tumors in both the liver and lungs. This information has been incorporated into the Results section.

(6) While renal capsule implantation for testing growth and metastatic behavior is reasonable and based on substantial literature using this site for implantation of patient tumor specimens, what would have increased the value of the paper is knowing the results from orthotopic (lung implantation). Whatever the results were (they occurred or did not occur) they will be important to know. I understand the "future experiments" argument, but in reading the manuscript this jumped out at me as an obvious thing for the authors to try. 

We conducted orthotopic implantation several ways, including via intra-tracheal instillation of 0.5 million RP or RPM cells in PBS per mouse. However, none of the subjects (0/5 mice) developed tumor-like growths and the number of animals used was small. Further, this outcome could be attributed to biological or physical factors. For instance, the conducting airway is coated with secretory cells producing protective mucins and may not have retained the 0.5 million cells. This is one example that may have hindered effective colonization. Future adjustments, such as increasing the number of cells, embedding them in Matrigel, or damaging the airway to denude secretory cells and trigger regeneration might alter the outcomes. These ideas might guide future work to strengthen the utility of the models.

(7) Another obvious piece of data that would have improved the value of this manuscript would be to know whether the RPM tumors responded to platin-etoposide chemotherapy. Such data was not presented in their first RP hESC notch inhibition paper (which we now know generated what the authors call "benign" tumors). While I realize chemotherapy responses represent other types of experiments, as the authors point out one of the main reasons they developed their new human model was for therapy testing. Two papers in and we are all still asking - does their model respond or not respond dramatically to platin-etoposide therapy? Whatever the results are they are a vital next step in considering the use of their model. 

Please see the comments above regarding our decision not to include data from a clinical trial that lacked appropriate controls.

(8) The finding of RPM cells that expressed NEUROD1, ASCL1, or both was interesting. From the way the data were presented, I don't have a clear idea which of these lineage oncogenes the metastatic lesions from ~11 different mice expressed. Whatever the result is it would be useful to know - all NEUROD1, some ASCL1, some mixed etc.

Based on the bulk RNA-sequencing of a few metastatic sites (Figure 4H), what we can demonstrate is that all sites were NEUROD1 and expressed low or no detectable  ASCL1.

(9) While several H&E histologic images were presented, even when I enlarged them to 400% I couldn't clearly see most of them. For future reference, I think it would be important to have several high-quality images of the RP, RPM, RPMT58A subcutaneous tumors, sub-renal capsule tumors, and liver and lung metastatic lesions. If there is heterogeneity in the primary tumors or the metastases it would be important to show this. The quality of the images they have in the pdf file is suboptimal. If they have already provided higher-quality images - great. If not, I think in the long run as people come back to this paper, it will help both the field and the authors to have really great images of their tumors and metastases. 

We have attempted to improve the quality of the embedded images. Digital resolution is a tradeoff with data size – higher resolution images are always available upon request, but may not be suitable  for generation of figures in a manuscript viewed on-line.

eLife Assessment

This study reports valuable insights into the interactome of the RNA-binding protein SERBP1 and possible links through PARylation to diverse processes, including splicing, cell division, and ribosome biogenesis. The diversity of processes SERBP1 may regulate means this work would be of very broad interest to the cell biology community. The proteomics data are solid, but the functional connection to downstream processes and the link to Alzheimer's disease, while compelling, still require further examination. These latter data currently rely on a very limited set of experiments and patient samples with questionable quality of preservation and methodology.

Reviewer #1 (Public review):

Summary:

Here the authors convincingly identify and characterize the SERBP1 interactome and further define its role in the nucleus, where it is associated with complexes involved in splicing, cell division, chromosome structure, and ribosome biogenesis. Many of the SERBP1-associated proteins are RNA-binding proteins and SERBP1 exerts its impact, at least in part, through these players. SERBP1 is mostly disordered but along with its associated proteins displays a preference for G4 binding and can can bind to PAR and be PARylated. They present data that strongly suggest that complexes in which SERBP1 participates are assembled through G4 or PAR binding. The authors suggest that because SERBP1 lacks traditional functional domains yet is clearly involved in distinct regulatory complexes, SERBP1 likely acts in the early steps of assembly through the recognition of interacting sites present in RNA, DNA, and proteins.

Strengths:

The data is very convincing and demonstrated through multiple approaches.

Weaknesses:

None. The authors have adequately addressed earlier reviewer concerns.

Reviewer #2 (Public review):

Summary:

In this study the authors have used pull-down experiments in a cell line overexpressing tagged SERPINE1 mRNA binding protein 1 (SERBP1) followed by mass spectrometry-based proteomics, to establish its interactome. Extensive analyses are performed to connect the data to published resources. The authors attempt to connect SERBP1 to stress granules and Alzheimer's disease associated tau pathology. Based on the interactome, the authors propose a cross-talk between SERBP1 and PARP1 functions.

Strengths:

The main strength of this study lies in the extensive proteomics data analysis, and its effort to connect the data to published studies.

Weaknesses:

Support for the proposed model: While the authors propose a feedback regulatory model for SERBP1 and PARP1 function, strong evidence for PARylation modulating SERBP1 functions is lacking. PARP inhibition decreasing the amount of PARylated proteins associated with SERBP1 and likely all other PARylated proteins is expected.<br /> Evidence from autopsy brain tissue: This study shows unexplained round, punctate staining for SERBP1 in immunohistochemistry (IHC) staining. This may be due to poor preservation of cellular structures in frozen autopsy brain tissue. SERBP1 and pTau co-staining lacks an age matched non-AD control. Most quantifications of human IHC staining and co-localization do not indicate the number of cases and what data points are shown.<br /> The link to stress granules (SGs): G3BP1 staining indicates cytoplasmic mislocalization and perhaps aggregation pathology, but not necessarily SGs. It is not clear whether physiological transient stress granules are preserved in autopsy brain tissue. The co-localization of abundant cytoplasmic G3BP1 and SERBP1 under normal conditions does not indicate association with SGs. Stress granule proteins assemble phase-separated granules in the cytoplasm under cellular stress, whereas here it is shown that normally cytoplasmic SERBP1 has a nucleocytoplasmic distribution in the presence of H2O2, with no evidence for SG formation.

Author response:

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

Reviewer 1 (Public Review):

Summary:

Here the authors convincingly identify and characterize the SERBP1 interactome and further define its role in the nucleus, where it is associated with complexes involved in splicing, cell division, chromosome structure, and ribosome biogenesis. Many of the SERBP1-associated proteins are RNA-binding proteins and SERBP1 exerts its impact, at least in part, through these players. SERBP1 is mostly disordered but along with its associated proteins displays a preference for G4 binding and can bind to PAR and be PARylated. They present data that strongly suggest that complexes in which SERBP1 participates are assembled through G4 or PAR binding. The authors suggest that because SERBP1 lacks traditional functional domains yet is clearly involved in distinct regulatory complexes, SERBP1 likely acts in the early steps of assembly through the recognition of interacting sites present in RNA, DNA, and proteins.

Strengths:

The data is very convincing and demonstrated through multiple approaches.

Weaknesses:

No weaknesses were identified by this reviewer.

Reviewer #2 (Public Review):

Summary:

In this study the authors have used pull-down experiments in a cell line overexpressing tagged SERPINE1 mRNA binding protein 1 (SERBP1) followed by mass spectrometry-based proteomics, to establish its interactome. Extensive analyses are performed to connect the data to published resources. The authors attempt to connect SERBP1 to stress granules and Alzheimer's disease-associated tau pathology. Based on the interactome, the authors propose a cross-talk between SERBP1 and PARP1 functions.

Strengths:

The main strength of this study lies in the proteomics data analysis, and its effort to connect the data to published studies.

Weaknesses:

While the authors propose a feedback regulatory model for SERBP1 and PARP1 functions, strong evidence for PARylation modulating SERBP1 functions is lacking. PARP inhibition decreasing the amount of PARylated proteins associated with SERBP1 and likely all other PARylated proteins is expected. This study is also incomplete in its attempt to establish a connection to Alzheimer's disease related tauopathy. A single AD case is not sufficient, and frozen autopsy tissue shows unexplained punctate staining likely due to poor preservation of cellular structures for immunohistochemistry. There is a lack of essential demographic data, source of the tissue, brain regions shown, and whether there was an IRB protocol for the human brain tissue. The presence of phase-separated transient stress granules in an autopsy brain is unlikely, even if G3BP1 staining is present. Normally, stress granule proteins move to the cytoplasm under cellular stress, whereas SERBP1 becomes nuclear. The co-localization of abundant cytoplasmic G3BP1 and SERBP1 under normal conditions does not indicate an association with stress granules.

Reviewer #3 (Public Review):

Summary:

A survey of SERBP1-associated functions and their impact on the transcriptome upon gene depletion, as well as the identification of chemical inhibitors upon gene over-expression.

Strengths:

(1) Provides a valuable resource for the community, supported by statistical analyses.

(2) Offers a survey of different processes with correlation data, serving as a good starting point for the community to follow up.

Weaknesses:

(1) The authors provided numerous correlations on diverse topics, from cell division to RNA splicing and PARP1 association, but did not follow up their findings with experiments, offering little mechanistic insight into the actual role of SERBP1. The model in Figure 5D is entirely speculative and lacks data support in the manuscript.

Our article includes several pieces of evidence that support SERBP1’s role in splicing, translation, cell division and association with PARP1. We respectfully disagree that the model in Figure 5D is speculative. The goal of our study was to generate initial evidence of SERBP1 involvement in different biological processes based on its interactome. The characterization of molecular mechanisms in all these scenarios requires a substantial amount work and will the topic of follow up manuscripts. 

(2) Following up with experiments to demonstrate that their findings are real (e.g., those related to splicing defects and the PARylation/PAR-binding association) would be beneficial. For example, whether the association between PARP1 and SERBP1 is sensitive to PAR-degrading enzymes is unclear.

We included experiments showing the interaction between endogenous SERBP1 and PARP1. Additionally, we demonstrated that SERBP1 interaction with PARP1 was disrupted when cells are treated with PARP inhibitors.

(3) They did not clearly articulate how experiments were performed. For instance, the drug screen and even the initial experiment involving the pull-down were poorly described. Many in the community may not be familiar with vectors such as pSBP or pUltra without looking up details.

We provided additional details about the vectors and expanded the description of experiments in results and figure legends.

(4) The co-staining of SERBP1 with pTau, PARP1, and G3BP1 in the brain is interesting, but it would be beneficial to follow up with immunoprecipitation in normal and patient samples to confirm the increased physical association.

Thank you for this suggestion. We performed instead a Proximity Ligation Assay (PLA) on human tissue. Data was included in Fig. 7B and C. PLA between pTau and SERBP1 confirmed interaction in AD cortices as well as SERBP1 with PARP1.

(5) The combination index of 0.7-0.9 for PJ34 + siSERBP1 is weak. Could this be due to the non-specific nature of the drug against other PARPs? Have the authors looked into this possibility?

The combination index could be considered weak in the case of U251 cells but not in the case of U343 cells. PJ34 has been shown to be mainly a PARP-1 inhibitor. Different PJ34 concentrations and different drugs will be examined in future studies. It is worth mentioning that in a genetic screening, SERBP1 has been shown to increase sensitivity to different PARP inhibitors (PMID: 37160887). This information is included in the manuscript.

Reviewer #1 (Recommendations For The Authors):

This is a really well-done piece of research that is written very well. The data are very convincing and the conclusions are well supported. Some wording in Figures 2B and D is pixelated and hard to read. All the figure legends could benefit from being expanded but this is especially true for Figures 2, 3, 7, and 8. There is a ton of data being presented and a very limited description of what was done and what is being concluded. Some of the content may not be fully comprehended by some readers with limited descriptions.

We revised all figures to assure images are clear and their resolution is high. We expanded all figure legends to provide a better explanation of the experimental design.

Reviewer #2 (Recommendations For The Authors):

The "merged" pdf file is the same as the "article".

Individual files were uploaded this time.

The abstract should spell out acronyms, such as the name of the protein Serpine1 mRNA-binding protein 1 (SERBP1).

This was not included since the abstract has a word limit.

"SERBP1 (Serpine1 mRNA-binding protein 1) is a unique member of this group of RBPs". In what way is it unique?

The text was modified to better explain SERBP1’s singularities.

"RBPs containing IDRs and RGG motifs are particularly relevant in the nervous system. Their misfolding contributes to the formation of pathological protein aggregates in Alzheimer's disease (AD), Frontotemporal Lobar Dementia (FTLD), Amyotrophic Lateral Sclerosis (ALS), and Parkinson's disease (PD)" -> while TDP-43 and FUS in ALS/FTD may fit this description, it is not true for tau and amyloid-beta (AD) and alpha-synuclein (PD).

"SERBP1 is a unique RBPs containing IDRs and RGG motifs yet lacks other readily recognizable, canonical or structured RNA binding motifs. Moreover, SERBP1 has been observed by our study and others as common Tau interactor in Alzheimer’s Disease (AD) brains. RBPs containing IDRs (e.g. TDP-43, FUS, hnRNPs, TIA1) have been shown self-aggregate and co-aggregate with pathogenic amyloids (Tau, Aβ-amyloid and α-Synuclein)  in AD, Frontotemporal Lobar Dementia (FTLD), Amyotrophic Lateral Sclerosis (ALS), and Parkinson's disease (PD) and this suggest that, like other IDRs RBPs, SERBP1 contributes to RNA dysmetabolism in neurodegenerative diseases”.

While the authors propose a feedback regulatory model for SERBP1 and PARP1 functions, strong evidence for PARylation modulating SERBP1 functions is lacking. The fact that PARP inhibition decreases the amount of PARylated proteins associated with SERBP1 and likely all other PARylated proteins is expected and cannot count as evidence.

We included data showing that treatment with PJ34 (PARP inhibitor) decreases SERBP1 interaction with PARP1 and G3BP1. We are currently conducting a more extensive analysis to identify SERBP1 PAR binding domain and the impact of PARP inhibition on its interactions and functions. These experiments will be included in a new manuscript.

A single AD case is not sufficient.

Sorry for the poor clarity. We included in the study 6 cases from age-matched controls and 6 cases of AD. We summarize all cases demographics, and the experimental application assigned to each case in Table 1. Moreover, we included a paragraph regarding Human tissue harvesting.

Most western blot data are not quantified from multiple replicates, as required.

Quantifications are now provided.

FTLD - frontotemporal lobar degeneration (not dementia).

This was corrected.

Frozen autopsy tissue is problematic due to poor preservation. The staining presented here shows unexplained punctate staining likely due to poor preservation of cellular structures for immunohistochemistry.

We included a paragraph regarding human tissue harvesting. We have successfully used frozen tissues in our previous studies, observing a well preserved neuronal and tissue structure (PMIDs: 32855391, 31532069 and 30367664)

The presence of phase-separated stress granules in tissue is controversial since these are transient structures.

Normally, stress granule proteins move to the cytoplasm under cellular stress, whereas SERBP1 becomes nuclear. The co-localization of abundant (and partially overexposed) cytoplasmic G3BP1 and SERBP1 under normal conditions is not evidence for association with stress granules. Does induction of stress granule formation lead to colocalization in stress granules? The H2O2 experiment suggests otherwise.

RBPs implicated in stress response move to stress granules when cells are exposed to stress. SERBP1 has been shown to shuttle to stress granules and nucleus in stress conditions (PMID: 24205981). Our results are in agreement.

Using co-IF, we observed some overlap between G3BP1 and SERBP1 in AD tissues. As shown in Fig. S6A and B, 50% of stress granules overlap with SERBP1 signal. On the contrary, it is hard to assess their relationship in aged-matched control brains where stress granules form and accumulate with a lower rate than in AD. SERBP1 is not very abundant in normal brains.  It is known that RNA-Binding Proteins aggregation and/or dysfunctional LLPS dysregulate stress granules formation and accumulation in AD and other proteinopathies (PMIDs 30853299, 27256390 and 31911437). However, it is too early to determine the role of SERBP1 and its contribution to stress granules formation and accumulation. We will examine this topic in future studies.

There is a lack of essential demographics data (age, clinical diagnosis, path diagnosis, co-pathologies, Braak stage, etc.), source of the tissue (what brain bank?), brain regions shown, and whether there was informed consent for the collection and use of human brain tissue.

We included the information requested in materials and methods section.

Reviewer #3 (Recommendations For The Authors):

The authors need to better explain their experimental rationale and approach in the main text, not just in the supplementary materials.

We have extensively revised the text to provide a better description of experiments in the results section and figure legends.

eLife Assessment

This work is a valuable study that presents a detailed analysis of translation, driven by the untranslated regions of the Japanese encephalitis virus. It reports a role for the RNA helicase DDX3 in promoting a cap-independent translation mechanism. The conclusions are based on generally solid evidence, although there are some weaknesses in the overall model based on suboptimal experimental approaches and over-interpretation of some of the data. Addressing deficiencies noted in peer review could elevate the impact of the study.

Reviewer #1 (Public review):

Summary:

In cells undergoing Flavivirus infection, cellular translation is impaired but the viruses themselves escape this inhibition and are efficiently translated. In this study, the authors use very elegant and direct approaches to identify the regions in the 5' and 3' UTRs that are important for this phenomenon and then use them to retrieve two cellular proteins that associate with them and mediate translational shutoff evasion (DDX3 and PABP1). A number of experimental approaches are used with a series of well-controlled experiments that fully support the authors' conclusions.

Strengths:

The work identifies the regions in the 5' and 3' UTRs of the viral genome that mediate the escape of JEV from cellular transcriptional shutoff, they evaluate the infectivity of the mutant viruses bearing or not these structures and even explore their pathogenicity in mice. They then identify the cellular proteins that bind to these regions (DDX3 and PABP1) and determine their role in translation blockade escape, in addition to examining and assessing the conservation of the stem-loop identified in JEV in other Flaviviridae.

In almost all of their systematic analyses, translational effects are put in parallel with the replication kinetics of the different mutant viruses. The experimental thread followed in this study is rigorous and direct, and all experiments are truly well-controlled, fully supporting the authors' conclusions

Reviewer #2 (Public review):

Summary:

The authors use a combination of techniques including viral genetics, in vitro reporters, and purified proteins and RNA to interrogate how the Japanese encephalitis virus maintains translation of its RNA to produce viral proteins after the host cell has shut down general translation as a means to block viral replication. They report a role for the RNA helicase DDX3 in promoting virus translation in a cap-independent manner through binding a dumbbell RNA structure in the 3' untranslated region previously reported to drive Japanese encephalitis virus cap-independent translation and a stem-loop at the viral RNA 5' end.

Strengths:

The authors clearly show that the Japanese encephalitis virus does not possess an IRES activity to initiate translation using a range of mono- and bi-cistronic mRNAs. Surprisingly, using a replicon system, the translation of a capped or uncapped viral RNA is reported to have the same translation efficiency when transfected into cells. The authors have applied a broad range of techniques to support their hypotheses.

Weaknesses:

(1) The authors' original experiments in Figure 1 where the virus is recovered following transfection of in vitro transcribed viral RNA with alternative 5' ends such as capped or uncapped ignore that after a single replication cycle of that transfected RNA, the subsequent viral RNA will be capped by the viral capping proteins making the RNA in all conditions the same.

(2) The authors report that deletion of the dumbbell and the large 3' stem-loop RNA reduce replication of a Japanese encephalitis virus replicon. These structures have been reported for other flaviviruses to be important respectively for the accumulation of short flaviviral RNAs that can regulate replication and stability of the viral RNA that lacks a polyA tail. The authors don't show any assessment of RNA stability or degradation state.

(3) The authors propose a model for DDX3 to drive 5'-3' end interaction of the Japanese encephalitis virus viral genome but no direct evidence for this is presented.

(4) The authors' final model in Figure 10 proposes a switch from a cap-dependent translation system in early infection to cap-independent DDX3-driven translation system late in infection. The replicon data that measures translation directly however shows identical traces for capped and uncapped RNAs in all untreated conditions so that which mechanism is used at different stages of the infection is not clear.

Reviewer #3 (Public review):

Summary:

This work is a valuable study that aims to decipher the molecular mechanisms underlying the translation process in Japanese encephalitis virus (JEV), a relevant member of the genus Flavivirus. The authors provide evidence that cap-independent translation, which has already been demonstrated for other flaviviruses, could also account in JEV. This process depends on the genomic 3' UTR, as previously demonstrated in other flaviviruses. Further, the authors find that cellular proteins such as DDX3 or PABP1 could contribute to JEV translation in a cap-independent way. Both DDX3 and PABP1 had previously been described to have a role in cellular protein synthesis and also in the translation step of other flaviviruses distinct from JEV; therefore, this work would expand the cap-independent translation in flaviviruses as a general mechanism to bypass the translation repression exerted by the host cell during viral infection. Further, the findings can be relevant for the development of specific drugs that could interfere with flaviviral translation in the future. Nevertheless, the conclusions are not fully supported by the provided results.

Strengths:

The results provide a good starting point to investigate the molecular mechanism underlying the translation in flaviviruses, which even today is an area of knowledge with many limitations.

Weaknesses:

The main limit of the work is related to the fact that the role of the 3' UTR structural elements and DDX3 is not only circumscribed to translation, but also to replication and encapsidation. In fact, some of the provided results suggest this idea. Particularly, it is intriguing why the virus titer can be completely abrogated while the viral protein levels are only partially affected by the knockdown of DDX3. This points to the fact that many of the drawn conclusions could be overestimated or, at least, all the observed effect cannot be attributed only to the DDX3 effect on translation. Finally, it is noteworthy that the use of uncapped transcripts could be misleading, since this is not the natural molecular context of the viral genome.

Author response:

Reviewer #1 (Public review):

Summary:

In cells undergoing Flavivirus infection, cellular translation is impaired but the viruses themselves escape this inhibition and are efficiently translated. In this study, the authors use very elegant and direct approaches to identify the regions in the 5' and 3' UTRs that are important for this phenomenon and then use them to retrieve two cellular proteins that associate with them and mediate translational shutoff evasion (DDX3 and PABP1). A number of experimental approaches are used with a series of well-controlled experiments that fully support the authors' conclusions.

Strengths:

The work identifies the regions in the 5' and 3' UTRs of the viral genome that mediate the escape of JEV from cellular transcriptional shutoff, they evaluate the infectivity of the mutant viruses bearing or not these structures and even explore their pathogenicity in mice. They then identify the cellular proteins that bind to these regions (DDX3 and PABP1) and determine their role in translation blockade escape, in addition to examining and assessing the conservation of the stem-loop identified in JEV in other Flaviviridae.

In almost all of their systematic analyses, translational effects are put in parallel with the replication kinetics of the different mutant viruses. The experimental thread followed in this study is rigorous and direct, and all experiments are truly well-controlled, fully supporting the authors' conclusions.

We greatly appreciate the reviewer's recognition of this study. We elucidated the role of UTR in translation blockade escape of JEV from the perspective of the RNA structure of the UTR and its interaction with host proteins (DDX3 and PABP1), and we hope that this study could gain wider recognition.

Reviewer #2 (Public review):

Summary:

The authors use a combination of techniques including viral genetics, in vitro reporters, and purified proteins and RNA to interrogate how the Japanese encephalitis virus maintains translation of its RNA to produce viral proteins after the host cell has shut down general translation as a means to block viral replication. They report a role for the RNA helicase DDX3 in promoting virus translation in a cap-independent manner through binding a dumbbell RNA structure in the 3' untranslated region previously reported to drive Japanese encephalitis virus cap-independent translation and a stem-loop at the viral RNA 5' end.

Strengths:

The authors clearly show that the Japanese encephalitis virus does not possess an IRES activity to initiate translation using a range of mono- and bi-cistronic mRNAs. Surprisingly, using a replicon system, the translation of a capped or uncapped viral RNA is reported to have the same translation efficiency when transfected into cells. The authors have applied a broad range of techniques to support their hypotheses.

We are grateful for the reviewer’s recognition of the thoroughness and multi-faceted nature of our study.

Weaknesses:

(1) The authors' original experiments in Figure 1 where the virus is recovered following transfection of in vitro transcribed viral RNA with alternative 5' ends such as capped or uncapped ignore that after a single replication cycle of that transfected RNA, the subsequent viral RNA will be capped by the viral capping proteins making the RNA in all conditions the same.

Thank you for your suggestion. We share the same viewpoint as the reviewer. After the first round of translation of the uncapped viral RNA, the subsequent viral RNA will inevitably be capped by the viral capping proteins. However, there is no doubt that the transfected cells do not contain viral capping proteins in the initial transfection stage, which directly proved that JEV possesses a cap-independent translation initiation mechanism.

(2) The authors report that deletion of the dumbbell and the large 3' stem-loop RNA reduce replication of a Japanese encephalitis virus replicon. These structures have been reported for other flaviviruses to be important respectively for the accumulation of short flaviviral RNAs that can regulate replication and stability of the viral RNA that lacks a polyA tail. The authors don't show any assessment of RNA stability or degradation state.

Thank you for your suggestion. We agree that a rigorous supplementary experiment for the assessment of RNA stability or degradation state is desirable. To address this, the relative amounts of viral RNA with the deletion of DB2 or sHP-SL will be determined by real-time RT-PCR analysis in transfected cells at multiple time points, which will allow us to test whether the deletion of the dumbbell and the large 3' stem-loop RNA reduce the RNA stability of JEV.

(3) The authors propose a model for DDX3 to drive 5'-3' end interaction of the Japanese encephalitis virus viral genome but no direct evidence for this is presented.

Thank you for your suggestion. In this study, we did not have direct evidence to suggest that DDX3 can drive the 5'-3' end interaction of the Japanese encephalitis virus viral genome, which is indeed a limitation of our research. In the revision, we will more explicitly discuss the interrelationship between DDX3 and 5'-3' UTR, as well as incorporate a discussion of these points into the main text, acknowledging the limitations of our current models.

(4) The authors' final model in Figure 10 proposes a switch from a cap-dependent translation system in early infection to cap-independent DDX3-driven translation system late in infection. The replicon data that measures translation directly however shows identical traces for capped and uncapped RNAs in all untreated conditions so that which mechanism is used at different stages of the infection is not clear.

Thank you for your suggestion. The replicon transfection system was used to evaluate the key viral element for cap-independent translation. We only monitored reporter gene expression from 2 hpt to 12 hpt, which can’t fully recapitulate the different stages of JEV infection. In the experimental results Figure 1 and Figure 1-figure supplement 1, we demonstrated that JEV significantly induced the host translational shutoff at 36 hpi, while the expression level of viral protein gradually increased as infection went on, suggesting that JEV translation could evade the shutoff of cap-dependent translation initiation at the late stage of infection. As shown in the growth curves in Figure 5Q, JEV replicated to similar virus titers in WT and DDX3-KO cells from 12 hpi to 36 hpi, but higher level virus yields were observed in WT cells from 48 hpi, suggesting that DDX3 is important for JEV infection at the late stage. DDX3 was demonstrated to be critical for JEV cap-independent translation. Based on these data, we proposed that the DDX3-dependent cap-independent translation is employed by JEV to maintain efficient infection at the late stage when the cap-dependent translation imitation was suppressed.

Reviewer #3 (Public review):

Summary:

This work is a valuable study that aims to decipher the molecular mechanisms underlying the translation process in Japanese encephalitis virus (JEV), a relevant member of the genus Flavivirus. The authors provide evidence that cap-independent translation, which has already been demonstrated for other flaviviruses, could also account in JEV. This process depends on the genomic 3' UTR, as previously demonstrated in other flaviviruses. Further, the authors find that cellular proteins such as DDX3 or PABP1 could contribute to JEV translation in a cap-independent way. Both DDX3 and PABP1 had previously been described to have a role in cellular protein synthesis and also in the translation step of other flaviviruses distinct from JEV; therefore, this work would expand the cap-independent translation in flaviviruses as a general mechanism to bypass the translation repression exerted by the host cell during viral infection. Further, the findings can be relevant for the development of specific drugs that could interfere with flaviviral translation in the future. Nevertheless, the conclusions are not fully supported by the provided results.

Strengths:

The results provide a good starting point to investigate the molecular mechanism underlying the translation in flaviviruses, which even today is an area of knowledge with many limitations.

Thank you to the reviewer for providing positive feedback. The research on the molecular mechanism underlying cap-independent translation is still a limited field in the flaviviruses, and its mechanism has not been well elucidated at present. We only hope that this study could reveal a novel mechanism of translation initiation for flaviviruses.

Weaknesses:

The main limit of the work is related to the fact that the role of the 3' UTR structural elements and DDX3 is not only circumscribed to translation, but also to replication and encapsidation. In fact, some of the provided results suggest this idea. Particularly, it is intriguing why the virus titer can be completely abrogated while the viral protein levels are only partially affected by the knockdown of DDX3. This points to the fact that many of the drawn conclusions could be overestimated or, at least, all the observed effect cannot be attributed only to the DDX3 effect on translation. Finally, it is noteworthy that the use of uncapped transcripts could be misleading, since this is not the natural molecular context of the viral genome.

Thank you for your suggestion. We agree with the reviewer's comments that the role of the 3' UTR structural elements and DDX3 may not only be circumscribed to translation. However, not as described by the reviewer, DDX3 knockdown did not completely abrogate JEV infection. As indicated in Figure 5E-5F, the recombinant virus was successfully rescued at 36 hpt and 48 hpt using the uncapped viral genomic RNA, although the viral titer rescued with the uncapped genomic RNA at 24 hpt was below the limit of detection. We have confirmed that the DB2 and sHP-SL elements in 3' UTR play a decisive role in the replication of viral RNA in our research (Figure 2G and Figure 2-figure supplement 4C), and we will further analyze the role of DDX3 in viral RNA replication and encapsidation, thereby clarifying the multiple functions of DDX3 in JEV life cycle. Meanwhile, we will incorporate a discussion of these points into the main text, acknowledging the limitations of our current research.

To eliminate the misleading effects of using uncapped transcripts, we will use a natural molecular background of the viral genome with cap methylation deficiency. The methyltransferase (MTase) of the flavivirus NS5 protein catalyzes  N-7 and 2’-O methylations in the formation of the 5’-end cap of the genome, and the E218 amino acid of the NS5 protein MTase domain is one of the active sites of flavivirus methyltransferase (PLoS Pathogens. 2012. PMID:22496660; Journal of Virology. 2007. PMID: 1866096). We will construct a mutant virus of the E218A mutation to abolish 2'-O methylation activity and significantly reduce N-7 methylation activity and then analyze the roles of UTR structure and DDX3 in recombinant viruses with the type-I cap structure functional deficiency.

eLife Assessment

The authors demonstrated cellular heterogeneity of companion cells (CCs) and also suggested the CC subpopulation that highly expressed the florigen gene FT. Based on this finding, they further identified flowering time regulators acting in CCs, including small proteins and NITRATE-INDUCIBLE GARP-TYPE TRANSCRIPTIONAL REPRESSOR1 type proteins (NIGT1s). In particular, the authors propose the NIGT1-FT regulatory module, which may be involved in the response to nitrogen status. This important study advances our understanding of flowering time control at high spatial resolution. While we believe this work will be of broad interest to plant biologists, the supporting evidence remains in parts incomplete. In particular, the quality of the single-cell and bulk RNA-seq data needs to be addressed to solidify the conclusions.

Reviewer #1 (Public review):

Summary:

The authors revealed the cellular heterogeneity of companion cells (CCs) and demonstrated that the florigen gene FT is highly expressed in a specific subpopulation of these CCs in Arabidopsis. Through a thorough characterization of this subpopulation, they further identified NITRATE-INDUCIBLE GARP-TYPE TRANSCRIPTIONAL REPRESSOR 1 (NIGT1)-like transcription factors as potential new regulators of FT. Overall, these findings are intriguing and valuable, contributing significantly to our understanding of florigen and the photoperiodic flowering pathway. However, there is still room for improvement in the quality of the data and the depth of the analysis. I have several comments that may be beneficial for the authors.

Strengths:

The usage of snRNA-seq to characterize the FT-expressing companion cells (CCs) is very interesting and important. Two findings are novel: 1) Expression of FT in CCs is not uniform. Only a subcluster of CCs exhibits high expression level of FT. 2) Based on consensus binding motifs enriched in this subcluster, they further identify NITRATE-INDUCIBLE GARP-TYPE TRANSCRIPTIONAL REPRESSOR 1 (NIGT1)-like transcription factors as potential new regulators of FT.

Weaknesses:

(1) Title: "A florigen-expressing subpopulation of companion cells". It is a bit misleading. The conclusion here is that only a subset of companion cells exhibit high expression of FT, but this does not imply that other companion cells do not express it at all.<br /> (2) Data quality: Authors opted for fluorescence-activated nuclei sorting (FANS) instead of traditional cell sorting method. What is the rationale behind this decision? Readers may wonder, especially given that RNA abundance in single nuclei is generally lower than that in single cells. This concern also applies to snRNA-seq data. Specifically, the number of genes captured was quite low, with a median of only 149 genes per nucleus. Additionally, the total number of nuclei analyzed was limited (1,173 for the pFT:NTF and 3,650 for the pSUC2:NTF). These factors suggest that the quality of the snRNA-seq data presented in this study is quite low. In this context, it becomes challenging for the reviewer to accurately assess whether this will impact the subsequent conclusions of the paper. Would it be possible to repeat this experiment and get more nuclei?<br /> (3) Another disappointment is that the authors did not utilize reporter genes to identify the specific locations of the FT-high expressing cells (cluster 7 cells) within the CC population in vivo. Are there any discernible patterns that can be observed?<br /> (4) The final disappointment is that the authors only compared FT expression between the nigtQ mutants and the wild type. Does this imply that the mutant does not have a flowering time defect particularly under high nitrogen conditions?

Reviewer #2 (Public review):

This manuscript submitted by Takagi et al. details the molecular characterization of the FT-expressing cell at a single-cell level. The authors examined what genes are expressed specifically in FT-expressing cells and other phloem companion cells by exploiting bulk nuclei and single-nuclei RNA-seq and transgenic analysis. The authors found the unique expression profile of FT-expressing cells at a single-cell level and identified new transcriptional repressors of FT such as NIGT1.2 and NIGT1.4.

Although previous researchers have known that FT is expressed in phloem companion cells, they have tended to neglect the molecular characterization of the FT-expressing phloem companion cells. To understand how FT, which is expressed in tiny amounts in phloem companion cells that make up a very small portion of the leaf, can be a key molecule in the regulation of the critical developmental step of floral transition, it is important to understand the molecular features of FT-expressing cells in detail. In this regard, this manuscript provides insight into the understanding of detailed molecular characteristics of the FT-expressing cell. This endeavor will contribute to the research field of flowering time.

Here are my comments on how to improve this manuscript.

(1) The most noble finding of this manuscript is the identification of NTGI1.2 as the upstream regulator of FT-expressing cluster 7 gene expression. The flowering phenotypes of the nigtQ mutant and the transgenic plants in which NIGT1.2 was expressed under the SUC2 gene promoter support that NIGT1.2 functions as a floral repressor upstream of the FT gene. Nevertheless, the expression patterns of NIGT1.2 genes do not appear to have much overlap with those of NIGT1.2-downstream genes in the cluster 7 (Figs S14 and F3). An explanation for this should be provided in the discussion section.<br /> (2) To investigate gene expression in the nuclei of specific cell populations, the authors generated transgenic plants expressing a fusion gene encoding a Nuclear Targeting Fusion protein (NTF) under the control of various cell type-specific promoters. Since the public audience would not know about NTF without reading reference 16, some explanation of NTF is necessary in the manuscript. Please provide a schematic of constructs the authors used to make the transformants.

Author response:

Reviewer #1 (Public review):

Summary:

The authors revealed the cellular heterogeneity of companion cells (CCs) and demonstrated that the florigen gene FT is highly expressed in a specific subpopulation of these CCs in Arabidopsis. Through a thorough characterization of this subpopulation, they further identified NITRATE-INDUCIBLE GARP-TYPE TRANSCRIPTIONAL REPRESSOR 1 (NIGT1)-like transcription factors as potential new regulators of FT. Overall, these findings are intriguing and valuable, contributing significantly to our understanding of florigen and the photoperiodic flowering pathway. However, there is still room for improvement in the quality of the data and the depth of the analysis. I have several comments that may be beneficial for the authors.

Strengths:

The usage of snRNA-seq to characterize the FT-expressing companion cells (CCs) is very interesting and important. Two findings are novel: 1) Expression of FT in CCs is not uniform. Only a subcluster of CCs exhibits high expression level of FT. 2) Based on consensus binding motifs enriched in this subcluster, they further identify NITRATE-INDUCIBLE GARP-TYPE TRANSCRIPTIONAL REPRESSOR 1 (NIGT1)-like transcription factors as potential new regulators of FT.

We are pleased to hear that reviewer 1 noted the novelty and importance of our work. As reviewer 1 mentioned, we are also excited about the identification of a subcluster of companion cells with very high FT expression. We believe that this work is an initial step to describe the molecular characteristics of these FT-expressing cells. We are also excited to share our new findings on NIGT1_s as potential _FT regulators. We think that this finding attracts broader audiences, as the molecular factor that coordinates plant nutrition status with flowering time remains largely unknown despite its well-known plant phenomenon.

Weaknesses:

(1) Title: "A florigen-expressing subpopulation of companion cells". It is a bit misleading. The conclusion here is that only a subset of companion cells exhibit high expression of FT, but this does not imply that other companion cells do not express it at all.

We agree with this comment, as we also did not intend to say that FT is not produced in other companion cells than the subpopulation we identified. We will revise the title to more accurately reflect the point.

(2) Data quality: Authors opted for fluorescence-activated nuclei sorting (FANS) instead of traditional cell sorting method. What is the rationale behind this decision? Readers may wonder, especially given that RNA abundance in single nuclei is generally lower than that in single cells. This concern also applies to snRNA-seq data. Specifically, the number of genes captured was quite low, with a median of only 149 genes per nucleus. Additionally, the total number of nuclei analyzed was limited (1,173 for the pFT:NTF and 3,650 for the pSUC2:NTF). These factors suggest that the quality of the snRNA-seq data presented in this study is quite low. In this context, it becomes challenging for the reviewer to accurately assess whether this will impact the subsequent conclusions of the paper. Would it be possible to repeat this experiment and get more nuclei?

We appreciate this comment; we noticed that we did not clearly explain the rationale of using single-nucleus RNA sequencing (snRNA-seq) instead of single-cell RNA-seq (scRNA-seq). As reviewer 1 mentioned, RNA abundance in scRNA-seq is higher than in snRNA-seq. To conduct scRNA-seq using plant cells, protoplasting is the necessary step. However, in our study, protoplasting has many drawbacks in isolating our target cells from the phloem. It is technically challenging to efficiently isolate protoplasts from highly embedded phloem companion cells from plant tissues. Usually, it requires a minimum of several hours of enzymatic incubation to protoplast companion cells and the efficiencies of protoplasting these cells are still low. For our analysis, restoring the time information within a day is also crucial. Therefore, we performed more speedy isolation method. In the revision, we will explain our rationale of choosing snRNA-seq due to the technical limitations.

Here, reviewer 1 raised a concern about the quality of our snRNA-seq data, referring to the relatively low readcounts per nucleus. Although we believe that shallow reads do not necessaryily indicate low quality and are confident in the accuracy of our snRNA-seq data, as supported by the detailed follow-up experiments (e.g., imaging analysis in Fig. 4B), we agree that it is important to address this point in the revision and alleviate readers’ concerns regarding the data quality.

(3) Another disappointment is that the authors did not utilize reporter genes to identify the specific locations of the FT-high expressing cells (cluster 7 cells) within the CC population in vivo. Are there any discernible patterns that can be observed?

As we previously showed only limited spatial images of overlap between FT-expressing cells and other cluster 7 gene-expressing cells in Fig. 4B, this comment is understandable. To respond to it, we will include whole leaf images of FT- and cluster 7 gene-expressing cells to assess the spatial overlaps between FT and cluster 7 genes within a leaf.

(4) The final disappointment is that the authors only compared FT expression between the nigtQ mutants and the wild type. Does this imply that the mutant does not have a flowering time defect particularly under high nitrogen conditions?

To answer this question, we will include the flowering time measurement data of the nigtQ mutants grown on the soil with sufficient nitrogen sources.

Reviewer #2 (Public review):

This manuscript submitted by Takagi et al. details the molecular characterization of the FT-expressing cell at a single-cell level. The authors examined what genes are expressed specifically in FT-expressing cells and other phloem companion cells by exploiting bulk nuclei and single-nuclei RNA-seq and transgenic analysis. The authors found the unique expression profile of FT-expressing cells at a single-cell level and identified new transcriptional repressors of FT such as NIGT1.2 and NIGT1.4.

Although previous researchers have known that FT is expressed in phloem companion cells, they have tended to neglect the molecular characterization of the FT-expressing phloem companion cells. To understand how FT, which is expressed in tiny amounts in phloem companion cells that make up a very small portion of the leaf, can be a key molecule in the regulation of the critical developmental step of floral transition, it is important to understand the molecular features of FT-expressing cells in detail. In this regard, this manuscript provides insight into the understanding of detailed molecular characteristics of the FT-expressing cell. This endeavor will contribute to the research field of flowering time.

We are grateful that reviewer 2 recognizes the importance of transcriptome profiling of FT-expressing cells at the single-cell level.

Here are my comments on how to improve this manuscript.

(1) The most noble finding of this manuscript is the identification of NTGI1.2 as the upstream regulator of FT-expressing cluster 7 gene expression. The flowering phenotypes of the nigtQ mutant and the transgenic plants in which NIGT1.2 was expressed under the SUC2 gene promoter support that NIGT1.2 functions as a floral repressor upstream of the FT gene. Nevertheless, the expression patterns of NIGT1.2 genes do not appear to have much overlap with those of NIGT1.2-downstream genes in the cluster 7 (Figs S14 and F3). An explanation for this should be provided in the discussion section.

We agree reviewer 2 that spatial expression patterns of NIGT1.2 and cluster 7 genes do not overlap much, and some discussion should be provided in the manuscript. Although we do not have a concrete answer for this phenomenon, NIGT1.2 may suppress FT gene expression in non-cluster 7 cells to prevent the misexpression of FT. Another possible explanation is that NIGT1.2 negatively affects the formation of cluster 7 cells. If so, cells with high NIGT1.2 gene expression hardly become cluster 7 cells. We will discuss it further in the discussion section in our revised manuscript.

(2) To investigate gene expression in the nuclei of specific cell populations, the authors generated transgenic plants expressing a fusion gene encoding a Nuclear Targeting Fusion protein (NTF) under the control of various cell type-specific promoters. Since the public audience would not know about NTF without reading reference 16, some explanation of NTF is necessary in the manuscript. Please provide a schematic of constructs the authors used to make the transformants.

As reviewer 2 pointed out, we lacked a clear explanation why we used NTF in this study. NTF is the fusion protein that consists of a nuclear envelope targeting domain, GFP, and biotin acceptor peptide. It was originally designed for the INTACT (isolation of nuclei tagged in specific cell types) method that enables us to isolate bulk nuclei from specific tissues. Although our original intention was profiling the bulk transcriptome of mRNAs that exist in nuclei of the FT-expressing cells using INTACT, we utilized our NTF transgenic lines for snRNA-seq analysis. To explain what NTF is to readers, we will include a schematic diagram of NTF.

eLife Assessment

The manuscript provides an important assessment of the number and distribution of different retrovirus env genes present in primate genomes in the form of ancient endogenous retroviruses (ERV loci) and the potential role that viral recombination played in the diversification of retrovirus env genes and their propagation in the primate germline over millions of years. The exploration of this process in this study is considered solid, ultimately representing a conceptual advance with potentially broad implications. However, issues of clarity in the text and figures of the current version of the manuscript, as noted by multiple reviewers, may limit the ultimate impact of the work if insufficiently unaddressed.

Reviewer #1 (Public review):

Summary

Chabukswar et al analysed endogenous retrovirus (ERV) Env variation in a set of primate genomes using consensus Env sequences from ERVs known to be present in hominoids using a Blast homology search with the aim of characterising env gene changes over time. The retrieved sequences were analysed phylogenetically, and showed that some of the integrations are LTR-env recombinants.

Strengths

The strength of the manuscript is that such an analysis has not been performed yet for the subset of ERV Env genes selected and most of the publicly available primate genomes.

Weaknesses

Unfortunately, the weaknesses of the manuscript outnumber its strengths. Especially the methods section does not contain sufficient information to appreciate or interpret the results. The results section contains methodological information that should be moved, while the presentation of the data is often substandard. For instance, the long lists of genomes in which a certain Env was found could better be shown in tables. Furthermore, there is no overview of the primate genomes, or accession numbers, used. It is unclear whether the analyses, such as the phylogenetic trees, are based on nucleotide or amino acid sequences since this is not stated. tBLASTn was used in the homology searches, so one would suppose aa are retrieved. In the Discussion, both env (nt?) and Env (aa?) are used.

For the non-hominoids, genome assembly of publicly available sequences is not always optimal, and this may require Blasting a second genome from a species. Which should for instance be done for the HML2 sequences found in the Saimiri boliviensis genome, but not in the related Callithrix jacchus genome. Finally, the authors propose to analyse recombination in Env sequences but only retrieve env-LTR recombinant Envs, which should likely not have passed the quality check.

Since the Methods section does not contain sufficient information to understand or reproduce the results, while the Results are described in a messy way, it is unclear whether or not the aims have been achieved. I believe not, as characterisation of env gene changes over time is only shown for a few abberrant integrations containing part of the LTR in the env ORF.

Reviewer #2 (Public review):

Summary:

The manuscript by Chabukswar et al. describes a comprehensive attempt to identify and describe the diversity of retroviral envelope (env) gene sequences present in primate genomes in the form of ancient endogenous retrovirus (ERV) sequences.

Strengths:

The focus on env can be justified because of the role the Env proteins likely played in determining viral tropism and host range of the viruses that gave rise to the ERV insertions, and to a lesser extent, because of the potential for env ORFs to be coopted for cellular functions (in the rare cases where the ORF is still intact and capable of encoding a functional Env protein). In particular, these analyses can reveal the potential roles of recombination in giving rise to novel combinations of env sequences. The authors began by compiling env sequences from the human genome (from human endogenous retrovirus loci, or "HERVs") to build consensus Env protein sequences, and then they use these as queries to screen other primate genomes for group-specific envs by tBLASTn. The "groups" referred to here are previously described, as unofficial classifications of endogenous retrovirus sequences into three very broad categories - Class I, Class II and Class III. These are not yet formally recognized in retroviral taxonomy, but they each comprise representatives of multiple genera, and so would fall somewhere between the Family and Genus levels. The retrieved sequences are subject to various analyses, most notably they are screened for evidence of recombination. The recombinant forms appear to include cases that were probably viral dead-ends (i.e. inactivating the env gene) even if they were propagated in the germline.<br /> The availability of the consensus sequences (supplement) is also potentially useful to others working in this area.

Weaknesses:

The weaknesses are largely in presentation. Discussions of ERVs are always complicated by the lack of a formal and consistent nomenclature and the confusion between ERVs as loci and ERVs as indirect information about the viruses that produced them. For this reason, additional attention needs to be paid to precise wording in the text and/or the use of illustrative figures.

Reviewer #3 (Public review):

Summary:

Retroviruses have been endogenized into the genome of all vertebrate animals. The envelope protein of the virus is not well conserved and acquires many mutations hence can be used to monitor viral evolution. Since they are incorporated into the host genome, they also reflect the evolution of the hosts. In this manuscript the authors have focused their analyses on the env genes of endogenous retroviruses in primates. Important observations made include the extensive recombination events between these retroviruses that were previously unknown and the discovery of HML species in genomes prior to the splitting of old and new world monkeys.

Strengths:

They explored a number of databases and made phylogenetic trees to look at the distribution of retroviral species in primates. The authors provide a strong rationale for their study design, they provide a clear description of the techniques and the bioinformatics tools used.

Weaknesses:

The manuscript is based on bioinformatics analyses only. The reference genomes do not reflect the polymorphisms in humans or other primate species. The analyses thus likely under estimates the amount of diversity in the retroviruses. Further experimental verification will be needed to confirm the observations.<br /> Not sure which databases were used, but if not already analyzed, ERVmap.com and repeatmesker are ones that have many ERVs that are not present in the reference genomes. Also, long range sequencing of the human genome has recently become available which may also be worth studying for this purpose.

eLife Assessment

This study provides a valuable and timely analysis of invasive and non-invasive Streptococcus pyogenes emm89 isolates, which have become a dominant serotype in the past decade. Using genome sequencing of 311 strains from Japan and comparing them with 666 global strains, the authors present compelling evidence in support of the identification of genetic factors linked to the invasive phenotype of emm89. The findings are both theoretically and practically significant in medical microbiology.

Reviewer #1 (Public review):

Summary:

In this study, the authors sequenced emm89 serotype genomes of clinical isolates from patients in Japan, where the number of invasive Group A Streptococcus (GAS), especially those of the emm89 serotype, has drastically increased over the past 10-15 years. The sequences from this cohort were compared against a large collection of publicly available global isolates, yielding a total of almost 1000 genomes in the analysis. Because the researchers focused on the emm89 serotype, they could construct a common core genome, with subsequent ability to analyze genomic differences in accessory genes and intergenic regions that contributed to the invasive phenotype using multiple types of GWAS analysis (SNP, k-mer). Their analysis demonstrates some mutations responsible for invasiveness are specific to the Japanese strains, and that multiple independent virulence factors can contribute to invasiveness. None of the invasive phenotypes were correlated with new gene acquisition. Together, the data support that synergy between bacterial survival and upregulation of virulence factors contributes to the development of severe infection.

Strengths:

• The authors verify their analysis by confirming that covS is one of the more frequently mutated genes in invasive strains of GAS, as has been shown in other publications.

• A mutation in one of the SNPs attributed to invasiveness (SNP fhuB) was introduced into an invasive strain. The authors demonstrate that this mutant strain survives less well in human blood. Therefore, the authors have experimental data to support their claims that their analysis uncovered a new mutation/SNP that contributed to invasiveness.

Weaknesses:

• It would be helpful for the authors to highlight why their technique (large scale analysis of one emm type) can yield more information than a typical GWAS analysis of invasive vs. non-invasive strains. Are SNPs easier to identify using a large-scale core genome? Is it more likely evolutionarily to find mutations in non-coding regions as opposed to the core genome and accessory genes, and this is what this technique allows? Did the analysis yield unexpected genes or new genes that had not been previously identified in other GWAS analyses? These points may need to be made more apparent in the results and deserve some thought in the discussion section.

• The Alpha-fold data does not demonstrate why the mutations the authors identified could contribute to the invasive phenotype. It would be helpful to show an overlay of the predicted structures containing the different SNPs to demonstrate the potential structural differences that can occur due to the SNP. This would make the data more convincing that the SNP has a potential impact on the function of the protein. Similarly, the authors discuss modification of the hydrophobicity of the side chain in the ferrichrome transporter (lines 317-318) due to a SNP, but this is not immediately obvious in the figure (Fig. 5).

Reviewer #2 (Public review):

Summary:

In this manuscript, the authors aim to identify genetic determinants associated with the invasion profile of Streptococcus pyogenes strains of the emm89 type, which has been increasingly linked to invasive infections. The study leverages both in-house sequenced genomes and publicly available genomic data. Several GWAS approaches are applied to these datasets, leading to the identification of potential genetic targets. For these targets, the authors conduct additional analyses, including three-dimensional structural modeling of the encoded proteins, as well as the development of mutant strains. The functional impact of these mutations is further explored through transcriptomic comparisons between the mutants and wild-type strains

Strengths:

The strengths of this manuscript include the large amount of data analyzed and the various methodologies applied. The identification of CovS, a gene known to influence the invasion profile, as a significant variation further validates the methodology employed in this study. Then, the gene fhuD is an intriguing target, identified through both bioinformatics and wet lab approaches.

Weaknesses:

I do not identify any additional weaknesses in the manuscript, beyond those already acknowledged by the authors themselves.

eLife Assessment

This study presents a valuable finding regarding the role of Arp2/3 and the actin nucleators N-WASP and WAVE complexes in myoblast fusion. The data presented is convincing, but it is suggested to perform validation of the knock-down efficiency of the mouse model and making adjustments to some of the data interpretation. The work will be of interest to biologists studying skeletal muscle stem cell biology in the context of skeletal muscle regeneration.

Reviewer #1 (Public review):

Overall, the manuscript reveals the role of actin polymerization to drive the fusion of myoblasts during adult muscle regeneration. This pathway regulates fusion in many contexts, but whether it was conserved in adult muscle regeneration remained unknown. Robust genetic tools and histological analyses were used to support the claims convincingly.

There are a few interpretations that could be adjusted.

The beginning of the results about macrophages traversing ghost fibers after regeneration was a surprise given the context in the abstract and introduction. These results also lead to new questions about this biology that would need to be answered to substantiate the claims in this section. Also, it is unclear the precise new information learned here because it seems obvious that macrophages would need to extravasate the basement membrane to enter ghost fibers and macrophages are known to have this ability. Moreover, the model in Figure 4D has macrophages and BM but there is not even mention of this in the legend. The authors may wish to consider removing this topic from the manuscript.

Which Pax7CreER line was used? In the methods, the Jax number provided is the Gaka line but in the results, Lepper et al 2009 are cited, which is not the citation for the Gaka line.

Did the authors assess regeneration in the floxed mice that do not contain Cre as a control? Or is it known these alleles do not perturb the function of the targeted gene?

The authors comment: 'Interestingly, expression of the fusogenic proteins, MymK and MymX, was up-regulated in the TA muscle of these mice (Fig. S4F), suggesting that fusogen overexpression is not able to rescue the SCM fusion defect resulted from defective branched actin polymerization.' It is unclear if fusogens are truly overexpressed because the analysis is performed at dpi 4 when the expression of fusogens may be decreased in control mice because they have already fused. Also, only two animals were analyzed and it is unclear if MymX is definitively increased. The authors should consider adjusting the interpretation to SCM fusion defect resulting from defective branched actin polymerization is unlikely to be caused by a lack of fusogen expression.

Reviewer #2 (Public review):

To fuse, differentiated muscle cells must rearrange their cytoskeletaon and assemble actin-enriched cytoskeletal structures. These actin foci are proposed to generate mechanical forces necessary to drive close membrane apposition and fusion pore formation.

While the study of these actin-rich structures has been conducted mainly in drosophila, the present manuscript presents clear evidence this mechanism is necessary for the fusion of adult muscle stem cells in vivo, in mice.

However, the authors need to tone down their interpretation of their findings and remember that genetic proof for cytoskeletal actin remodeling to allow muscle fusion in mice has already been provided by different labs (Vasyutina E, et al. 2009 PMID: 19443691; Gruenbaum-Cohen Y, et al., 2012 PMID: 22736793; Hamoud et al., 2014 PMID: 24567399). In the same line of thought, the authors write they "demonstrated a critical function of branched actin-propelled invasive protrusions in skeletal muscle regeneration". I believe this is not a premiere, since Randrianarison-Huetz V, et al., previously reported the existence of finger-like actin-based protrusions at fusion sites in mice myoblasts (PMID: 2926942) and Eigler T, et al., live-recorded said "fusogenic synapse" in mice myoblasts (PMID: 34932950).

Hence, while the data presented here clearly demonstrate that ARP2/3 and SCAR/WAVE complexes are required for differentiating satellite cell fusion into multinucleated myotubes, this is an incremental story, and the authors should put their results in the context of previous literature.

Reviewer #3 (Public review):

The manuscript by Lu et al. explores the role of the Arp2/3 complex and the actin nucleators N-WASP and WAVE in myoblast fusion during muscle regeneration. The results are clear and compelling, effectively supporting the main claims of the study. However, the manuscript could benefit from a more detailed molecular and cellular analysis of the fusion synapse. Additionally, while the description of macrophage extravasation from ghost fibers is intriguing, it seems somewhat disconnected from the primary focus of the work.

Despite this, the data are robust, and the major conclusions are well supported. Understanding muscle fusion mechanism is still a widely unexplored topic in the field and the authors make important progress in this domain.

I have a few suggestions that might strengthen the manuscript as outlined below.

(1) Could the authors provide more detail on how they defined cells with "invasive protrusions" in Figure 4C? Membrane blebs are commonly observed in contacting cells, so it would be important to clarify the criteria used for counting this specific event.

(2) Along the same line, please clarify what each individual dot represents in Figure 4C. The authors mention quantifying approximately 83 SCMs from 20 fibers. I assume each dot corresponds to data from individual fibers, but if that's the case, does this imply that only around four SCMs were quantified per fiber? A more detailed explanation would be helpful.

(3) Localizing ArpC2 at the invasive protrusions would be a strong addition to this study. Furthermore, have the authors examined the localization of Myomaker and Myomixer in ArpC2 mutant cells? This could provide insights into potential disruptions in the fusion machinery.

(4) As a minor curiosity, can ArpC2 WT and mutant cells fuse with each other?

(5) The authors report a strong reduction in CSA at 14 dpi and 28 dpi, attributing this defect primarily to failed myoblast fusion. Although this claim is supported by observations at early time points, I wonder whether the Arp2/3 complex might also play roles in myofibers after fusion. For instance, Arp2/3 could be required for the growth or maintenance of healthy myofibers, which could also contribute to the reduced CSA observed, since regenerated myofibers inherit the ArpC2 knockout from the stem cells. Could the authors address or exclude this possibility? This is rather a broader criticism of how things are being interpreted in general beyond this paper.

Reviewer #1 (Public review):

Summary:

The authors use FIB SEM methods to generate 3D volumes of almost all cells comprising a miniature wasp eye and describe the anatomy of each cell type in detail. The function of each cell type is determined through comparisons with descriptions using other methods from larger insect species.

Strengths:

The data show that, despite the small size, many elements of the eye are consistent with those found in larger insects. In addition, the powerful FIB-SEM technique revealed a hitherto unknown case of ectopic photoreceptors.

Weaknesses:

As this paper only uses anatomical analyses, no functional interpretations of cell function are tested.

The aim of this paper was to describe the ultrastructural organization of compound eyes in the extremely small wasp Megaphragma viggianii. The authors successfully achieved this aim and provided an incredibly detailed description of all cell types with respect to their location, volume, and dimensions. As this is the first of its kind, the results cannot easily be compared with previous work. The findings are likely to be an important reference for future work that uses similar techniques to reconstruct the eyes of other insect species. The FIB-SEM method used is being used increasingly often in structural studies of insect sensory organs and brains and this work demonstrates the utility of this method.

Reviewer #2 (Public review):

Summary:

Makarova et al. provide the first complete cellular-level reconstruction of an insect eye. They use the extremely miniaturized parasitoid wasp, Megaphragma viggiani, and apply improved and optimized volumetric EM methods they can describe, the size, volume, and position of every single cell in the insect compound eye.

This data has previously only been inferred from TEM cross-sections taken in different parts of the eye, but in this study and in the associated 3d datasets video and stacks, one can observe the exact position and orientation in 3D space.

The authors have made a very rigorous effort to describe and assess the variation in each cell type and have also compared two different classes of the dorsal rim and non-dorsal rim ommatidia and the associated visual apparatus for each, confirming previous known findings about the distribution and internal structure that assists in polarization detection in these insects.

Strengths:

The paper is well written and strives to compare the data with previous literature wherever possible and goes beyond cell morphology, calculating the optical properties of the different ommatidia and estimating light sensitivity and spatial resolution limits using rhabdom diameter, focal length and showing how this varies across the eye.

Finally, the authors provide very informative and illustrative videos showing how the cones, lenses, photoreceptors, pigment cells, and even the mitochondria are arranged in 3D space, comparing the structure of the dorsal rim and non-dorsal rim ommatidia. They also describe three 'ectopic' photoreceptors in more anatomical detail providing images and videos of them.

Reviewer #3 (Public review):

Summary:

The article presents a meticulous and quantitative anatomical reconstruction of the compound eye of a tiny wasp at the level of subcellular structures, and cellular and optical organization of the ommatidia and reveals the ectopic photoreceptors, which are decoupled from the eye's dioptrical apparatus.

Strengths:

The graphic material is of very high quality, beautifully organized, and presented in a logical order. The anatomical analysis is fully supported by quantitative numerical data at all scales, from organelles to cells and ommatidia, which should be a valuable source for future studies in cellular biology and visual physiology. The 3D renders are highly informative and a real eye candy.

Weaknesses:

The claim that the large dorsal part of the eye is the dorsal rim area (DRA), supported by anatomical data on rhabdomere geometry and connectomics in authors' earlier work, would eventually greatly benefit from additional evidence, obtained by immunocytochemical staining, that could also reveal a putative substrate for colour vision. The cell nuclei that are located in the optical path in the DRA crystalline cone have only a putative optical function, which may be either similar to pore canals in hymenopteran DRA cornea (scattering) or to photoreceptor nuclei in camera-type eyes (focussing), both explanations being mutually exclusive.

eLife Assessment

This study provides important insights into how cryptic pockets play a role in shaping binding preferences of protein-nucleic acid interactions. By combining biochemical assays and state-of-the-art molecular dynamics simulations, mechanism underlying viral protein 35 (VP35) homologs to bind the backbone of double stranded RNA is presented. The evidence is compelling for molecular determinants that suggest two different dsRNA binding modes for VP35 and also underscores the evolutionary importance of these pockets.

Reviewer #1 (Public review):

Summary:

Mallimadugula et al. combined Molecular Dynamics (MD) simulations, thiol-labeling experiments, and RNA-binding assays to study and compare the RNA-binding behavior of the Interferon Inhibitory Domain (IID) from Viral Protein 35 (VP35) of Zaire ebolavirus, Reston ebolavirus, and Marburg marburgvirus. Although the structures and sequences of these viruses are similar, the authors suggest that differences in RNA binding stem from variations in their intrinsic dynamics, particularly the opening of a cryptic pocket. More precisely, the dynamics of this pocket may influence whether the IID binds to RNA blunt ends or the RNA backbone.

Overall, the authors present important findings to reveal how the intrinsic dynamics of proteins can influence their binding to molecules and, hence, their functions. They have used extensive biased simulations to characterize the opening of a pocket which was not clearly seen in experimental results - at least when the proteins were in their unbound forms. Biochemical assays further validated theoretical results and linked them to RNA binding modes. Thus, with the combination of biochemical assays and state-of-the-art Molecular Dynamics simulations, these results are clearly compelling.

Strengths:

The use of extensive Adaptive Sampling combined with biochemical assays clearly points to the opening of the Interferon Inhibitory Domain (IID) as a factor for RNA binding. This type of approach is especially useful to assess how protein dynamics can affect its function.

Weaknesses :

Although a connection between the cryptic pocket dynamics and RNA binding mode is proposed, the precise molecular mechanism linking pocket opening to RNA binding still remains unclear.

Reviewer #2 (Public review):

Summary:

The authors aimed to determine whether a cryptic pocket in the VP35 protein of Zaire ebolavirus has a functional role in RNA binding and, by extension, in immune evasion. They sought to address whether this pocket could be an effective therapeutic target resistant to evolutionary evasion by studying its role in dsRNA binding among different filovirus VP35 homologs. Through simulations and experiments, they demonstrated that cryptic pocket dynamics modulate the RNA binding modes, directly influencing how VP35 variants block RIG-I and MDA5-mediated immune responses.

The authors successfully achieved their aim, showing that the cryptic pocket is not a random structural feature but rather an allosteric regulator of dsRNA binding. Their results not only explain functional differences in VP35 homologs despite their structural similarity but also suggest that targeting this cryptic pocket may offer a viable strategy for drug development with reduced risk of resistance.

This work represents a significant advance in the field of viral immunoevasion and therapeutic targeting of traditionally "undruggable" protein features. By demonstrating the functional relevance of cryptic pockets, the study challenges long-standing assumptions and provides a compelling basis for exploring new drug discovery strategies targeting these previously overlooked regions.

Strengths:

The combination of molecular simulations and experimental approaches is a major strength, enabling the authors to connect structural dynamics with functional outcomes. The use of homologous VP35 proteins from different filoviruses strengthens the study's generality, and the incorporation of point mutations adds mechanistic depth. Furthermore, the ability to reconcile functional differences that could not be explained by crystal structures alone highlights the utility of dynamic studies in uncovering hidden allosteric features.

Weaknesses:

While the methodology is robust, certain limitations should be acknowledged. For example, the study would benefit from a more detailed quantitative analysis of how specific mutations impact RNA binding and cryptic pocket dynamics, as this could provide greater mechanistic insight. This study would also benefit from providing a clear rationale for the selection of the amber03 force field and considering the inclusion of volume-based approaches for pocket analysis. Such revisions will strengthen the robustness and impact of the study.

Reviewer #3 (Public review):

Summary:

The authors suggest a mechanism that explains the preference of viral protein 35 (VP35) homologs to bind the backbone of double-stranded RNA versus blunt ends. These preferences have a biological impact in terms of the ability of different viruses to escape the immune response of the host.<br /> The proposed mechanism involves the existence of a cryptic pocket, where VP35 binds the blunt ends of dsRNA when the cryptic pocket is closed and preferentially binds the RNA double-stranded backbone when the pocket is open.<br /> The authors performed MD simulation results, thiol labelling experiments, fluorescence polarization assays, as well as point mutations to support their hypothesis.

Strengths:

This is a genuinely interesting scientific question, which is approached through multiple complementary experiments as well as extensive MD simulations. Moreover, structural biology studies focused on RNA-protein interactions are particularly rare, highlighting the importance of further research in this area.

Weaknesses:

- Sequence similarity between Ebola-Zaire (94% similarity) explains their similar behaviour in simulations and experimental assays. Marburg instead is a more distant homolog (~80% similarity relative to Ebola/Zaire). This difference is sequence and structure can explain the propensities, without the need to involve the existence of a cryptic pocket.<br /> - No real evidence for the presence of a cryptic pocket is presented, but rather a distance probability distribution between two residues obtained from extensive MD simulations. It would be interesting to characterise the modelled RNA-protein interface in more detail.

eLife Assessment

This important work substantially advances our understanding of reactive oxygen species (ROS) as a regenerative signal during postnatal cerebellum repair by activating adaptive progenitor reprogramming. The evidence supporting the conclusions is generally compelling, although addressing reviewers' comments would further strengthen the study. This work will be of broad interest to biologists working on stem cells, neurodevelopment and regenerative medicine.

Reviewer #1 (Public review):

Summary:

In this manuscript, Pakula et al. explore the impact of reactive oxygen species (ROS) on neonatal cerebellar regeneration, providing evidence that ROS activates regeneration through Nestin-expressing progenitors (NEPs). Using scRNA-seq analysis of FACS-isolated NEPs, the authors characterize injury-induced changes, including an enrichment in ROS metabolic processes within the cerebellar microenvironment. Biochemical analyses confirm a rapid increase in ROS levels following irradiation, and forced catalase expression, which reduces ROS levels, and impairs external granule layer (EGL) replenishment post-injury.

Strengths:

Overall, the study robustly supports its main conclusion and provides valuable insights into ROS as a regenerative signal in the neonatal cerebellum.

Weaknesses:

Below are specific comments and concerns:

(1) The diversity of cell types recovered from scRNA-seq libraries of sorted Nes-CFP cells is unexpected, especially the inclusion of minor types such as microglia, meninges, and ependymal cells. The authors should validate whether Nes and CFP mRNAs are enriched in the sorted cells; if not, they should discuss the potential pitfalls in sampling bias or artifacts that may have affected the dataset, impacting interpretation.<br /> (2) The authors should de-emphasize that ROS signaling and related gene upregulation exclusively in gliogenic NEPs. Genes such as Cdkn1a, Phlda3, Ass1, and Bax are identified as differentially expressed in neurogenic NEPs and granule cell progenitors (GCPs), with Ass1 absent in GCPs. According to Table S4, gene ontology (GO) terms related to ROS metabolic processes are also enriched in gliogenic NEPs, neurogenic NEPs, and GCPs.<br /> (3) The authors need to justify the selection of only the anterior lobe for EGL replenishment and microglia quantification.<br /> (4) Figure 1K: The figure presents linkages between genes and GO terms as a network but does not depict a gene network. The terminology should be corrected accordingly.<br /> (5) Figure 1H and S2: The x-axis appears to display raw p-values rather than log10(p.value) as indicated. The x-axis should ideally show -log10(p.adjust), beginning at zero. The current format may misleadingly suggest that the ROS GO term has the lowest p-values.<br /> (6) Genes such as Ppara, Egln3, Foxo3, Jun, and Nos1ap were identified by bulk ATAC-seq based on proximity to peaks, not by scRNA-seq. Without additional expression data, caution is needed when presenting these genes as direct evidence of ROS involvement in NEPs.<br /> (7) The authors should annotate cell identities for the different clusters in Table S2.<br /> (8) Reiterative clustering analysis reveals distinct subpopulations among gliogenic and neurogenic NEPs. Could the authors clarify the identities of these subclusters? Can we distinguish the gliogenic NEPs in the Bergmann glia layer from those in the white matter?<br /> (9) In the Methods section, the authors mention filtering out genes with fewer than 10 counts. They should specify if these genes were used as background for enrichment analysis. Background gene selection is critical, as it influences the functional enrichment of gene sets in the list.<br /> (10) Figure S1C: The authors could consider using bar plots to better illustrate cell composition differences across conditions and replicates.<br /> (11) Figures 4-6: It remains unclear how the white matter microglia contribute to the recruitment of BgL-NEPs to the EGL, as the mCAT-mediated microglia loss data are all confined to the white matter.

Reviewer #2 (Public review):

Summary:

The authors have previously shown that the mouse neonatal cerebellum can regenerate damage to granule cell progenitors in the external granular layer, through reprogramming of gliogenic nestin-expressing progenitors (NEPs). The mechanisms of this reprogramming remain largely unknown. Here the authors used scRNAseq and ATACseq of purified neonatal NEPs from P1-P5 and showed that ROS signatures were transiently upregulated in gliogenic NEPs ve neurogenic NEPs 24 hours post injury (P2). To assess the role of ROS, mice transgenic for global catalase activity were assessed to reduce ROS. Inhibition of ROS significantly decreased gliogenic NEP reprogramming and diminished cerebellar growth post-injury. Further, inhibition of microglia across this same time period prevented one of the first steps of repair - the migration of NEPs into the external granule layer. This work is the first demonstration that the tissue microenvironment of the damaged neonatal cerebellum is a major regulator of neonatal cerebellar regeneration. Increased ROS is seen in other CNS damage models including adults, thus there may be some shared mechanisms across age and regions, although interestingly neonatal cerebellar astrocytes do not upregulate GFAP as seen in adult CNS damage models. Another intriguing finding is that global inhibition of ROS did not alter normal cerebellar development.

Strengths:

This paper presents a beautiful example of using single cell data to generate biologically relevant, testable hypotheses of mechanisms driving important biological processes. The scRNAseq and ATACseq analyses are rigorously conducted and conclusive. Data is very clearly presented and easily interpreted supporting the hypothesis next tested by reduce ROS in irradiated brains.

Analysis of whole tissue and FAC sorted NEPS in transgenic mice where human catalase was globally expressed in mitochondria were rigorously controlled and conclusively show that ROS upregulation was indeed decreased post injury and very clearly the regenerative response was inhibited. The authors are to be commended on the very careful analyses which are very well presented and again, easy to follow with all appropriate data shown to support their conclusions.

Weaknesses:

The authors also present data to show that microglia are required for an early step of mobilizing gliogenic NEPs into the damaged EGL. While the data that PLX5622 administration from P0-P5 or even P0-P8 clearly shows that there is an immediate reduction of NEPs mobilized to the damaged EGL, there is no subsequent reduction of cerebellar growth such that by P30, the treated and untreated irradiated cerebella are equivalent in size. There is speculation in the discussion about why this might be the case, but there is no explanation for why further, longer treatment was not attempted nor was there any additional analyses of other regenerative steps in the treated animals. The data still implicate microglia in the neonatal regenerative response, but how remains uncertain.

eLife Assessment

The study provides a valuable analysis of escape from X-inactivation based on three rare female GTEX-donors with non-mosaic X-inactivation. The methods and analyses broadly support the author's claims, although some additional explanation could be helpful. Their data are more comprehensive than those presented previously and add significant weight to evidence for which genes are inactivated or escape from X inactivation in humans. However, without further experimentation the overall study unfortunately remains incomplete in its current form.

Reviewer #1 (Public review):

Summary:

This manuscript investigates genes that escape X-Chromosome Inactivation (XCI) across human tissues, using females that exhibit skewed or non-random XCI. The authors identified 2 female individuals with skewed XCI in the GTex database, in addition to the 1 female skewed sample in this database that has been described in a previous publication (Ref.16). The authors also determined the genes that escape XCI for 380 X-linked genes across 30 different tissues.

Strengths:

The novelty of this manuscript is that the authors have identified the XCI expression status for a total of 380 genes across 30 different human tissues, and also discovered the XCI status (escape, variable escape, or silenced) for 198 X-linked genes, whose status was previously not determined. This report is a good resource for the field of XCI, and would benefit from additional analyses and clarification of their comparisons of XCI status.

Weaknesses:

Specific comments:

(1) The authors state that they have reclassified the allelic expression status of 32 genes (shown in Table S5, Supplementary Figure 3). The concern is the source of the tissue or cell line which was originally used to make the classification of XCI status, and whether the comparisons are equivalent. For example, if cell lines (and not tissues) were used to define the XCI status for EGFL6, TSPAN6, and CXorf38, then how can the authors be sure that the escape status in whole tissues would be the same? Also along these lines, the authors should consider whether escape status in previous studies using immortalized/cancer cell lines (such as the meta analyses done in Balaton publication) would be different compared to healthy tissues (seems like it should be). Therefore making comparisons between healthy whole tissues and cancer cell lines doesn't make sense.

(2) The authors note that skewed XCI is prevalent in the human population, and cite some publications (references 8, 10-12). If RNAseq data is available from these female individuals with skewed XCI (such as ref 12), the authors should consider using their allelic expression pipeline to identify XCI status of more X-linked genes.

(3) It has been well established that the human inactive X has more XCI escape genes compared to the mouse inactive X. In light of the author's observations across human tissues, how does the XCI status compare with the same tissues in mice?

Reviewer #2 (Public review):

Summary:

Gylemo et al. present a manuscript focused on identifying the X-inactivation or X-inactivation escape status for 380 genes across 30 normal human tissues. X-inactivation status of X-linked genes across tissues is important for understanding sex-specific differences in X-linked gene expression and therefore traits, and the likely effect of X-linked pathogenic variants in females. These new data are significant as they double the number of genes that have been classified in the human, and double the number of tissues studied previously.

Strengths:

The strengths of this work are that they analyse 3 individuals from the GTex dataset (2 newly identified, 1 previously identified and published) that have highly/ completely skewed X inactivation, which allows the study of escape from X inactivation in bulk RNA-sequencing. The number of individuals and breadth of tissues analysed add significantly to both the number of genes that have been classified and the weight of evidence for their claims. The additional 198 genes that have been classified and the reclassification of genes that previously had only limited support for their status is useful for the field.

In analysing the data they find that tissue-specific escape from X inactivation appears relatively rare. Rather, if genes escape, even variably, it tends to occur across tissues. Similarly, if a gene is inactivated, it is stable across tissues.

Weaknesses:

In my view there are only minor weaknesses in this work, that tend to come about due to the requirement to study individuals with highly skewed X inactivation. I wonder whether the cause of the highly skewed X inactivation may somehow influence the likelihood of observing tissue-specific escape from X inactivation. In this light, it would be interesting to further understand the genetic cause for the highly skewed X inactivation in each of these three cases in the whole exome sequencing data. Future additional studies may validate these findings using single-cell approaches in unrelated individuals across tissues, where there is normal X inactivation.

Reviewer #3 (Public review):

Summary:

Nestor and colleagues identify genes escaping X chromosome inactivation (XCI) in rare individuals with non-mosaic XCI (nmXCI) whose tissue-specific RNA-seq datasets were obtained from the GTEX database. Because XCI is non-mosaic, read counts representing a second allele are tested for statistically significant escape, in this case > 2.5% of active X expression. Whereas a prior GTEX analysis found only one nmXCI female, this study finds two additional donors in GTEX, therefore expanding the number of assessed X-linked genes to 380. Although this is fewer than half of X-linked genes, the study demonstrates that although rare, nmXCI females are represented in RNA-seq databases such as GTEX. Therefore this analytical approach is worthwhile pursuing in other (larger) databases as well, to provide deeper insight into escape from XCI which is relevant to X-linked diseases and sex differences.

Strengths:

The analysis is well-documented, straightforward, and valuable. The supplementary tables are useful, and the claims in the main text well-supported.

Weaknesses:

There are very few, except that this escape catalogue is limited to 3 donors, based on a single (representative) tissue screen in 285 female donors, mostly using muscle samples. However, if only pituitary samples had been screened, nmXCI-1 would have been missed. Additional donors in the 285 representative samples cross a lower threshold of AE = 0.4. It would be worthwhile to query all tissues of the 285 donors to discover more nmXCI cases, as currently fewer than half of X-linked genes received a call using this very worthwhile approach.

eLife Assessment

This important study reveals a critical role of the transcription factor NR2F2 in mouse fetal Leydig cell (FLC) differentiation. With elegantly carried out experiments, the authors provide compelling evidence that NR2F2 helps to initiate the differentiation of certain interstitial cells into FLC until these cells mature into functional secretory cells that produce androgen and insulin-like peptide 3 (INSL3). The particular importance of the work comes from the fact that NR2F2 affects FLCs without altering paracrine signals known to be involved in FLC differentiation. The work will be of interest to colleagues studying reproductive development in mammals including humans or the biological functions of the nuclear receptor family.

Reviewer #1 (Public review):

Summary<br /> In this beautiful paper the authors examined the role and function of NR2F2 in testis development and more specifically on fetal Leydig cells development. It is well known by now that FLC are developed from an interstitial steroidogenic progenitors at around E12.5 and are crucial for testosterone and INSL3 production during embryonic development, which in turn shapes the internal and external genitalia of the male. Indeed, lack of testosterone or INSL3 are known to cause DSD as well as undescended testis, also termed as cryptorchidism.<br /> The authors first characterized the expression pattern of the NR2R2 protein during testis development and then used two cKO systems of NR2F2, namely the Wt1-creERT2 and the Nr5a1-cre to explore the phenotype of loss of NR2F2. They found in both cases that mice are presenting with undescended testis and major reduction in FLC numbers. They show that NR2F2 has no effect on the amount and expression of the progenitor cells but in its absence, there are less FLC and they are immature.<br /> The effect of NR2F2 is cell autonomous and does not seem to affect other signalling pathways implemented in Leydig cell development as the DHH, PDGFRA and the NOTCH pathway.

Overall, this paper is excellent, very well written, fluent and clear. The data is well presented, and all the controls and statistics are in place. I think this paper will be of great interest to the field and paves the way for several interesting follow up studies as stated in the discussion

Reviewer #2 (Public review):

The major conclusion of the manuscript is expressed in the title: "NR2F2 is required in the embryonic testis for Fetal Leydig Cell development" and also at the end of the introduction and all along the result part. All the authors' assertions are supported by very clear and statistically validated results from ISH, IHC, precise cell counting and gene expression levels by qPCR. The authors used two different conditional Nr2f2 gene ablation systems that demonstrate the same effects at the FLC level. They also showed that the haplo-insufficiency of Wt1 in the first system (knock-in Wt1-cre-ERT2) aggravated the situation in FLC differentiation by disturbing the differentiation of Sertoli cells and their secretion of pro-FLC factors, which had a confounding effect and encouraged them to use the second system. This demonstrates the great rigor with which the authors interpreted the results. In conclusion, all authors' claims and conclusions are justified by their high-quality results.

eLife Assessment

This useful study provides the first assessment of potentially interactive effects of seasonality and blood source on mosquito fitness, together in one study. During revision, the manuscript has been improved, providing additional solid data to support the robustness of observations. However, the discussion still requires further refinement to present the conclusions in manner that is consistent with the data presented. Overall, this interesting study will advance our current understanding of mosquito biology.

Reviewer #1 (Public review):

Summary:

This study examines the role of host blood meal source, temperature, and photoperiod on the reproductive traits of Cx. quinquefasciatus, an important vector of numerous pathogens of medical importance. The host use pattern of Cx. quinquefasciatus is interesting in that it feeds on birds during spring and shifts to feeding on mammals towards fall. Various hypotheses have been proposed to explain the seasonal shift in host use in this species but have provided limited evidence. This study examines whether the shifting of host classes from birds to mammals towards autumn offers any reproductive advantages to Cx. quinquefasciatus in terms of enhanced fecundity, fertility, and hatchability of the offspring. The authors found no evidence of this, suggesting that alternate mechanisms may drive the seasonal shift in host use in Cx. quinquefasciatus.

Strengths:

Host blood meal source, temperature, and photoperiod were all examined together.

Weaknesses:

The study was conducted in laboratory conditions with a local population of Cx. quinquefasciatus from Argentina. I'm not sure if there is any evidence for a seasonal shift in the host use pattern in Cx. quinquefasciatus populations from the southern latitudes.

Comments on the revision:

Overall, the manuscript is much improved. However, the introduction and parts of the discussion that talk about addressing the question of seasonal shift in host use pattern of Cx. quin are still way too strong and must be toned down. There is no strong evidence to show this host shift in Argentinian mosquito populations. Therefore, it is just misleading. I suggest removing all this and sticking to discussing only the effects of blood meal source and seasonality on the reproductive outcomes of Cx. quin.

Reviewer #2 (Public review):

Summary:

Conceptually, this study is interesting and is the first attempt to account for the potentially interactive effects of seasonality and blood source on mosquito fitness, which the authors frame as a possible explanation for previously observed host-switching of Culex quinquefasciatus from birds to mammals in the fall. The authors hypothesize that if changes in fitness by blood source change between seasons, higher fitness on birds in the summer and on mammals in the autumn could drive observed host switching. To test this, the authors fed individuals from a colony of Cx. quinquefasciatus on chickens (bird model) and mice (mammal model) and subjected each of these two groups to two different environmental conditions reflecting the high and low temperatures and photoperiod experienced in summer and autumn in Córdoba, Argentina (aka seasonality). They measured fecundity, fertility, and hatchability over two gonotrophic cycles. The authors then used generalized linear mixed models to evaluate the impact of host species, seasonality, and gonotrophic cycle on fecundity, fertility, and hatchability. The authors were trying to test their hypothesis by determining whether there was an interactive effect of season and host species on mosquito fitness. This is an interesting hypothesis; if it had been supported, it would provide support for a new mechanism driving host switching. While the authors did report an interactive impact of seasonality and host species, the directionality of the effect was the opposite from that hypothesized. The authors have done a very good job of addressing many of the reviewer's concerns, especially by adding two additional replicates. Several minor concerns remain, especially regarding unclear statements in the discussion.

Strengths:

(1) Using a combination of laboratory feedings and incubators to simulate seasonal environmental conditions is a good, controlled way to assess the potentially interactive impact of host species and seasonality on the fitness of Culex quinquefasciatus in the lab.<br /> (2) The driving hypothesis is an interesting and creative way to think about a potential driver of host switching observed in the field.

Weaknesses:

(1) The methods would be improved by some additional details. For example, clarifying the number of generations for which mosquitoes were maintained in colony (which was changed from 20 to several) and whether replicates were conducted at different time points.<br /> (2) The statistical analysis requires some additional explanation. For example, you suggest that the power analysis was conducted a priori, but this was not mentioned in your first two drafts, so I wonder if it was actually conducted after the first replicate. It would be helpful to include further detail, such as how the parameters were estimated. Also, it would be helpful to clarify why replicate was included as a random effect for fecundity and fertility but as a fixed effect for hatchability. This might explain why there were no significant differences for hatchability given that you were estimating for more parameters.<br /> (3) A number of statements in the discussion are not clear. For example, what do you mean by a mixed perspective in the first paragraph? Also, why is the expectation mentioned in the second paragraph different from the hypothesis you described in your introduction?<br /> (4) According to eLife policy, data must be made freely available (not just upon request).

Author response:

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

We have carefully addressed all the reviewers' suggestions, and detailed responses are provided at the end of this letter. In summary:

• We conducted two additional replicates of the study to obtain more robust and reliable data.

• The Introduction has been revised for greater clarity and conciseness.

• The Results section was shortened and reorganized to highlight the key findings more effectively.

• The Discussion was modified according to the reviewers' suggestions, with a focus on reorganization and conciseness.

We hope you find this revised version of the manuscript satisfactory.

Reviewer #1 (Public Review):

Summary:

This study examines the role of host blood meal source, temperature, and photoperiod on the reproductive traits of Cx. quinquefasciatus, an important vector of numerous pathogens of medical importance. The host use pattern of Cx. quinquefasciatus is interesting in that it feeds on birds during spring and shifts to feeding on mammals towards fall. Various hypotheses have been proposed to explain the seasonal shift in host use in this species but have provided limited evidence. This study examines whether the shifting of host classes from birds to mammals towards autumn offers any reproductive advantages to Cx. quinquefasciatus in terms of enhanced fecundity, fertility, and hatchability of the offspring. The authors found no evidence of this, suggesting that alternate mechanisms may drive the seasonal shift in host use in Cx. quinquefasciatus.

Strengths:

Host blood meal source, temperature, and photoperiod were all examined together.

Weaknesses:

The study was conducted in laboratory conditions with a local population of Cx. quinquefasciatus from Argentina. I'm not sure if there is any evidence for a seasonal shift in the host use pattern in Cx. quinquefasciatus populations from the southern latitudes.

Comments on the revision: 

Overall, I am not quite convinced about the possible shift in host use in the Argentinian populations of Cx. quinquefasciatus. The evidence from the papers that the authors cite is not strong enough to derive this conclusion. Therefore, I think that the introduction and discussion parts where they talk about host shift in Cx. quinquefasciatus should be removed completely as it misleads the readers. I suggest limiting the manuscript to talking only about the effects of blood meal source and seasonality on the reproductive outcomes of Cx. quinquefasciatus. 

As mentioned in the previous revision, we agree on the reviewer observation about the lack of evidence on seasonal shift in the host use pattern in Cx. quinquefasciatus populations from Argentina. We include this topic in the discussion.

Additionally, we also added a paragraph in the discussion section to include the limitations of our study and conclusions. One of them is the fact that our results are based on controlled conditions experiments. Future studies are needed to elucidate if the same trend is found in the field.

Reviewer #1 (Recommendations for the authors): 

Abstract

Line 73: shift in feeding behavior

Accepted as suggested. 

Discussion

Line 258: addressed that Accepted as suggested.

Line 263: blood is nutritionally richer

Accepted as suggested.

Reviewer #2 (Public Review): 

Summary:

Conceptually, this study is interesting and is the first attempt to account for the potentially interactive effects of seasonality and blood source on mosquito fitness, which the authors frame as a possible explanation for previously observed host-switching of Culex quinquefasciatus from birds to mammals in the fall. The authors hypothesize that if changes in fitness by blood source change between seasons, higher fitness on birds in the summer and on mammals in the autumn could drive observed host switching. To test this, the authors fed individuals from a colony of Cx. quinquefasciatus on chickens (bird model) and mice (mammal model) and subjected each of these two groups to two different environmental conditions reflecting the high and low temperatures and photoperiod experienced in summer and autumn in Córdoba, Argentina (aka seasonality). They measured fecundity, fertility, and hatchability over two gonotrophic cycles. The authors then used a generalized linear model to evaluate the impact of host species, seasonality, and gonotrophic cycle on fecundity, fertility, and hatchability. The authors were trying to test their hypothesis by determining whether there was an interactive effect of season and host species on mosquito fitness. This is an interesting hypothesis; if it had been supported, it would provide support for a new mechanism driving host switching. While the authors did report an interactive impact of seasonality and host species, the directionality of the effect was the opposite from that hypothesized. The authors have done a very good job of addressing many of the reviewer concerns, with several exception that continue to cause concern about the conclusions of the study. 

Strengths:

(1) Using a combination of laboratory feedings and incubators to simulate seasonal environmental conditions is a good, controlled way to assess the potentially interactive impact of host species and seasonality on the fitness of Culex quinquefasciatus in the lab.

(2) The driving hypothesis is an interesting and creative way to think about a potential driver of host switching observed in the field. 

(3) The manuscript has become a lot clearer and easier to read with the revisions - thank you to the authors for working hard to make many of the suggested changes. 

Weaknesses:

(1) The authors have decided not to follow the suggestion of conducting experimental replicates of the study. This is understandable given the significant investment of resources and time necessary, however, it leaves the study lacking support. Experimental replication is an important feature of a strong study and helps to provide confidence that the observed patterns are real and replicable. Without replication, I continue to lack confidence in the conclusions of the study. 

We included replicates as suggested.  

(2) The authors have included some additional discussion about the counterintuitive nature of their results, but the paragraph discussing this in the discussion was confusing. I believe that this should be revised. This is a key point of the paper and needs to be clear to the reader.

Revised as suggested. 

(3) There should be more discussion of the host switching observed in the two studies conducted in Argentina referenced by the authors. Since host switching is the foundation for the hypothesis tested in this paper, it is important to fully explain what is currently known in Argentina. 

Accepted as suggested.

(4) In some cases, the explanations of referenced papers are not entirely accurate. For example, when referencing Erram et al 2022, I think the authors misrepresented the paper's discussion regarding pre-diuresis- Erram et al. are suggesting that pre-diuresis might be the mechanism by which C. furens compensates for the lower nutritional value of avian blood, leading to no significant difference between avian/mammal blood on fecundity/fertility (rather than leading to higher fecundity on birds, as stated in this manuscript). The study performed by Erram et al. also didn't prove this phenomenon, they just suggest it as a possible mechanism to explain their results, so that should be made clear when referencing the paper. 

Changed as suggested.

(5) In some cases, the conclusions continue to be too strongly worded for the evidence available. For example, lines 322-324: I don't think the data is sufficient to conclude that a different physiological state is induced, nor that they are required to feed on a blood source that results in higher fitness. 

Redaction was modified as suggested to tight our discussion with results.

(6) There is limited mention of the caveat that this experiment performed with simulated seasonality that does not perfectly replicate seasonality in the field. I think this caveat should be discussed in the discussion (e.g. that humidity is held constant).

This topic is now included in the discussion as suggested. 

Reviewer #2 (Recommendations for the authors): 

59-60: These terms should end with -phagic instead of -philic. These papers study blood feeding patterns, not preference. I understand that the Janssen papers calls it "mammalophilic" in their title, but this was an incorrect use of the term in their paper. There are some review papers that explain the difference in this terminology if it's helpful.

Accepted as suggested. 

73: edit to "in" feeding behavior 

Accepted as suggested.

77-78: Given that the premise of your study is based on the phenomenon of host switching, I suggest that you expand your discussion of these two papers. What did they observe? Which hosts did they switch from / to and how dramatic was the shift?

Accepted as suggested. 

79: replace acknowledged with experienced 

Accepted as suggested.

79-80: the way that this is written is misleading. It suggests that Spinsanti showed that seasonal variation in SLEV could be attributed to a host shift, which isn't true. This citation should come before the comma and then you should use more cautious language in the second half. E.g which MIGHT be possible to attribute to .... 

Accepted as suggested.

80-82: this is not convincing. Even if the Robin isn't in Argentina, Argentina does have migrating birds, so couldn't this be the case for other species of birds? Do any of the birds observed in previous blood meal analyses in Argentina migrate? If so, couldn't this hypothesis indeed play a role? 

A paragraph about this topic was added to the discussion as suggested.

90: hypotheses for what? The fall peak in cases? Or host switching? 

Changed to be clearer.

98: where was this mentioned before? I think "as mentioned before" can be removed. 

Accepted as suggested.

101: edit to "whether an interaction effect exists" 

Accepted as suggested.

104: edit to "We hypothesize that..." 

Accepted as suggested.

106: reported host USE changes, not host PREFERENCE changes, right? 

All the terminology was change to host pattern and not preference to avoid confusion.

200: Briefly reading Carsey and Harden, it looks like the methodology was developed for social science. Is there anything you can cite to show this applied to other types of data? If not, I think this requires more explanation in your MS. 

This was removed as replicates were included.

237-239: I think it is best not to make a definitive statement about greater/higher if it isn't statistically significant; I suggest modifying the sentences to state that the differences you are listing were not significantly different up front rather than at the end, otherwise if people aren't reading carefully, they may get the wrong impression. 

Accepted as suggested.

245: you only use the term MS-I once before and I forgot what it meant since it wasn't repeated, so I had to search back through with command-F. I suggest writing this out rather than using the acronym. 

Accepted as suggested.

249: edit to: "an interaction exists between the effect of..." 

Accepted as suggested.

253-254: greater compared to what? 

Change for clearness. 258-260: edit for grammar 

Accepted as suggested.

260-262: edit for grammar; e.g. "However, this assumption lacks solid evidence; there is a scarcity of studies regarding nutritional quality of avian blood and its impact on mosquito fitness." 

Accepted as suggested.

263: edit: blood is nutritionally... 

Accepted as suggested.

264-267: This doesn't sound like an accurate interpretation of what the paper suggests regarding pre-diuresis in their discussion - they are suggesting that pre-diuresis might be the mechanism by which C. furens compensates for the lower nutritional value of avian blood, leading to no significant difference between avian/mammal blood on fecundity/fertility. They also don't show this, they just suggest it as a possible mechanism to explain their results. 

This topic was removed given the restructuring of discussion.

253-269: You should tie this paragraph back to your results to explicitly compare/contrast your findings with the previous literature. 

Accepted as suggested.

270-282: This paragraph would be a good place to explain the caveat of working in the laboratory - for example, humidity was the same across the two seasons which I'm guessing isn't the case in the field in Argentina. You can discuss what aspects of laboratory season simulation do not accurately replicate field conditions and how this can impact your findings. You said in your response to the reviewers that you weren't interested in measuring other variables (which is fair, and not expected!), but the beauty of the discussion section is to be able to think about how your experimental design might impact your results - one possibility is that your season simulation may not have produced the results produced by true seasonal shifts. 

Accepted as suggested.

279-281: You say your experiment was conducted within the optimal range, which would suggest that both summer and autumn were within that range, but then you only talk about summer as optimal in the following sentence. 

Changed for clearness.

281-282: You should clarify this sentence - state what the interaction has an effect on. 

Accepted as suggested.

283-291: I appreciate that your discussion now acknowledges the small sample size and the questions that remain unanswered due to the results being opposite to that of the hypothesis, but this paragraph lacks some details and in places doesn't make sense. 

I think you need to emphasize which groups had small sample size and which conclusions that might impact. I also think you need to explain why the sample size was substantially smaller for some groups (e.g. did they refuse to feed on the mouse in the autumn?). I appreciate that sample sizes are hard to keep high across many groups and two gonotrophic periods, but unfortunately, that is why fitness experiments are so hard to do and by their nature, take a long time. I understand that other papers have even lower sample size, but I was not asked to review those papers and would have had the same critique of them. I don't believe that creating simulated data via a Monte Carlo approach can make up for generating real data. As I understand it from your explanation, you are parametrizing the Monte Carlo simulations with your original data, which was small to begin with for autumn mouse. Using this simulation doesn't seem like a satisfactory replacement for an experimental replicate in my opinion. I maintain that at least a second replicate is necessary to see whether the patterns that you have observed hold. 

The performing of a power analysis and addition of more replicates tried to solve the issue of sample size. More about this critic is added in the discussion. The simulation approach was totally removed.

Regarding the directionality of the interaction effect, I think this warrants more discussion. Lines 287-291 don't make sense to me. You suggest that feeding on birds in the autumn may confer a reproductive advantage when conditions are more challenging. But then why wouldn't they preferentially feed on birds in the autumn, rather than mammals? I suggest rewriting this paragraph to make it clearer. 

Accepted as suggested.

297: earlier mentioned treatments? Do you mean compared to the first gonotrophic cycle? This isn't clear. 

Changed for clearness.

302-303: Did you clarify whether you are allowed to reference unpublished data in eLife? 

This was removed to follow the guidelines of eLife.

316-317: "it becomes apparent" sounds awkward, I suggest rewording and also explaining how this conclusion was made. 

Accepted as suggested.

322-324: I think that this statement is too strongly worded. I don't think your data is sufficient to conclude that a different physiological state is induced, nor that they are required to feed on a blood source that results in higher fitness. Please modify this and make your conclusions more cautious and closely linked to what you actually demonstrated. 

Accepted as suggested.

325: change will perform to would have 

Accepted as suggested.

326: add to the sentence: "and vice versa in the summer" 

Accepted as suggested.

330: possible explanations, not explaining scenarios. 

Accepted as suggested.

517: I think you should repeat the abbreviation definitions in the caption to make it easier for readers, otherwise they have to flip back and forth which can be difficult depending on formatting.

Accepted as suggested. 

In general, I think that your captions need more information. I think the best captions explain the figure relatively thoroughly such that the reader can look at the figure and caption and understand without reading the paper in depth. (e.g. the statistical test used).

Data availability: The eLife author instructions do say that data must be made available, so there should be a statement on data availability in your MS. I also suggest you make the code available.

Accepted as suggested.

eLife Assessment

This useful study presents a genetically encoded barcoding system that could advance transcriptomic studies and that has the potential for further applications, such as in high-throughput population-scale behavioral measurements. The evidence supporting the claims of the authors is solid and highlights both the usefulness and the limitations of the approach.

Reviewer #1 (Public review):

The aim of this paper is to describe a novel method for genetic labelling of animals or cell populations, using a system of DNA/RNA barcodes.

Strengths:

• The author's attempt at providing a straightforward method for multiplexing Drosophila samples prior to scRNA-seq is commendable. The perspective of being able to load multiple samples on a 10X Chromium without antibody labelling is appealing.<br /> • The authors are generally honest about potential issues in their method, and areas that would benefit from future improvement.<br /> • The article reads well. Graphs and figures are clear and easy to understand.

Weaknesses:

• The usefulness of TaG-EM for phototaxis, egg laying or fecundity experiments is questionable. The behaviours presented here are all easily quantifiable, either manually or using automated image-based quantification, even when they include a relatively large number of groups and replicates. Despite their claims (e.g., L311-313), the authors do not present any real evidence about the cost- or time-effectiveness of their method in comparison to existing quantification methods.<br /> • Behavioural assays presented in this article have clear outcomes, with large effect sizes, and therefore do not really challenge the efficiency of TaG-EM. By showing a T-maze in Fig 1B, the authors suggest that their method could be used to quantify more complex behaviours. Not exploring this possibility in this manuscript seems like a missed opportunity.<br /> • Experiments in Figs S3 and S6 suggest that some tags have a detrimental effect on certain behaviours or on GFP expression. Whereas the authors rightly acknowledge these issues, they do not investigate their causes. Unfortunately, this question the overall suitability of TaG-EM, as other barcodes may also affect certain aspects of the animal's physiology or behaviour. Revising barcode design will be crucial to make sure that sequences with potential regulatory function are excluded.<br /> • For their single-cell experiments, the authors have used the 10X Genomics method, which relies on sequencing just a short segment of each transcript (usually 50-250bp - unknown for this study as read length information was not provided) to enable its identification, with the matching paired-end read providing cell barcode and UMI information (Macosko et al., 2015). With average fragment length after tagmentation usually ranging from 300-700bp, a large number of GFP reads will likely not include the 14bp TaG-EM barcode. When a given cell barcode is not associated with any TaG-EM barcode, then demultiplexing is impossible. This is a major problem, which is particularly visible in Figs 5 and S13. In 5F, BC4 is only detected in a couple of dozen cells, even though the Jon99Ciii marker of enterocytes is present in a much larger population (Fig 5C). Therefore, in this particular case, TaG-EM fails to detect most of the GFP-expressing cells. Similarly, in S13, most cells should express one of the four barcodes, however many of them (maybe up to half - this should be quantified) do not. Therefore, the claim (L277-278) that "the pan-midgut driver were broadly distributed across the cell clusters" is misleading. Moreover, the hypothesis that "low expressing driver lines may result in particularly sparse labelling" (L331-333) is at least partially wrong, as Fig S13 shows that the same Gal4 driver can lead to very different levels of barcode coverage.<br /> • Comparisons between TaG-EM and other, simpler methods for labelling individual cell populations are missing. For example, how would TaG-EM compare with expression of different fluorescent reporters, or a strategy based on the brainbow/flybow principle?<br /> • FACS data is missing throughout the paper. The authors should include data from their comparative flow cytometry experiment of TaG-EM cells with or without additional hexameric GFP, as well as FSC/SSC and fluorescence scatter plots for the FACS steps that they performed prior to scRNA-seq, at least in supplementary figures.<br /> • The authors should show the whole data described in L229, including the cluster that they chose to delete. At least, they should provide more information about how many cells were removed. In any case, the fact that their data still contains a large number of debris and dead cells despite sorting out PI negative cells with FACS and filtering low abundance barcodes with Cellranger is concerning.

Overall, although a method for genetic tagging cell populations prior to multiplexing in single-cell experiments would be extremely useful, the method presented here is inadequate. However, despite all the weaknesses listed above, the idea of barcodes expressed specifically in cells of interest deserves more consideration. If the authors manage to improve their design to resolve the major issues and demonstrate the benefits of their method more clearly, then TaG-EM could become an interesting option for certain applications.

Comments on revisions:

The authors have addressed many important points, providing reassurances about the initial weaknesses of their work. Although the TaG-EM is unlikely to have a significant influence on the field due to its limited benefits, the results are now sound and provide the reader with an unbiased view of the possibilities and limitations of the method.

Reviewer #2 (Public review):

The authors developed the TaG-EM system to address challenges in multiplexing Drosophila samples for behavioral and transcriptomic studies. This system integrates DNA barcodes upstream of the polyadenylation site in a UAS-GFP construct, enabling pooled behavioral measurements and cell type tracking in scRNA-seq experiments. The revised manuscript expands on the utility of TaG-EM by demonstrating its application to complex assays, such as larval gut motility, and provides a refined analysis of its limitations and cost-effectiveness.

Strengths

(1) Novelty and Scope: The study demonstrates the potential for TaG-EM to streamline multiplexing in both behavioral and transcriptomic contexts. The additional application to labor-intensive larval gut motility assays highlights its scalability and practical utility.

(2) Data Quality and Clarity: Figures and supplemental data are mostly clear and significantly enhanced in the revised manuscript. The addition of Supplemental Figures 18-21 addresses initial concerns about scRNA-seq data and driver characterization.

(3) Cost-Effectiveness Analysis: New analyses of labor and cost savings (e.g., Supplemental Figure 8) provide a practical perspective.

(4) Improvements in Barcode Detection and Analysis: Enhanced enrichment protocols (Supplemental Figures 18-19) demonstrate progress in addressing limitations of barcode detection and increase the detection rate of labeled cells.

Weaknesses

(1) Barcode Detection Efficiency: While improvements are noted, the low barcode detection rate (~37% in optimized conditions) limits the method's scalability in some applications, such as single-cell sequencing experiments with complex cell populations.

(2) Sparse Labeling: Sparse labeling of cell populations, particularly in scRNA-seq assays, remains a concern. Variability in driver strength and regional expression introduces inconsistencies in labeling density.

(3) Behavioral Applications: The utility of TaG-EM in quantifying more complex behaviors remains underexplored, limiting the generalizability of the method beyond simpler assays like phototaxis and oviposition.

(4) Driver Line Characterization: While improvements in driver line characterization were made, variability in expression patterns and sparse labeling emphasize the need for further refinement of constructs and systematic backcrossing to standardize the genetic background.

Author response:

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

Public Reviews:

Reviewer #1 (Public Review):

The aim of this paper is to describe a novel method for genetic labelling of animals or cell populations, using a system of DNA/RNA barcodes.

Strengths:

• The author's attempt at providing a straightforward method for multiplexing Drosophila samples prior to scRNA-seq is commendable. The perspective of being able to load multiple samples on a 10X Chromium without antibody labelling is appealing.

• The authors are generally honest about potential issues in their method, and areas that would benefit from future improvement.

• The article reads well. Graphs and figures are clear and easy to understand.

We thank the reviewer for these positive comments.

Weaknesses:

• The usefulness of TaG-EM for phototaxis, egg laying or fecundity experiments is questionable. The behaviours presented here are all easily quantifiable, either manually or using automated image-based quantification, even when they include a relatively large number of groups and replicates. Despite their claims (e.g., L311-313), the authors do not present any real evidence about the cost- or time-effectiveness of their method in comparison to existing quantification methods.

While the behaviors that were quantified in the original manuscript were indeed relatively easy to quantify through other methods, they nonetheless demonstrated that sequencing-based TaG-EM measurements faithfully recapitulated manual behavioral measurements. In response to the reviewer’s comment, we have added additional experiments that demonstrate the utility of TaG-EM-based behavioral quantification in the context of a more labor-intensive phenotypic assay (measuring gut motility via food transit times in Drosophila larvae, Figure 4, Supplemental Figure 7). We found that food transit times in the presence and absence of caffeine are subtly different and that, as with larger effect size behaviors, TaG-EM data recapitulates the results of the manual assay. This experiment demonstrates both that TaG-EM can be used to streamline labor-intensive behavioral assays (we have included an estimate of the savings in hands-on labor for this assay by using a multiplexed sequencing approach, Supplemental Figure 8) and that TaG-EM can quantify small differences between experimental groups. We also note in the discussion that an additional benefit of TaGEM-based behavioral assays is that the observed is blinded as to the experimental conditions as they are intermingled in a single multiplexed assay. We have added the following text to the paper describing these experiments.

Results:

“Quantifying food transit time in the larval gut using TaG-EM

Gut motility defects underlie a number of functional gastrointestinal disorders in humans (Keller et al., 2018). To study gut motility in Drosophila, we have developed an assay based on the time it takes a food bolus to transit the larval gut (Figure 4A), similar to approaches that have been employed for studying the role of the microbiome in human gut motility (Asnicar et al., 2021). Third instar larvae were starved for 90 minutes and then fed food containing a blue dye. After 60 minutes, larvae in which a blue bolus of food was visible were transferred to plates containing non-dyed food, and food transit (indicated by loss of the blue food bolus) was scored every 30 minutes for five hours (Supplemental Figure 7). 

Because this assay is highly labor-intensive and requires hands-on effort for the entire five-hour observation period, there is a limit on how many conditions or replicates can be scored in one session (~8 plates maximum). Thus, we decided to test whether food transit could be quantified in a more streamlined and scalable fashion by using TaG-EM (Figure 4B). Using the manual assay, we observed that while caffeinecontaining food is aversive to larvae, the presence of caffeine reduces transit time through the gut (Figure 4C, Supplemental Figure 7). This is consistent with previous observations in adult flies that bitter compounds (including caffeine) activate enteric neurons via serotonin-mediated signaling and promote gut motility (Yao and Scott, 2022). We tested whether TaG-EM could be used to measure the effect of caffeine on food transit time in larvae. As with prior behavioral tests, the TaG-EM data recapitulated the results seen in the manual assay (Figure 4D). Conducting the transit assay via TaGEM enables several labor-saving steps. First, rather than counting the number of larvae with and without a food bolus at each time point, one simply needs to transfer nonbolus-containing larvae to a collection tube. Second, because the TaG-EM lines are genetically barcoded, all the conditions can be tested at once on a single plate, removing the need to separately count each replicate of each experimental condition. This reduces the hands-on time for the assay to just a few minutes per hour.  A summary of the anticipated cost and labor savings for the TaG-EM-based food transit assay is shown in Supplemental Figure 8.”

Discussion:

“While the utility of TaG-EM barcode-based quantification will vary based on the number of conditions being analyzed and the ease of quantifying the behavior or phenotype by other means, we demonstrate that TaG-EM can be employed to cost-effectively streamline labor-intensive assays and to quantify phenotypes with small effect sizes (Figure 4, Supplemental Figure 8). An additional benefit of multiplexed TaG-EM behavioral measurements is that the experimental conditions are effectively blinded as the multiplexed conditions are intermingled in a single assay.”

Methods:

“Larval gut motility experiments

Preparing Yeast Food Plates

Yeast agar plates were prepared by making a solution containing 20% Red Star Active Dry Yeast 32oz (Red Star Yeast) and 2.4% Agar Powder/Flakes (Fisher) and a separate solution containing 20% Glucose (Sigma-Aldrich). Both mixtures were autoclaved with a 45-minute liquid cycle and then transferred to a water bath at 55ºC. After cooling to 55ºC, the solutions were combined and mixed, and approximately 5 mL of the combined solution was transferred into 100 x 15 mm petri dishes (VWR) in a PCR hood or contamination-free area. For blue-dyed yeast food plates, 0.4% Blue Food Color (McCormick) was added to the yeast solution. For the caffeine assays, 300 µL of a solution of 100 mM 99% pure caffeine (Sigma-Aldrich) was pipetted onto the blue-dyed yeast plate and allowed to absorb into the food during the 90-minute starvation period.

Manual Gut Motility Assay

Third instar Drosophila larvae were transferred to empty conical tubes that had been misted with water to prevent the larvae from drying out. After a 90-minute starvation period the larvae were moved from the conical to a blue-dyed yeast plate with or without caffeine and allowed to feed for 60 minutes. Following the feeding period, the larvae were transferred to an undyed yeast plate. Larvae were scored for the presence or absence of a food bolus every 30 minutes over a 5-hour period. Up to 8 experimental replicates/conditions were scored simultaneously. 

TaG-EM Gut Motility Assay

Third instar larvae were starved and fed blue dye-containing food with or without caffeine as described above. An equal number of larvae from each experimental condition/replicate were transferred to an undyed yeast plate. During the 5-hour observation period, larvae were examined every 30 minutes and larvae lacking a food bolus were transferred to a microcentrifuge tube labeled for the timepoint. Any larvae that died during the experiment were placed in a separate microcentrifuge tube and any larvae that failed to pass the food bolus were transferred to a microcentrifuge tube at the end of the experiment. DNA was extracted from the larvae in each tube and TaG-EM barcode libraries were prepared and sequenced as described above.”

• Behavioural assays presented in this article have clear outcomes, with large effect sizes, and therefore do not really challenge the efficiency of TaG-EM. By showing a Tmaze in Fig 1B, the authors suggest that their method could be used to quantify more complex behaviours. Not exploring this possibility in this manuscript seems like a missed opportunity.

See the response to the previous point.

• Experiments in Figs S3 and S6 suggest that some tags have a detrimental effect on certain behaviours or on GFP expression. Whereas the authors rightly acknowledge these issues, they do not investigate their causes. Unfortunately, this question the overall suitability of TaG-EM, as other barcodes may also affect certain aspects of the animal's physiology or behaviour. Revising barcode design will be crucial to make sure that sequences with potential regulatory function are excluded.

We have determined that the barcode (BC#8) that had no detectable Gal4induced gene expression in Figure S6 (now Supplemental Figure 9) has a deletion in the GFP coding region that ablates GFP function. Interestingly, the expressed TaG-EM barcode transcript is still detectable in single cell sequencing experiments, but obviously this line cannot be used for cell enrichment (at least based solely on GFP expression from the TaG-EM construct). While it is unclear how this line came to have a lesion in the GFP gene, we have subsequently generated >150 additional TaG-EM stocks and we have tested the GFP expression of these newly established stocks by crossing them to Mhc-Gal4. All of the additional stocks had GFP expression in the expected pattern, indicating that the BC#8 construct is an outlier with respect to inducibility of GFP. We have added the following text to the results section to address this point:

“No GFP expression was visible for TaG-EM barcode number 8, which upon molecular characterization had an 853 bp deletion within the GFP coding region (data not shown). We generated and tested GFP expression of an additional 156 TaG-EM barcode lines (Alegria et al., 2024), by crossing them to Mhc-Gal4 and observing expression in the adult thorax. All 156 additional TaG-EM lines had robust GFP expression (data not shown).”

It is certainly the case that future improvements to the construct design may be necessary or desirable and that back-crossing could likely be used to alleviate line-toline differences for specific phenotypes, we also address this point in the discussion with the following text:

“We excluded this poor performing barcode line from the fecundity tests, however, backcrossing is often used to bring reagents into a consistent genetic background for behavioral experiments and could also potentially be used to address behavior-specific issues with specific TaG-EM lines. In addition, other strategies such as averaging across multiple barcode lines or permutation of barcode assignment across replicates could also mitigate such deficiencies.”

• For their single-cell experiments, the authors have used the 10X Genomics method, which relies on sequencing just a short segment of each transcript (usually 50-250bp - unknown for this study as read length information was not provided) to enable its identification, with the matching paired-end read providing cell barcode and UMI information (Macosko et al., 2015). With average fragment length after tagmentation usually ranging from 300-700bp, a large number of GFP reads will likely not include the 14bp TaG-EM barcode. 

The 10x Genomics 3’ workflows that were used for sequencing TaG-EM samples reads the cell barcode and UMI in read one and the expressed RNA sequence in read two. We sequenced the samples shown in Figure 5 in the initial manuscript using a run configuration that generated 150 bp for read two. The TaG-EM barcodes are located just upstream of the poly-adenylation sites (based on the sequencing data, we observe two different poly-A sites and the TaG-EM barcode is located 35 and 60 bp upstream of these sites). Based on the location of the TaG-EM barcodes,150 bp reads is sufficient to see the barcode in any GFP-associated read (when using the 3’ gene expression workflow). In addition to detecting the expression of the TaG-EM barcodes in the 10x Genomics gene expression library, it is possible to make a separate library that enriches the barcode sequence (similar to hashtag or CITE-Seq feature barcode libraries). We have added experimental data where we successfully performed an enrichment of the TaG-EM barcodes and sequenced this as a separate hashtag library (Supplemental Figure 18). We have added text to the results describing this work and also included a detailed information in the methods for performing TaG-EM barcode enrichment during 10x library prep. 

Results:

“In antibody-conjugated oligo cell hashing approaches, sparsity of barcode representation is overcome by spiking in an additional primer at the cDNA amplification step and amplifying the hashtag oligo by PCR. We employed a similar approach to attempt to enrich for TaG-EM barcodes in an additional library sequenced separately from the 10x Genomics gene expression library. Our initial attempts at barcode enrichment using spike-in and enrichment primers corresponding to the TaG-EM PCR handle were unsuccessful (Supplemental Figure 18). However, we subsequently optimized the TaG-EM barcode enrichment by 1) using a longer spike-in primer that more closely matches the annealing temperature used during the 10x Genomics cDNA creation step, and 2) using a nested PCR approach to amplify the cell-barcode and unique molecular identifier (UMI)-labeled TaG-EM barcodes (Supplemental Figure 18). Using the enriched library, TaG-EM barcodes were detected in nearly 100% of the cells at high sequencing depths (Supplemental Figure 19). However, although we used a polymerase that has been engineered to have high processivity and that has been shown to reduce the formation of chimeric reads in other contexts (Gohl et al., 2016), it is possible that PCR chimeras could lead to unreliable detection events for some cells. Indeed, many cells had a mixture of barcodes detected with low counts and single or low numbers of associated UMIS. To assess the reliability of detection, we analyzed the correlation between barcodes detected in the gene expression library and the enriched TaG-EM barcode library as a function of the purity of TaG-EM barcode detection for each cell (the percentage of the most abundant detected TaG-EM barcode, Supplemental Figure 19). For TaG-EM barcode detections where the most abundance barcode was a high percentage of the total barcode reads detected (~75%-99.99%), there was a high correlation between the barcode detected in the gene expression library and the enriched TaG-EM barcode library. Below this threshold, the correlation was substantially reduced. 

In the enriched library, we identified 26.8% of cells with a TaG-EM barcode reliably detected, a very modest improvement over the gene expression library alone (23.96%), indicating that at least for this experiment, the main constraint is sufficient expression of the TaG-EM barcode and not detection. To identify TaG-EM barcodes in the combined data set, we counted a positive detection as any barcode either identified in the gene expression library or any barcode identified in the enriched library with a purity of >75%. In the case of conflicting barcode calls, we assigned the barcode that was detected directly in the gene expression library. This increased the total fraction of cells where a barcode was identified to approximately 37% (Figure 6B).”

Methods:

“The resulting pool was prepared for sequencing following the 10x Genomics Single Cell 3’ protocol (version CG000315 Rev C), At step 2.2 of the protocol, cDNA amplification, 1 µl of TaG-EM spike-in primer (10 µM) was added to the reaction to amplify cDNA with the TaG-EM barcode. Gene expression cDNA and TaG-EM cDNA were separated using a double-sided SPRIselect (Beckman Coulter) bead clean up following 10x Genomics Single Cell 3’ Feature Barcode protocol, step 2.3 (version CG000317 Rev E). The gene expression cDNA was created into a library following the CG000315 Rev C protocol starting at section 3. Custom nested primers were used for enrichment of TaG-EM barcodes after cDNA creation using PCR.  The following primers were tested (see Supplemental Figure 18):

UMGC_IL_TaGEM_SpikeIn_v1:

GTGACTGGAGTTCAGACGTGTGCTCTTCCGATCTCTTCCAACAACCGGAAGT*G*A UMGC_IL_TaGEM_SpikeIn_v2:

GTGACTGGAGTTCAGACGTGTGCTCTTCCGATCTGCAGCTTATAACTTCCAACAACCGGAAGT*G*A

UMGC_IL_TaGEM_SpikeIn_v3:

TGTGCTCTTCCGATCTGCAGCTTATAACTTCCAACAACCGGAAGT*G*A D701_TaGEM:

CAAGCAGAAGACGGCATACGAGATCGAGTAATGTGACTGGAGTTCAGACGTGTGCTCTTCCGATCTGCAGC*T*T

SI PCR Primer:

AATGATACGGCGACCACCGAGATCTACACTCTTTCCCTACACGACGC*T*C

UMGC_IL_DoubleNest:

GTGACTGGAGTTCAGACGTGTGCTCTTCCGATCTGCAGCTTATAACTTCCAACAACCGG*A*A

P5: AATGATACGGCGACCACCGA

D701:

GATCGGAAGAGCACACGTCTGAACTCCAGTCACATTACTCGATCTCGTATGCCGTCTTCTGCTTG

D702:

GATCGGAAGAGCACACGTCTGAACTCCAGTCACTCCGGAGAATCTCGTATGCCGTCTTCTGCTTG

After multiple optimization trials, the following steps yielded ~96% on-target reads for the TaG-EM library (Supplemental Figure 18, note that for the enriched barcode data shown in Figure 6 and Supplemental Figure 19, a similar amplification protocol was used TaG-EM barcodes were amplified from the gene expression library cDNA and not the SPRI-selected barcode pool). TaG-EM cDNA was amplified with the following PCR reaction: 5 µl purified TaG-EM cDNA, 50 µl 2x KAPA HiFi ReadyMix (Roche), 2.5 µl UMGC_IL_DoubleNest primer (10 µM), 2.5 µl SI_PCR primer (10 µM), and 40 µl nuclease-free water. The reaction was amplified using the following cycling conditions: 98ºC for 2 minutes, followed by 15 cycles of 98ºC for 20 seconds, 63ºC for 30 seconds, 72ºC for 20 seconds, followed by 72ºC for 5 minutes. After the first PCR, the amplified cDNA was purified with a 1.2x SPRIselect (Beckman Coulter) bead cleanup with 80% ethanol washes and eluted into 40 µL of nuclease-water. A second round of PCR was run with following reaction: 5 µl purified TaG-EM cDNA, 50 µl 2x KAPA HiFi ReadyMix (Roche), 2.5 µl D702 primer (10 µM), 2.5 µl p5 Primer (10 µM), and 40 µl nuclease-free water. The reaction was amplified using the following cycling conditions: 98ºC for 2 minutes, followed by 10 cycles of 98ºC for 20 seconds, 63ºC for 30 seconds, 72ºC for 20 seconds, followed by 72ºC for 5 minutes. After the second PCR, the amplified cDNA was purified with a 1.2x SPRIselect (Beckman Coulter) bead cleanup with 80% ethanol washes and eluted into 40uL of nuclease-water. The resulting 3’ gene expression library and TaG-EM enrichment library were sequenced together following Scenario 1 of the BioLegend “Total-Seq-A Antibodies and Cell Hashing with 10x Single Cell 3’ Reagents Kit v3 or v3.1” protocol. Additional sequencing of the enriched TaG-EM library also done following Scenario 2 from the same protocol.” 

When a given cell barcode is not associated with any TaG-EM barcode, then demultiplexing is impossible. This is a major problem, which is particularly visible in Figs 5 and S13. In 5F, BC4 is only detected in a couple of dozen cells, even though the Jon99Ciii marker of enterocytes is present in a much larger population (Fig 5C). Therefore, in this particular case, TaG-EM fails to detect most of the GFP-expressing cells. 

Figure 5 in the original manuscript represented data from an experiment in which there were eight different TaG-EM barcoded samples present, including four replicates of the pan-midgut driver (each of which included enterocyte populations). One would not expect the BC4 enterocyte driver expression to be observed in all of the Jon99Ciii cells, since the majority of the GFP+ cells shown in the UMAP plot were likely derived from and are labeled by the pan-midgut driver-associated barcodes. Thus, the design and presentation of this particular experiment (in particular, the presence of eight distinct samples in the data set) is making the detection of the TaG-EM barcodes look sparser than it actually is. We have added a panel in both Figure 6B and Supplemental Figure 17B that shows the overall detection of barcodes in the enriched barcode library and gene expression library or the gene expression library only, respectively, for this experiment.

However, the reviewer’s overall point regarding barcode detection is still valid in that if we consider all eight barcodes, we only see TaG-EM barcode labeling associated with about a quarter of all the cells in this gene expression library, or about 37% of cells when we include the enriched TaG-EM barcode library. While improving barcode detection will improve the yield and is necessary for some applications (such as robust detection of multiplets), we would argue that even at the current level of success this approach has significant utility. First, if one’s goal is to unambiguously label a cell cluster and trace it to a defined cell population in vivo, sparse labeling may be sufficient. Second, demultiplexing is still possible (as we demonstrate) but involves a trade off in yield (not every cell is recovered and there is some extra sequencing cost as some sequenced cells cannot be assigned to a barcode). 

Similarly, in S13, most cells should express one of the four barcodes, however many of them (maybe up to half - this should be quantified) do not. Therefore, the claim (L277278) that "the pan-midgut driver were broadly distributed across the cell clusters" is misleading. Moreover, the hypothesis that "low expressing driver lines may result in particularly sparse labelling" (L331-333) is at least partially wrong, as Fig S13 shows that the same Gal4 driver can lead to very different levels of barcode coverage.

As described above, since this experiment included eight different TaG-EM barcodes expressed by five different drivers, the expectation is that only about half of the cells in Figure S13 (now Figure S20) should express a TaG-EM barcode. It is not clear why BC2 is underrepresented in terms of the number of cells labeled and BC7 is overrepresented. We agree with the reviewer that this should be described more accurately in the paper and that it does impact our interpretation related to driver strength and barcode detection. We have revised this sentence in the discussion and also added additional text in the results describing the within driver variability seen in this experiment.

Results text:

“As expected, the barcodes expressed by the pan-midgut driver were broadly distributed across the cell clusters (Supplemental Figure 20). However, the number of cells recovered varied significantly among the four pan-midgut driver associated barcodes.”

Discussion text:

“It is likely that the strength of the Gal4 driver contributes to the labeling density. However, we also observed variable recovery of TaG-EM barcodes that were all driven by the same pan-midgut Gal4 driver (Supplemental Figure 20).”

• Comparisons between TaG-EM and other, simpler methods for labelling individual cell populations are missing. For example, how would TaG-EM compare with expression of different fluorescent reporters, or a strategy based on the brainbow/flybow principle?

The advantage of TaG-EM is that an arbitrarily large number of DNA barcodes can be used (contingent upon the availability of transgenic lines – we described 20 barcoded lines in our initial manuscript and we have now extended this collection to over 170 lines), while the number of distinguishable FPs is much lower. Brainbow/Flybow uses combinatorial expression of different FPs, but because this combinatorial expression is stochastic, tracing a single cell transcriptome to a defined cell population in vivo based on the FP signature of a Brainbow animal would likely not be possible (and would almost certainly be impossible at scale).

• FACS data is missing throughout the paper. The authors should include data from their comparative flow cytometry experiment of TaG-EM cells with or without additional hexameric GFP, as well as FSC/SSC and fluorescence scatter plots for the FACS steps that they performed prior to scRNA-seq, at least in supplementary figures.

We have added Supplemental Figures with the FACS data for all of the single cell sequencing data presented in the manuscript (Supplemental Figures 12 and 14).

• The authors should show the whole data described in L229, including the cluster that they chose to delete. At least, they should provide more information about how many cells were removed. In any case, the fact that their data still contains a large number of debris and dead cells despite sorting out PI negative cells with FACS and filtering low abundance barcodes with Cellranger is concerning.

This description was referring to the unprocessed Cellranger output (not filtered for low abundance barcodes). Prior to filtering for cell barcodes with high mitochondria or rRNA (or other processing in Seurat/Scanpy), we saw two clusters, one with low UMI counts and enrichment of mitochondrial genes (see Cellranger report below). 

Author response image 1.

These cell barcodes were removed by downstream quality filtering and the remaining cells showed expression of expected intestinal stem cell and enteroblast marker genes.

Overall, although a method for genetic tagging cell populations prior to multiplexing in single-cell experiments would be extremely useful, the method presented here is inadequate. However, despite all the weaknesses listed above, the idea of barcodes expressed specifically in cells of interest deserves more consideration. If the authors manage to improve their design to resolve the major issues and demonstrate the benefits of their method more clearly, then TaG-EM could become an interesting option for certain applications.

We thank the reviewer for this comment and hope that the above responses and additional experiments and data that we have added have helped to alleviate the noted weaknesses.

Reviewer #2 (Public Review):

In this manuscript, Mendana et al developed a multiplexing method - Targeted Genetically-Encoded Multiplexing or TaG-EM - by inserting a DNA barcode upstream of the polyadenylation site in a Gal4-inducible UAS-GFP construct. This Multiplexing method can be used for population-scale behavioral measurements or can potentially be used in single-cell sequencing experiments to pool flies from different populations. The authors created 20 distinctly barcoded fly lines. First, TaG-EM was used to measure phototaxis and oviposition behaviors. Then, TaG-EM was applied to the fly gut cell types to demonstrate its applications in single-cell RNA-seq for cell type annotation and cell origin retrieving.

This TaG-EM system can be useful for multiplexed behavioral studies from nextgeneration sequencing (NGS) of pooled samples and for Transcriptomic Studies. I don't have major concerns for the first application, but I think the scRNA-seq part has several major issues and needs to be further optimized.

Major concerns:

(1) It seems the barcode detection rate is low according to Fig S9 and Fig 5F, J and N. Could the authors evaluate the detection rate? If the detection rate is too low, it can cause problems when it is used to decode cell types.

See responses to Reviewer #1 on this topic above.  

(2) Unsuccessful amplification of TaG-EM barcodes: The authors attempted to amplify the TaG-EM barcodes in parallel to the gene expression library preparation but encountered difficulties, as the resulting sequencing reads were predominantly offtarget. This unsuccessful amplification raises concerns about the reliability and feasibility of this amplification approach, which could affect the detection and analysis of the TaG-EM barcodes in future experiments.

As noted above, we have now established a successful amplification protocol for the TaG-EM barcodes. This data is shown in Figure 6, and Supplemental Figures 18-19 and we have included a detailed information in the methods for performing TaG-EM barcode enrichment during 10x library prep. We have also included code in the paper’s Github repository for assigning TaG-EM barcodes from the enriched library to the associated 10x Genomics cell barcodes.

(3) For Fig 5, the singe-cell clusters are not annotated. It is not clear what cell types are corresponding to which clusters. So, it is difficult to evaluate the accuracy of the assignment of barcodes.

We have added annotation information for the cell clusters based on expression of cell-type-specific marker genes (Figure 6A, Supplemental Figures 16-17).

(4) The scRNA-seq UMAP in Fig 5 is a bit strange to me. The fly gut epithelium contains only a few major cell types, including ISC, EB, EC, and EE. However, the authors showed 38 clusters in fig 5B. It is true that some cell types, like EE (Guo et al., 2019, Cell Reports), have sub-populations, but I don't expect they will form these many subtypes. There are many peripheral small clusters that are not shown in other gut scRNAseq studies (Hung et al., 2020; Li et al., 2022 Fly Cell Atlas; Lu et al., 2023 Aging Fly Cell Atlas). I suggest the authors try different data-processing methods to validate their clustering result.

For all of the single cell experiments, after doublet and ambient RNA removal (as suggested below), we have reclustered the datasets and evaluated different resolutions using Clustree. As the Reviewer points out, there are different EE subtypes, as well as regionalized expression differences in EC and other cell populations, so more than four clusters are expected (an analysis of the adult midgut identified 22 distinct cell types). With this revised analysis our results more closely match the cell populations observed in other studies (though it should be noted that the referenced studies largely focus on the adult and not the larval stage).  

(5) Different gut drivers, PMC-, PC-, EB-, EC-, and EE-GAL4, were used. The authors should carefully characterize these GAL4 expression in larval guts and validate sequencing data. For example, does the ratio of each cell type in Fig 5B reflect the in vivo cell type ratio? The authors used cell-type markers mostly based on the knowledge from adult guts, but there are significant morphological and cell ratio differences between larval and adult guts (e.g., Mathur...Ohlstein, 2010 Science).

We have characterized the PC driver which is highlighted in Supplemental Figure 13, and the EC and EE drivers which are highlighted in Figure 6G-N in detail in larval guts and have added this data to the paper (Supplemental Figure 21). The EB driver was not characterized histologically as EB-specific antibodies are not currently available. The PMG-Gal4 line exhibits strong expression throughout the larval gut (Figure 5B and barcodes are recovered from essentially all of the larval gut cell clusters using this driver (Supplemental Figure 20). We don’t necessarily expect the ratios of cells observed in the scRNA-Seq data to reflect the ratios typically observed in the gut as we performed pooled flow sorting on a multiplexed set of eight genotypes and driver expression levels, flow sorting, and possibly other processing steps could all influence the relative abundance of different cell types. However, detailed characterization of these driver lines did reveal spatial expression patterns that help explain aspects of the scRNA-Seq data. We have also added the following text to the paper to further describe the characterization of the drivers:

Results:

“Detailed characterization of the EC-Gal4 line indicated that although this line labeled a high percentage of enterocytes, expression was restricted to an area at the anterior and middle of the midgut, with gaps between these regions and at the posterior (Supplemental Figure 21). This could explain the absence of subsets of enterocytes, such as those labeled by betaTry, which exhibits regional expression in R2 of the adult midgut (Buchon et al., 2013).”

“Detailed characterization of the EE-Gal4 driver line indicated that ~80-85% of Prospero-positive enteroendocrine cells are labeled in the anterior and middle of the larval midgut, with a lower percentage (~65%) of Prospero-positive cells labeled in the posterior midgut (Supplemental Figure 21). As with the enterocyte labeling, and consistent with the Gal4 driver expression pattern, the EE-Gal4 expressed TaG-EM barcode 9 did not label all classes of enteroendocrine cells and other clusters of presumptive enteroendocrine cells expressing other neuropeptides such as Orcokinin, AstA, and AstC, or neuropeptide receptors such as CCHa2 (not shown) were also observed.”

Methods:

“Dissection and immunostaining

Midguts from third instar larvae of driver lines crossed to UAS-GFP.nls or UAS-mCherry were dissected in 1xPBS and fixed with 4% paraformaldehyde (PFA) overnight at 4ºC. Fixed samples were washed with 0.1% PBTx (1xPBS + 0.1% Triton X-100) three times for 10 minutes each and blocked in PBTxGS (0.1% PBTx + 3% Normal Goat Serum) for 2–4 hours at RT. After blocking, midguts were incubated in primary antibody solution overnight at 4ºC. The next day samples were washed with 0.1% PBTx three times for 20 minutes each and were incubated in secondary antibody solution for 2–3 hours at RT (protected from light) followed by three washes with 0.1% PBTx for 20 minutes each. One µg/ml DAPI solution prepared in 0.1% PBTx was added to the sample and incubated for 10 minutes followed by washing with 0.1% PBTx three times for 10 minutes each. Finally, samples were mounted on a slide glass with 70% glycerol and imaged using a Nikon AX R confocal microscope. Confocal images were processed using Fiji software. 

The primary antibodies used were rabbit anti-GFP (A6455,1:1000 Invitrogen), mouse anti-mCherry (3A11, 1:20 DSHB), mouse anti-Prospero (MR1A, 1:50 DSHB) and mouse anti-Pdm1 (Nub 2D4, 1:30 DSHB). The secondary antibodies used were goat antimouse and goat anti-rabbit IgG conjugated to Alexa 647 and Alexa 488 (1:200) (Invitrogen), respectively. Five larval gut specimens per Gal4 line were dissected and examined.”

(6) Doublets are removed based on the co-expression of two barcodes in Fig 5A. However, there are also other possible doublets, for example, from the same barcode cells or when one cell doesn't have detectable barcode. Did the authors try other computational approaches to remove doublets, like DoubleFinder (McGinnis et al., 2019) and Scrublet (Wolock et al., 2019)?

We have included DoubleFinder-based doublet removal in our data analysis pipeline. This is now described in the methods (see below).

(7) Did the authors remove ambient RNA which is a common issue for scRNA-seq experiments?

We have also used DecontX to remove ambient RNA. This is now described in the methods:

“Datasets were first mapped and analyzed using the Cell Ranger analysis pipeline (10x Genomics). A custom Drosophila genome reference was made by combining the BDGP.28 reference genome assembly and Ensembl gene annotations. Custom gene definitions for each of the TaG-EM barcodes were added to the fasta genome file and .gtf gene annotation file. A Cell Ranger reference package was generated with the Cell Ranger mkref command. Subsequent single-cell data analysis was performed using the R package Seurat (Satija et al., 2015). Cells expressing less than 200 genes and genes expressed in fewer than three cells were filtered from the expression matrix. Next, percent mitochondrial reads, percent ribosomal reads cells counts, and cell features were graphed to determine optimal filtering parameters. DecontX (Yang et al., 2020) was used to identify empty droplets, to evaluate ambient RNA contamination, and to remove empty cells and cells with high ambient RNA expression. DoubletFinder (McGinnis et al., 2019) to identify droplet multiplets and remove cells classified as multiplets. Clustree (Zappia and Oshlack, 2018) was used to visualize different clustering resolutions and to determine the optimal clustering resolution for downstream analysis. Finally, SingleR (Aran et al., 2019) was used for automated cell annotation with a gut single-cell reference from the Fly Cell Atlas (Li et al., 2022). The dataset was manually annotated using the expression patterns of marker genes known to be associated with cell types of interest. To correlate TaG-EM barcodes with cell IDs in the enriched TaG-EM barcode library, a custom Python script was used (TaGEM_barcode_Cell_barcode_correlation.py), which is available via Github: https://github.com/darylgohl/TaG-EM.”

(8) Why does TaG-EM barcode #4, driven by EC-GAL4, not label other classes of enterocyte cells such as betaTry+ positive ECs (Figures 5D-E)? similarly, why does TaG-EM barcode #9, driven by EE-GAL4, not label all EEs? Again, it is difficult to evaluate this part without proper data processing and accurate cell type annotation.

As noted in the response to a comment by Reviewer #1 above, part of this apparent sparsity of labeling is due to the way that this experiment was designed and visualized. We have added a new Figure panel in both Figure 6B and Supplemental Figure 17B that shows the overall detection of barcodes in the enriched barcode library and gene expression library or the gene expression library only, respectively, to better illustrate the efficacy of barcode detection. See also the response to point 5 above. Both the lack of labelling of betaTry+ ECs and subsets of EEs is consistent with the expression patterns of the EC-Gal4 and EE-Gal4 drivers.

(9) For Figure 2, when the authors tested different combinations of groups with various numbers of barcodes. They found remarkable consistency for the even groups. Once the numbers start to increase to 64, barcode abundance becomes highly variable (range of 12-18% for both male and female). I think this would be problematic because the differences seen in two groups for example may be due to the barcode selection rather than an actual biologically meaningful difference.

While there is some barcode-to-barcode variability for different amplification conditions, the magnitude of this variation is relatively consistent across the conditions tested. We looked at the coefficient of variation for the evenly pooled barcodes or for the staggered barcodes pooled at different relative levels. While the absolute magnitude of the variation is higher for the highly abundant barcodes in the staggered conditions, the CVs for these conditions (0.186 for female flies and for 0.163 male flies) were only slightly above the mean CV (0.125) for all conditions (see Supplemental Figure 3):

We have added this analysis as Supplemental Figure 3 and added the following text to the paper:(

“The coefficients of variation were largely consistent for groups of TaG-EM barcodes pooled evenly or at different levels within the staggered pools (Supplemental Figure 3).”

(10) Barcode #14 cannot be reliably detected in oviposition experiment. This suggests that the BC 14 fly line might have additional mutations in the attp2 chromosome arm that affects this behavior. Perhaps other barcode lines also have unknown mutations and would cause issues for other untested behaviors. One possible solution is to backcross all 20 lines with the same genetic background wild-type flies for >7 generations to make all these lines to have the same (or very similar) genetic background. This strategy is common for aging and behavior assays.

See response to Reviewer #1 above on this topic.

Reviewer #3 (Public Review):

The work addresses challenges in linking anatomical information to transcriptomic data in single-cell sequencing. It proposes a method called Targeted Genetically-Encoded Multiplexing (TaG-EM), which uses genetic barcoding in Drosophila to label specific cell populations in vivo. By inserting a DNA barcode near the polyadenylation site in a UASGFP construct, cells of interest can be identified during single-cell sequencing. TaG-EM enables various applications, including cell type identification, multiplet droplet detection, and barcoding experimental parameters. The study demonstrates that TaGEM barcodes can be decoded using next-generation sequencing for large-scale behavioral measurements. Overall, the results are solid in supporting the claims and will be useful for a broader fly community. I have only a few comments below:

We thank the reviewer for these positive comments.

Specific comments:

(1) The authors mentioned that the results of structure pool tests in Fig. 2 showed a high level of quantitative accuracy in detecting the TaG-EM barcode abundance. Although the data were generally consistent with the input values in most cases, there were some obvious exceptions such as barcode 1 (under-represented) and barcodes 15, 20 (overrepresented). It would be great if the authors could comment on these and provide a guideline for choosing the appropriate barcode lines when implementing this TaG-EM method.

See the response to point 9 from Reviewer 2. Although there seem to be some systematic differences in barcode amplification, the coefficient of variation was relatively consistent across all of the barcode combinations and relative input levels that we examined. Our recommendation (described in the text) is to average across 3-4 independent barcodes (which yielded a R2 values of >0.99 with expected abundance in the structured pooled tests).  

(2) In Supplemental Figure 6, the authors showed GFP antibody staining data with 20 different TaG-EM barcode lines. The variability in GFP antibody staining results among these different TaG-EM barcode lines concerns the use of these TaG-EM barcode lines for sequencing followed by FACS sorting of native GFP. I expected the native GFP expression would be weaker and much more variable than the GFP antibody staining results shown in Supplemental Figure 6. If this is the case, variation of tissue-specific expression of TaG-EM barcode lines will likely be a confounding factor.

Aside from barcode 8, which had a mutation in the GFP coding sequence, we did not see significant variability in expression levels either in the wing disc. Subtle differences seen in this figure most likely result from differences in larval staging. Similar consistent native (unstained) GFP expression of the TaG-EM constructs was seen in crosses with Mhc-Gal4 (described above). 

(3) As the authors mentioned in the manuscript, multiple barcodes for one experimental condition would be a better experimental design. Could the authors suggest a recommended number of barcodes for each experiential condition? 3? 4? Or more? 

See response to Reviewer #3, point number 1 above.

(3b) Also, it would be great if the authors could provide a short discussion on the cost of such TaG-EM method. For example, for the phototaxis assay, if it is much more expensive to perform TaG-EM as compared to manually scoring the preference index by videotaping, what would be the practical considerations or benefits of doing TaG-EM over manual scoring?

While this will vary depending on the assay and the scale at which one is conducting experiments, we have added an analysis of labor savings for the larval gut motility assay (Supplemental Figure 8). We have also added the following text to the Discussion describing some of the trade-offs to consider in assessing the potential benefit of incorporating TaG-EM into behavioral measurements:

“While the utility of TaG-EM barcode-based quantification will vary based on the number of conditions being analyzed and the ease of quantifying the behavior or phenotype by other means, we demonstrate that TaG-EM can be employed to cost-effectively streamline labor-intensive assays and to quantify phenotypes with small effect sizes (Figure 4, Supplemental Figure 8).”

Recommendations for the authors:  

While recognising the potential of the TaG-EM methodology, we had a few major concerns that the authors might want to consider addressing:

As stated above, we are grateful to the reviewers and editor for their thoughtful comments. We have addressed many of the points below in our responses above, so we will briefly respond to these points and where relevant direct the reader to comments above.

(1) We were concerned about the efficacy of TaG-EM in assessing more complex behaviours than oviposition and phototaxis. We note that Barcode #14 cannot be reliably detected in oviposition experiment. This suggests that the BC 14 fly line might have additional mutations in the attp2 chromosome arm that affects this behavior. Perhaps other barcode lines also have unknown mutations and would cause issues for other untested behaviors. One possible solution is to back-cross all 20 lines with the same genetic background wild-type flies for >7 generations to make all these lines to have the same (or very similar) genetic background. This strategy is common for aging and behavior assays.

See response to Reviewer #1 and Reviewer #2, item 10, above.

(2) We were unable to assess the drop-out rates of the TaG-EM barcode from the sequencing. The barcode detection rate is low (Fig S9 and Fig 5F, J and N). This would be a considerable drawback (relating to both experimental design and cost), if a large proportion of the cells could not be assigned an identity.

See comments above addressing this point.

(3) The effectiveness of TaG-EM scRNA-seq on the larvae gut is not very effective - the cells are not well annotated, the barcodes seem not to have labelled expected cell types (ECs and EEs), and there is no validation of the Gal4 drivers in vivo.

See previous comments. We have addressed specific comments above on data processing and annotation, included a visualization of the overall effectiveness of labeling, added a protocol and data on enriched TaG-EM barcode libraries, and have added detailed characterization of the Gal4 drivers in the larval gut (Figure 6, Supplemental Figures 17-21).

(4) A formal assessment of the cost-effectiveness would be an important consideration in broad uptake of the methodology.

While this is difficult to do in a comprehensive manner given the breadth of potential applications, we have included estimates of labor savings for one of the behavioral assays that we tested (Supplemental Figure 8). We have also included a discussion of some of the factors that would make TaG-EM useful or cost-effective to apply for behavioral assays (see response to Reviewer #3, comment 3b, above). We have also added the following text to the discussion to address the cost considerations in applying TaG-EM for scRNA-Seq:

“For single cell RNA-Seq experiments, the cost savings of multiplexing is roughly the cost of a run divided by the number of independent lines multiplexed, plus labor savings by also being able to multiplex upstream flow cytometry, minus loss of unbarcoded cells. Our experiments indicated that for the specific drivers we tested TaG-EM barcodes are detected in around one quarter of the cells if relying on endogenous expression in the gene expression library, though this fraction was higher (~37%) if sequencing an enriched TaG-EM barcode library in parallel (Figure 6, Supplemental Figures 18-19).”

(5) Similarly, a formal assessment of the effect of the insertion on the variability in GFP expression and the behaviour needs to be documented.

See responses to Reviewer #1, Reviewer #2, item 9, and Reviewer #3, item 2 above.

Reviewer #1 (Recommendations For The Authors):

(in no particular order of importance)

• L84-85: the authors should either expand, or remove this statement. Indeed, lack of replicates is only true if one ignores that each cell in an atlas is indeed a replicate. Therefore, depending on the approach or question, this statement is inaccurate.

This sentence was meant to refer to experiments where different experimental conditions are being compared and not to more descriptive studies such as cell atlases. We have revised this sentence to clarify.

“Outside of descriptive studies, these costs are also a barrier to including replicates to assess biological variability; consequently, a lack of biological replicates derived from independent samples is a common shortcoming of single-cell sequencing experiments.”

• L103-104: this sentence is unclear.

We have revised this sentence as follows:

“Genetically barcoded fly lines can also be used to enable highly multiplexed behavioral assays which can be read out using high throughput sequencing.”

• In Fig S1 it is unclear why there are more than 20 different sequences in panel B where the text and panel A only mention the generation of 20 distinct constructs. This should be better explained.

The following text was added to the Figure legend to explain this discrepancy:

“Because the TaG-EM barcode constructs were injected as a pool of 29 purified plasmids, some of the transgenic lines had inserts of the same construct. In total 20 unique lines were recovered from this round of injection.”

• It would be interesting to compare the efficiency of TaG-EM driven doublet removal (Fig 5A) with standard doublet-removing software (e.g., DoubletFinder, McGinnis et al., 2019).

We have done this comparison, which is now shown in Supplemental Figure 15.

• I would encourage the authors to check whether barcode representation in Fig S13  can be correlated to average library size, as one would expect libraries with shorter reads to be more likely to include the 14-bp barcode and therefore more accurately recapitulate TaG-EM barcode expression.

These are not independent sequencing libraries, but rather data from barcodes that were multiplexed in a single flow sort, 10x droplet capture, and sequencing library. Thus, there must be some other variable that explains the differential recovery of these barcodes.

• Fig 4A should appear earlier in the paper.

We have moved Figure 4A from the previous manuscript (a schematic showing the detailed design of the TaG-EM construct) to Figure 1A in the revised version.

Reviewer #2 (Recommendations For The Authors):

Minor:

(1) There is a typo for Fig S13 figure legends: BC1, BC1, BC3... should be BC1, BC2, BC3.

Fixed.

Reviewer #3 (Recommendations For The Authors):

Comments to authors:

(1) It would be great if the authors could provide an additional explanation on how these 29 barcode sequences were determined.

Response: This information is in the Methods section. For the original cloned plasmids:

“Expected construct size was verified by diagnostic digest with _Eco_RI and _Apa_LI. DNA concentration was determined using a Quant-iT PicoGreen dsDNA assay (Thermo Fisher Scientific) and the randomer barcode for each of the constructs was determined by Sanger sequencing using the following primers:

SV40_post_R: GCCAGATCGATCCAGACATGA

SV40_5F: CTCCCCCTGAACCTGAAACA”

For transgenic flies, after DNA extraction and PCR enrichment (details also in the Methods section):

“The barcode sequence for each of the independent transgenic lines was determined by Sanger sequencing using the SV40_5F and SV40_PostR primers.”

(2) Why did the authors choose myr-GFP as the backbone instead of nls-GFP if the downstream application is to perform sequencing?

We initially chose myr::GFP as we planned to conduct single cell and not single nucleus sequencing and myr::GFP has the advantage of labeling cell membranes which could facilitate the characterization or confirmation of cell type-specific expression, particularly in the nervous system. However, we have considered making a version of the TaG-EM construct with a nuclear targeted GFP (thereby enabling “NucEM”). In the Discussion, we mention this possibility as well as the possibility of using a second nuclear-GFP construct in conjunction with TaG-EM lines is nuclear enrichment is desired:

“In addition, while the original TaG-EM lines were made using a membrane-localized myr::GFP construct, variants that express GFP in other cell compartments such as the cytoplasm or nucleus could be constructed to enable increased expression levels or purification of nuclei. Nuclear labeling could also be achieved by co-expressing a nuclear GFP construct with existing TaG-EM lines in analogy to the use of hexameric GFP described above.”

Minor comments:

(1) Line 193, Supplemental Figure 4 should be Supplemental Figure 5

Fixed.

(2) Scale bars should be added in Figure 4, Supplemental Figures 6, 7, and 8A.

We have added scale bars to these figures and also included scale bars in additional Supplemental Figures detailing characterization of the gut driver lines.

(3) Were Figure 4C and Supplemental Figure 7 data stained with a GFP antibody?

No, this is endogenous GFP signal. This is now noted in the Figure legends.

(4) Line 220, specify the three barcode lines (lines #7, 8, 9) in the text. 

Added this information.

Same for Lines 251-254. Line 258, which 8 barcode Gal4 line combinations?

(5) Line 994, typo: (BC1, BC1, BC3, and BC7)-> (BC1, BC2, BC3, and BC7)

Fixed.

(6) Figure 5 F, J and N, add EC-Gal4, EB-Gal4, and EE-Gal4 above each panel to improve readability.

We have added labels of the cell type being targeted (leftmost panels), the barcode, and the marker gene name to Figure 6 C-N.

eLife Assessment

Modulation of BMP signalling affects body size in the nematode Caenorhabditis elegans, and this paper examines the effects on C. elegans body size brought about by the modulation of BMP signalling. Thw study provides valuable analyses of ChIP-seq and RNA-Seq data to understand the function of SMA-3 (Smad) and SMA-9 (Schnurri) in this model. The authors provide compelling evidence that the BMP-dependent body size effect could be due to defects in cuticle collagen secretion, a finding of interest to those studying organismal growth and epidermal function.

Reviewer #1 (Public review):

Summary:

BMP signaling is, arguably, best known for its role in the dorsoventral patterning, but not in nematodes, where it regulates body size. In their paper, Vora et al. analyze ChIP-Seq and RNA-Seq data to identify direct transcriptional targets of SMA-3 (Smad) and SMA-9 (Schnurri) and understand the respective roles of SMA-3 and SMA-9 in the nematode model Caenorhabditis elegans. The Authors use SMA-3 and SMA-9 ChIP-Seq data and RNA-Seq data from SMA-3 and SMA-9 mutants, and bioinformatic analyses to identify the genes directly controlled by these two transcription factors (TFs) and find approximately 350 such targets for each. They show that all SMA-3-controlled targets are positively controlled by SMA-3 binding, while SMA-9-controlled targets can be either up- or downregulated by SMA-9. 129 direct targets were shared by SMA-3 and SMA-9, and, curiously, the expression of 15 of them was activated by SMA-3 but repressed by SMA-9. In case of such opposing effects, the SMA-9 appears to act epistatically to SMA-3. Since genes responsible for cuticle collagen production were eminent among the SMA-3 targets, the Authors focused on trying to understand the body size defect known to be elicited by the modulation of BMP signaling. Vora et al. provide compelling evidence that this defect is likely to be due to problems with the BMP signaling-dependent collagen secretion necessary for cuticle formation.

Strengths:

Vora et al. provide a valuable analysis of ChIP-Seq and RNA-Seq datasets, which will be very useful for the community. They also shed light on the mechanism of the BMP-dependent body size control by identifying SMA-3 target genes regulating cuticle collagen synthesis and by showing that downregulation of these genes affects body size in C. elegans.

Weaknesses:

(1) Although the analysis of the SMA-3 and SMA-9 ChIP-Seq and RNA-Seq data is extremely useful, the goal "to untangle the roles of Smad and Schnurri transcription factors in the developing C. elegans larva", has not been reached. While the role of SMA-3 as a transcriptional activator appears to be quite straightforward, the function of SMA-9 in the BMP signaling remains obscure.

(2) The Authors clearly show that both TFs can bind independently of each other, however, by using distances between SMA-3 and SMA-9 ChIP peaks, they claim that when the peaks are close these two TFs likely act as complexes. In the absence of proof that SMA-3 and SMA-9 physically interact (e.g. that they co-immunoprecipitate - as they do in Drosophila), this is an unfounded claim, which still has to be experimentally substantiated. In the revised version of the manuscript, the authors acknowledge this.

(3) The second part of the results (the collagen story) is loosely connected the first part. dpy-11 encodes an enzyme important for cuticle development, and it is a differentially expressed direct target of SMA-3. dpy-11 can be bound by SMA-9, but it is not affected by this binding according to RNA-Seq. Thus, technically, this part of the paper does not require any information about SMA-9. However, this can likely be improved by addressing the function of the 15 genes, with the opposing mode of regulation by SMA-3 and SMA-9.

Comments on revisions:

In comparison to the first version of the manuscript, the authors have significantly improved the "readability" of the paper, made the Discussion much better, and toned down some of the less supported arguments.

Author response:

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

Reviewer #1 (Public Review):

Summary:

BMP signaling is, arguably, best known for its role in the dorsoventral patterning, but not in nematodes, where it regulates body size. In their paper, Vora et al. analyze ChIP-Seq and RNA-Seq data to identify direct transcriptional targets of SMA-3 (Smad) and SMA-9 (Schnurri) and understand the respective roles of SMA-3 and SMA-9 in the nematode model Caenorhabditis elegans. The authors use publicly available SMA-3 and SMA-9 ChIP-Seq data, own RNA-Seq data from SMA-3 and SMA-9 mutants, and bioinformatic analyses to identify the genes directly controlled by these two transcription factors (TFs) and find approximately 350 such targets for each. They show that all SMA-3-controlled targets are positively controlled by SMA-3 binding, while SMA-9-controlled targets can be either up or downregulated by SMA-9. 129 direct targets were shared by SMA-3 and SMA-9, and, curiously, the expression of 15 of them was activated by SMA-3 but repressed by SMA-9. Since genes responsible for cuticle collagen production were eminent among the SMA-3 targets, the authors focused on trying to understand the body size defect known to be elicited by the modulation of BMP signaling. Vora et al. provide compelling evidence that this defect is likely to be due to problems with the BMP signaling-dependent collagen secretion necessary for cuticle formation.

We thank the reviewer for this supportive summary. We would like to clarify the status of the publicly available ChIP-seq data. We generated the GFP tagged SMA-3 and SMA‑9 strains and submitted them to be entered into the queue for ChIP-seq processing by the modENCODE (later modERN) consortium. Thus, the publicly available SMA-3 and SMA-9 ChIP-seq datasets used here were derived from our efforts.  Due to the nature of the consortium’s funding, the data were required to be released publicly upon completion. Nevertheless, our current manuscript provides the first comprehensive analysis of these datasets. We have updated the text to clarify this point.

Strengths:

Vora et al. provide a valuable analysis of ChIP-Seq and RNA-Seq datasets, which will be very useful for the community. They also shed light on the mechanism of the BMP-dependent body size control by identifying SMA-3 target genes regulating cuticle collagen synthesis and by showing that downregulation of these genes affects body size in C. elegans.

Weaknesses:

(1) Although the analysis of the SMA-3 and SMA-9 ChIP-Seq and RNA-Seq data is extremely useful, the goal "to untangle the roles of Smad and Schnurri transcription factors in the developing C. elegans larva", has not been reached. While the role of SMA-3 as a transcriptional activator appears to be quite straightforward, the function of SMA-9 in the BMP signaling remains obscure. The authors write that in SMA-9 mutants, body size is affected, but they do not show any data on the mechanism of this effect.

We thank the reviewer for directing our attention to the lack of clarity about SMA-9’s function. We have revised the text to highlight what this study and others demonstrate about SMA-9’s role in body size. Simply stated, SMA-9 is needed together with SMA-3 to promote the expression of genes involved in one-carbon metabolism, collagens, and chaperones, all of which are required for body size. SMA-3 has additional, SMA-9-independent transcriptional targets, including chaperones and ER secretion factors, that also contribute to body size. Finally, SMA-9 regulates additional targets independent of SMA-3 that likely have a minimal role in body size. We have adjusted Figure 5 with new graphs of the original data to make these points more clear.

(2) The authors clearly show that both TFs can bind independently of each other, however, by using distances between SMA-3 and SMA-9 ChIP peaks, they claim that when the peaks are close these two TFs act as complexes. In the absence of proof that SMA-3 and SMA-9 physically interact (e.g. that they co-immunoprecipitate - as they do in Drosophila), this is an unfounded claim, which should either be experimentally substantiated or toned down.

We acknowledge that we have not demonstrated a physical interaction between SMA-3 and SMA-9 through a co-immunoprecipitation, and we have indicated in the text that a formal biochemical demonstration would be required to make this point. Moreover, we toned down the text by stating that our results suggest that either SMA-3 and SMA-9 frequently bind as either subunits in a complex or in close vicinity to each other along the DNA. As the reviewer has indicated, a physical interaction between Smads and Schnurris has been amply demonstrated in other systems. A limitation in these previous studies is that only a small number of target genes were analyzed. Our goal in this study was to determine how widespread this interaction is on a genomic scale. Our analyses demonstrate for the first time that a Schnurri transcription factor has significant numbers of both Smad-dependent and Smad-independent target genes. We have revised the text to clarify this point.

(3) The second part of the paper (the collagen story) is very loosely connected to the first part. dpy-11 encodes an enzyme important for cuticle development, and it is a differentially expressed direct target of SMA-3. dpy-11 can be bound by SMA-9, but it is not affected by this binding according to RNA-Seq. Thus, technically, this part of the paper does not require any information about SMA-9. However, this can likely be improved by addressing the function of the 15 genes, with the opposing mode of regulation by SMA-3 and SMA-9.

We appreciate this suggestion and have clarified in the text how SMA-9 contributes to collagen organization and body size regulation.

(4) The Discussion does not add much to the paper - it simply repeats the results in a more streamlined fashion.

We thank the reviewer for this suggestion. We have added more context to the Discussion.

Reviewer #2 (Public Review):

In the present study, Vora et al. elucidated the transcription factors downstream of the BMP pathway components Smad and Schnurri in C. elegans and their effects on body size. Using a combination of a broad range of techniques, they compiled a comprehensive list of genome-wide downstream targets of the Smads SMA-3 and SMA-9. They found that both proteins have an overlapping spectrum of transcriptional target sites they control, but also unique ones. Thereby, they also identified genes involved in one-carbon metabolism or the endoplasmic reticulum (ER) secretory pathway. In an elaborate effort, the authors set out to characterize the effects of numerous of these targets on the regulation of body size in vivo as the BMP pathway is involved in this process. Using the reporter ROL-6::wrmScarlet, they further revealed that not only collagen production, as previously shown, but also collagen secretion into the cuticle is controlled by SMA-3 and SMA-9. The data presented by Vora et al. provide in-depth insight into the means by which the BMP pathway regulates body size, thus offering a whole new set of downstream mechanisms that are potentially interesting to a broad field of researchers.

The paper is mostly well-researched, and the conclusions are comprehensive and supported by the data presented. However, certain aspects need clarification and potentially extended data.

(1) The BMP pathway is active during development and growth. Thus, it is logical that the data shown in the study by Vora et al. is based on L2 worms. However, it raises the question of if and how the pattern of transcriptional targets of SMA-3 and SMA-9 changes with age or in the male tail, where the BMP pathway also has been shown to play a role. Is there any data to shed light on this matter or are there any speculations or hypotheses?

We agree that these are intriguing questions, and we are interested in the roles of transcriptional targets at other developmental stages and in other physiological functions, but these analyses are beyond the scope of the current study.

(2) As it was shown that SMA-3 and SMA-9 potentially act in a complex to regulate the transcription of several genes, it would be interesting to know whether the two interact with each other or if the cooperation is more indirect.

A physical interaction between Smads and Schnurri has been amply demonstrated in other systems. Our goal in this study was not to validate this physical interaction, but to analyze functional interactions on a genome-wide scale.

(3) It would help the understanding of the data even more if the authors could specifically state if there were collagens among the genes regulated by SMA-3 and SMA-9 and which.

We thank the reviewer for this suggestion. col-94 and col-153 were identified as direct targets of both SMA-3 and SMA-9. We noted this in the Discussion.

(4) The data on the role of SMA-3 and SMA-9 in the regulation of the secretion of collagens from the hypodermis is highly intriguing. The authors use ROL-6 as a reporter for the secretion of collagens. Is ROL-6 a target of SMA-9 or SMA-3? Even if this is not the case, the data would gain even more strength if a comparable quantification of the cuticular levels of ROL-6 were shown in Figure 6, and potentially a ratio of cuticular versus hypodermal levels. By that, the levels of secretion versus production can be better appreciated.

We previously showed that rol-6 mRNA levels are reduced in dbl-1 mutants at L2, but RNA-seq analysis did not find enough of a statistically significant change in rol-6 to qualify it as a transcriptional target and total levels of protein are also not significantly reduced in mutants. We added this information in the text.

(5) It is known that the BMP pathway controls several processes besides body size. The discussion would benefit from a broader overview of how the identified genes could contribute to body size. The focus of the study is on collagen production and secretion, but it would be interesting to have some insights into whether and how other identified proteins could play a role or whether they are likely to not be involved here (such as the ones normally associated with lipid metabolism, etc.).

We have added more information to the Discussion.

Reviewer #1 (Recommendations For The Authors):

Figure 1 - Figure 3: The authors might want to think about condensing this into two figures.

To avoid confusion with the different workflows, we prefer to keep these as three separate figures.

Figure 1a-b: Measurement unit missing on X.

We added the unit “bps” to these graphs.

Line 244-246: The authors should stress in the Results that they analyzed publicly available ChIP-Seq data, which was not generated by them, - not just by providing a reference to Kudron et al., 2018. As far as I understood, ChIP was performed with an anti-GFP antibody. Please mention this, and specify the information about the vendor and the catalog number in the Methods.

We would like to clarify the status of the publicly available ChIP-seq data. We generated the GFP tagged SMA-3 and SMA‑9 strains and submitted them to be entered into the queue for ChIP-seq processing by the modENCODE (later modERN) consortium. Thus, the publicly available SMA-3 and SMA-9 ChIP-seq datasets used here were derived from our efforts.  Due to the nature of the consortium’s funding, the data were required to be released publicly upon completion. Nevertheless, our current manuscript provides the first comprehensive analysis of these datasets. We have clarified these issues in the text.  We have also added information regarding the anti-GFP antibody to the Methods.

Line 267-270: The authors should either provide experimental evidence that SMA-3 and SMA-9 form complexes or write something like "significant overlap between SMA-3 and SMA-9 peaks may indicate complex formation between these two transcription factors as shown in Drosophila" - but in the absence of proof, this must be a point for the Discussion, not for the Results. Moreover, similar behavior of fat-6 (overlapping ChIP peaks) and nhr-114 (non-overlapping ChIP peaks) in SMA-3 and SMA-9 mutants may be interpreted as a circumstantial argument against SMA-3/SMA-9 complex formation (see Lines 342-348). Importantly, since ChIP-Seq data are available for a wide array of C. elegans TFs, it would be very useful to have an estimate of whether SMA-3/SMA-9 peak overlap is significantly higher than the peak overlap between SMA-3 and several other TFs expressed at the same L2 stage.

We have clarified our goals regarding SMA-3 and SMA-9 interactions and softened our conclusions by indicating in the text that a formal biochemical demonstration would be required to demonstrate a physical interaction. Moreover, we toned down the text by stating that our results suggest that either SMA-3 and SMA-9 frequently bind as either subunits in a complex or in close vicinity to each other along the DNA. We have added an analysis of HOT sites to address overlap of binding with other transcription factors. We disagree with the interpretation that transcription factors with non-overlapping sites cannot act together to regulate gene expression; however, nhr-114 also has an overlapping SMA-3 and SMA-9 site, so this point becomes less relevant. We have clarified the categorization of nhr-114 in the text.

Lines 272-292: The authors do not comment on the seemingly quite small overlap between the RNA-Seq and the ChIP-Seq dataset, but I think they should. They have 3205 SMA-3 ChIP peaks and 1867 SMA-3 DEGs, but the amount of directly regulated targets is 367. It is important that the authors provide information on the number of genes to which their peaks have been assigned. Clearly, this will not be one gene per peak, but if it were, this would mean that just 11.5% of bound targets are really affected by the binding. The same number would be 4.7% for the SMA-9 peaks.

We have added a discussion of the discrepancy between binding sites and DEGs. The high number of additional sites classified as non-functional could represent the detection of weak affinity targets that do not have an actual biological purpose. Alternatively, these sites could have an additional role in DBL-1 signaling besides transcriptional regulation of nearby genes, or they could be regulating the expression of target genes at a far enough distance to not be detected by our BETA analysis as per the constraints chosen for the analysis. The difference between total binding sites and those associated with changes in gene expression underscores the importance of combining RNA-seq with ChIP-seq to identify the most biologically relevant targets. And as the reviewer indicated, more than one gene can be assigned to a single neighboring peak.

Lines 294-323: I feel like there is a terminology problem, which makes reading very difficult. The authors use "direct targets" as bound genes with significant expression change, but then run into a problem when the gene is bound by SMA-9 and SMA-3, but significant expression change is only associated with one of the two factors. I am not sure this is consistent with the idea of the SMA3/SMA9 complex. Also, different modalities of the SMA3 and SMA9 effect in 15 cases can be explained by co-factors. Reading would be also simplified if the order of the panels in Figure 3 were different. Currently, the authors start their explanation by referring to the shared SMA-3/SMA-9 targets (Figures 3c-d), and only later come to Figure 3b. In general, the authors should start with a clear explanation of what is on the figure (currently starting on Line 313), otherwise, it is unclear why, if the authors only discuss common targets, it is not just 114+15=129 targets, but more.

We have re-ordered the columns in Figure 3 to match the order discussed in the text. We also incorporated more precise language about regulation by SMA-3 and/or SMA-9 in the text.

Lines 325-355: The chapter has a rather unfortunate name "Mechanisms of integration of SMA-3 and SMA-9 function", although the authors do not provide any mechanism. Using 3 target genes, they show that if the regulatory modality of SMA-3 and SMA-9 is the same (2 examples), there is no difference in the expression of the targets, but if the modalities are opposing (1 example), SMA-9 repressive action is epistatic to the SMA-3 activating action. Can this be generalized? The authors should test all their 15 targets with opposite regulations. Moreover, it seems obvious to ask whether the intermediate phenotype of the double-mutants can be attributed to the action of these 15 genes activated by SMA-3 and repressed by SMA-9. I would suggest testing this by RNAi. I would also suggest renaming the chapter to something better reflecting its content.

We have removed the word “mechanism” from the title of this section. We also performed additional RT-PCR experiments on another 5 targets with opposing directions of regulation. The results from these genes are consistent with the result from C54E4.5, demonstrating that the epistasis of sma-9 is generalizable.

Figure 4b: Why was a two-way ANOVA performed here? With the small number of measurements, I would consider using a non-parametric test.

These data are parametric and the distribution of the data is normal, so we chose to use a parametric test (ANOVA).

Lines 354-355. The authors offer two suggestions for the mechanism of the epistatic action of SMA-9 on SMA-3 in the case of C54E4.5, but this is something for the Discussion. If they want to keep it in the Results they should address this experimentally by performing SMA-3 ChIP-seq in the SMA-9 mutants and SMA-9 ChIP-Seq in the SMA-3 mutants.

We moved these models to the discussion as suggested.

Lines 365-367: "We expect that clusters of genes involved in fatty acid metabolism and innate immunity mediate the physiological functions of BMP signaling in fat storage and pathogen resistance, respectively." - This is pretty confusing since the Authors claim in the previous sentence that regulation of immunity by SMA-9 is TGF-beta independent.

Co-regulation of immunity by BMP signaling and SMA-9 is already known. The novel insight is that SMA-9 may have an additional independent role in immunity. We have clarified the language to address this confusion.

Lines 377, and 380: Please explain in non-C. elegans-specific terminology, what rrf-3 and LON-2 are (e.g. write "glypican LON-2" instead of just "LON-2") and add relevant references.

We added information on the proteins encoded by these genes.

Lines 382-384: I am not sure what the Authors mean here by "more limiting".

We substituted the phrase “might have a more prominent requirement in mediating the exaggerated growth defect of a lon-2 mutant”.

Lines 388-392: I found this very confusing. What were these 36 genes? Were these direct targets of SMA-3, SMA-9, or both? Top 36 targets? 36 targets for which mutants are available?

The new Figure 5 clarifies whether target genes are SMA-3-exclusive, SMA-9-exclusive, or co-regulated. The text was also updated for clarity.

Line 397: This is the first time the authors mention dpy-11 but they do not say what it is until later, and they do not say whether it is a target of SMA3/SMA9. Checking Figure 3, I found that it is among the 238 genes bound by both but upregulated only by SMA3. The authors need to explicitly state this - from this point on, they have a section for which SMA-9 appears to be irrelevant.

We added the molecular function of dpy-11 at its first mention. Furthermore, we included the hypothesis that SMA-3 may regulate collagen secretion independently of SMA-9. Our subsequent results with sma-9 mutants disprove this hypothesis.

Line 402: Is ROL-6 a SMA-3/SMA-9 target or just a marker gene?

We previously showed that rol-6 mRNA levels are reduced in dbl-1 mutants at L2, but RNA-seq analysis did not find enough of a statistically significant change in rol-6 to qualify it as a transcriptional target and total levels of protein are also not significantly reduced in mutants. We added this information in the text.

Line 421: I am not sure what "more skeletonized" means.

Replaced with “thinner and skeletonized”

Figure 2b and 2d legends: "Non-target genes nevertheless showing differential expression are indicated with green squares." (l. 581-582 and again l. 588-589) I think should be "Non-direct target genes...".

Changed to “non-direct target genes”

Figure 7 legend: Please indicate the scale bar size in the legend.

Indicated the scale bar size in the legend.

Figure 7: The ER marker is referred to as "ssGFP::KDEL" (in the image and Line 700), however in the text it is called "KDEL::oxGFP" (Line 419). Please use consistent naming.

We fixed the inconsistent naming.

All the experiment suggestions made are optional and can, in principle, be ignored if the authors tone down their claims (for example, the SMA-3/SMA-9 complex formation).

Reviewer #2 (Recommendations For The Authors):

(1) As a control: Have the authors found the known regulated genes among the differentially regulated ones?

Previously known target genes such as fat-6 and zip-10 were identified here. We have added this information in the text.

(2) How many repetitions were performed in Figure 4b? I am wondering as the deviation for C54E4.5 is quite large and that makes me worry that the significant differences stated are not robust.

There were two biologically independent collections from which three cDNA syntheses were analyzed using two technical replicates per point.

(3) Lines 333-336: Can you really make this claim that the antagonistic effects seen in the regulation of body size can be correlated with some targets being regulated in the opposite direction? I would assume that the situation is far more complex as SMADs also regulate other processes.

We agree with the reviewer that multiple models could explain this antagonism, and we have added distinct alternatives in the text.

(4) Lines 367-369: Add the respective reference please.

We have added the relevant references.

eLife Assessment

This valuable paper describes a comprehensive quantitative phospho-proteomic analysis of Xenopus oocytes during meiosis. Using time-resolved proteomic analyses, the authors provide insights into changes in protein levels and phosphorylation states to an unprecedented depth, quality, and quantitative detail. The key findings are solid and offer a helpful resource for the scientific community.

Reviewer #1 (Public review):

Summary:

The study aims to create a comprehensive repository about the changes in protein abundance and their modification during oocyte maturation in Xenopus laevis.

Strengths:

The results contribute meaningfully to the field.

Weaknesses:

The manuscript could have benefitted from more comprehensive analyses and clearer writing. Nonetheless, the key findings are robust and offer a valuable resource for the scientific community.

Reviewer #2 (Public review):

Summary:

The authors analyzed Xenopus oocytes at different stages of meiosis using quantitative phosphoproteomics. Their advanced methods and analyses revealed changes in protein abundances and phosphorylation states to an unprecedented depth and quantitative detail. In the manuscript they provide an excellent interpretation of these findings putting them in the context of past literature in Xenopus as well as in other model systems.

Strengths:

High quality data, careful and detailed analysis, outstanding interpretation in the context of the large body of the literature.

Weaknesses:

Merely a resource, none of the findings are tested in functional experiments.

I am very impressed by the quality of the data and the careful and detailed interpretation of the findings. In this form the manuscript will be an excellent resource to the cell division community in general, and it presents a very large number of hypotheses that can be tested in future experiments.

Xenopus has been and still is a popular and powerful model system that led to critical discoveries around countless cellular processes, including the spindle, nuclear envelope, translational regulation, just to name a few. This also includes a huge body of literature on the cell cycle describing its phosphoregulation. It is indeed somewhat frustrating to see that these earlier studies using phospho-mutants and phospho-antibodies were just scratching the surface. The phosphoproteomics analysis presented here reveals much more extensive and much more dynamic changes in phosphorylation states. Thereby, in my opinion, this manuscript opens a completely new chapter in this line of research, setting the stage for more systematic future studies.

Reviewer #3 (Public review):

Summary:

The authors performed time-resolved proteomics and phospho-proteomics in Xenopus oocytes from prophase I through the MII arrest of the unfertilized egg. The data contains protein abundance and phosphorylation sites of a large number set of proteins at different stages of oocyte maturation. The large sets of the data are of high quality. In addition, the authors discussed several key pathways critical for the maturation. The data is very useful for the researchers not only researchers in Xenopus oocytes but also those in oocyte biology in other organisms.

Strengths:

The data of proteomics and phospho-proteomics in Xenopus oocyte maturation is very useful for future studies to understand molecular networks in oocyte maturation.

Weaknesses:

Although the authors offered molecular pathways of the phosphorylation in the translation, protein degradation, cell cycle regulation, and chromosome segregation. The author did not check the validity of the molecular pathways based ontheir proteomic data by the experimentation.

Author response:

We are both honored and humbled by the high praise our work received from all three reviewers. Below, we address the common comments made by the reviewers:

(1) Value and Impact of the Resource: We are grateful for the recognition of our dataset as a valuable and high-quality resource. Our primary goal was to generate a comprehensive dataset on protein abundance and phosphorylation dynamics during Xenopus oocyte maturation. We are pleased that this work has been seen as a solid foundation for future studies in Xenopus research and beyond, with broader implications for oocyte and cell cycle biology.

(2) Focus on Functional Validation and Contextualization with Prior Studies: The manuscript was submitted as a Tools and Resources article, a format that emphasizes the creation and presentation of datasets, tools, and methodological advances to facilitate future discoveries. In alignment with this format, we ensured that the information is accessible and deployable for the broader scientific community. While we did not include functional validation of specific pathways, the dataset provides a robust framework for generating numerous testable hypotheses. We plan to pursue some of these follow-up studies in our labs and encourage the community to explore these further.

(3) Contextualization with Prior Studies: We appreciate the recognition of our efforts to integrate our findings with the existing body of literature. In conclusion, we would like to thank the reviewers for their evaluation and thoughtful suggestions. We look forward to seeing how this dataset contributes to future discoveries in the field.

eLife Assessment

In this important study, the authors combine innovative experimental approaches, including direct compressibility measurements and traction force analyses, with theoretical modeling to propose that wild-type cells exert compressive forces on softer HRasV12-transformed cells, influencing competition outcomes. The data generally provide solid evidence that transformed epithelial cells exhibit higher compressibility than wild-type cells, a property linked to their compaction during mechanical cell competition. However, the study would benefit from further characterization of how compression affects the behavior of HRasV12 cells and clearer causal links between compressibility and competition outcomes.

Reviewer #1 (Public review):

Summary:

In this article, Gupta and colleagues explore the parameters that could promote the elimination of active Ras cells when surrounded by WT cells. The elimination of active Ras cells by surrounding WT cells was previously described extensively and associated with a process named cell competition, a context dependant elimination of cells. Several mechanisms have been associated with competition, including more recently elimination processes based on mechanical stress. This was explored theoretically and experimentally and was either associated with differential growth and sensitivity to pressure and/or differences in homeostatic density/pressure. This was extensively validated for the case of Scribble mutant cells which are eliminated by WT MDCK cells due to their higher homeostatic density. However, there has been so far very little systematic characterisation of the mechanical parameters and properties of these different cell types and how this could contribute to mechanical competition.

Here, the authors used the context of active Ras cells in MDCK cells (with some observations in vivo in mice gut which are a bit more anecdotal) to explore the parameters causal to Ras cell elimination. Using for the first time traction force microscopy, stress microscopy combined with Bayesian inference, they first show that clusters of active Ras cells experience higher pressure compared to WT. Interestingly, this occurs in absence of differences in growth rate, and while Ras cells seems to have lower homeostatic density, in contractions with the previous models associated with mechanical cell competition. Using a self-propelled Voronoi model, they explored more systematically the conditions that will promote the compression of transformed cells, showing globally that higher Area compressibility and/or lower junctional tension are associated with higher compressibility. Using then an original and novel experimental method to measure bulk compressibility of cell populations, they confirmed that active Ras cells are globally twice more compressible than WT cells. This compressibility correlates with a disruption of adherens junctions. Accordingly, the higher pressure near transformed Ras cells can be completely rescued by increasing cell-cell adhesion through E-cad overexpression, which also reduces the compressibility of the transformed cells. Altogether, these results go along the lines of a previous theoretical work (Gradeci et al. eLife 2021) which was suggesting that reduced stiffness/higher compressibility was essential to promote loser cell elimination. Here, the authors provide for the first time a very convincing experimental measurement and validation of this prediction. Moreover, their modelling approach goes far beyond what was performed before in terms of exploration of conditions promoting compressibility, and their experimental data point at alternative mechanisms that may contribute to mechanical competition.

Strengths:

- Original methodologies to perform systematic characterisation of mechanical properties of Ras cells during cell competition, which include a novel method to measure bulk compressibility.<br /> - A very extensive theoretical exploration of the parameters promoting cell compaction in the context of competition.

Weaknesses:

- Most of the theoretical focus is centred on the bulk compressibility, but so far does not really explain the final fate of the transformed cells. Classic cell competition scenario (including the one involving active Ras cells) lead to the elimination of one cell population either by cell extrusion/cell death or global delamination. This aspect is absolutely not explored in this article, experimentally or theoretically, and as such it is difficult to connect all the observables with the final outcome of cell competition. For instance, higher compressibility may not lead to loser status if the cells can withstand high density without extruding compared to the WT cells (and could even completely invert the final outcome of the competition). Down the line, and as suggested in most of the previous models/experiments, the relationship between pressure/density and extrusion/death will be the key factor that determine the final outcome of competition. However, there is absolutely no characterisation of cell death/cell extrusion in the article so far.

- While the compressibility measurement are very original and interesting, this bulk measurement could be explained by very different cellular processes, from modulation of cell shape, to cell extrusion and tissue multilayering (which by the way was already observed for active Ras cells, see for instance https://pubmed.ncbi.nlm.nih.gov/34644109/). This could change a lot the interpretation of this measurement and to which extend it can explain the compression observed in mixed culture. This compressibility measurement could be much more informative if coupled with an estimation of the change of cell aspect ratio and the rough evaluation of the contribution of cell shape changes versus alternative mechanisms.

- So far, there is no clear explanation of why transformed Ras cells get more compacted in the context of mixed culture compared to pure Ras culture. Previously, the compaction of mutant Scribble cells could be explained by the higher homeostatic density of WT cells which impose their prefered higher density to Scribble mutant (see Wagstaff et al. 2016 or Gradeci et al 2021), however that is not the case of the Ras cells (which have even slightly higher density at confluency). If I understood properly, the Voronoid model assumes some directional movement of WT cell toward transformed which will actively compact the Ras cells through self-propelled forces (see supplementary methods), but this is never clearly discussed/described in the results section, while potentially being one essential ingredient for observing compaction of transformed cells. In fact, this was already described experimentally in the case of Scribble competition and associated with chemoattractant secretion from the mutant cells promoting directed migration of the WT (https://pubmed.ncbi.nlm.nih.gov/33357449/). It would be essential to show what happens in absence of directional propelled movement in the model and validate experimentally whether there is indeed directional movement of the WT toward the transformed cells. Without this, the current data does not really explain the competition process.

- Some of the data lack a bit of information on statistic, especially for all the stress microscopy and traction forces where we do no really know how representative at the stress patterns (how many experiment, are they average of several movies ? integrated on which temporal window ?)

Reviewer #2 (Public review):

The work by Gupta et al. addresses the role of tissue compressibility as a driver of cell competition. The authors use a planar epithelial monolayer system to study cell competition between wild type and transformed epithelial cells expressing HRasV12. They combine imaging and traction force measurements from which the authors propose that wild type cells generate compressive forces on transformed epithelial cells. The authors further present a novel setup to directly measure the compressibility of adherent epithelial tissues. These measurements suggest a higher compressibility of transformed epithelial cells, which is causally linked to a reduction in cell-cell adhesion in transformed cells. The authors support their conclusions by theoretical modelling using a self-Propelled Voronoi model that supports differences in tissue compressibility can lead to compression of the softer tissue type.

The experimental framework to measure tissue compressibility of adherent epithelial monolayers establishes a novel tool, however additional controls of this measurement appear required. Moreover, the experimental support of this study is mostly based on single representative images and would greatly benefit from additional data and their quantitative analysis to support the authors' conclusions. Specific comments are also listed in the following:

Major points:

It is not evident in Fig2A that traction forces increase along the interface between wild type and transformed populations and stresses in Fig2C also seem to be similar at the interface and surrounding cell layer. Only representative examples are provided and a quantification of sigma_m needs to be provided.

In Figure 1-3 only panel 2G and 2H provide a quantitative analysis, but it is not clear how many regions of interest and clusters of transform cells were quantified.

Several statements appear to be not sufficiently justified and supported by data.<br /> For example the statement on pg 3. line 38 seems to lack supportive data 'This comparison revealed that the thickness of HRasV12-expressing cells was reduced by more than 1.7-fold when they were surrounded by wild type cells. These observations pointed towards a selective, competition-dependent compaction of HRasV12-expressing transformed cells but not control cells, in the intestinal villi of mice.'<br /> Similarly, the statement about a cell area change of 2.7 fold (pg 3 line 47) lacks support by measurements.

What is the rationale for setting 𝐾p = 1 in the model assumptions if clear differences in junctional membranes of transformed versus wild type cells occur, including dynamic ruffling? This assumption does not seem to be in line with biological observations.

The novel approach to measure tissue compressibility is based on pH dependent hydrogels. As the pH responsive hydrogel pillar is placed into a culture medium with different conditions, an important control would be if the insertion of this hydrogel itself would change the pH or conditions of the culture assays and whether this alters tissue compressibility or cell adhesion. The authors could for example insert a hydrogel pillar of a smaller diameter that would not lead to compression or culture cells in a larger ring to assess the influence of the pillar itself.

The authors focus on the study of cell compaction of the transformed cells, but how does this ultimately lead to a competitive benefit of wild type cells? Is a higher rate of extrusion observed and associated with the compaction of transformed cells or is their cell death rate increased? While transformed cells seem to maintain a proliferative advantage it is not clear which consequences of tissue compression ultimately drive cell competition between wild type and transformed cells.

The argumentation that softer tissues would be more easily compressed is plausible. However, which mechanism do the authors suggest is generating the actual compressive stress to drive the compaction of transformed cells? They exclude a proliferative advantage of wild type cells, which other mechanisms will generate the compressive forces by wild type cells?

Author response:

eLife Assessment:

In this important study, the authors combine innovative experimental approaches, including direct compressibility measurements and traction force analyses, with theoretical modeling to propose that wild-type cells exert compressive forces on softer HRasV12-transformed cells, influencing competition outcomes. The data generally provide solid evidence that transformed epithelial cells exhibit higher compressibility than wild-type cells, a property linked to their compaction during mechanical cell competition. However, the study would benefit from further characterization of how compression affects the behavior of HRasV12 cells and clearer causal links between compressibility and competition outcomes.

We thank the reviewers and the editor for their thoughtful and encouraging feedback on our study and for appreciating the innovation in our experimental and theoretical approaches. We acknowledge the importance of further clarifying the mechanistic links between the compressibility of HRas^V12-transformed cells, their compaction, and the outcomes of mechanical cell competition. In the revised manuscript, we will include additional experiments and analyses to assess how compression influences the cellular behavior and fate of HRas^V12-transformed cells during competition. In addition, to strengthen the connection between collective compressibility and competition outcomes, we will integrate quantitative analyses of cell dynamics and additional modeling to explicitly correlate the mechanical properties with the spatial and temporal aspects of cell elimination. These additions will address the reviewer’s concerns comprehensively, further enriching the mechanistic understanding presented in the manuscript.

Public Reviews:

Reviewer #1 (Public review):

Summary:

In this article, Gupta and colleagues explore the parameters that could promote the elimination of active Ras cells when surrounded by WT cells. The elimination of active Ras cells by surrounding WT cells was previously described extensively and associated with a process named cell competition, a context dependant elimination of cells. Several mechanisms have been associated with competition, including more recently elimination processes based on mechanical stress. This was explored theoretically and experimentally and was either associated with differential growth and sensitivity to pressure and/or differences in homeostatic density/pressure. This was extensively validated for the case of Scribble mutant cells which are eliminated by WT MDCK cells due to their higher homeostatic density. However, there has been so far very little systematic characterisation of the mechanical parameters and properties of these different cell types and how this could contribute to mechanical competition.

Here, the authors used the context of active Ras cells in MDCK cells (with some observations in vivo in mice gut which are a bit more anecdotal) to explore the parameters causal to Ras cell elimination. Using for the first time traction force microscopy, stress microscopy combined with Bayesian inference, they first show that clusters of active Ras cells experience higher pressure compared to WT. Interestingly, this occurs in absence of differences in growth rate, and while Ras cells seems to have lower homeostatic density, in contractions with the previous models associated with mechanical cell competition. Using a self-propelled Voronoi model, they explored more systematically the conditions that will promote the compression of transformed cells, showing globally that higher Area compressibility and/or lower junctional tension are associated with higher compressibility. Using then an original and novel experimental method to measure bulk compressibility of cell populations, they confirmed that active Ras cells are globally twice more compressible than WT cells. This compressibility correlates with a disruption of adherens junctions. Accordingly, the higher pressure near transformed Ras cells can be completely rescued by increasing cell-cell adhesion through E-cad overexpression, which also reduces the compressibility of the transformed cells. Altogether, these results go along the lines of a previous theoretical work (Gradeci et al. eLife 2021) which was suggesting that reduced stiffness/higher compressibility was essential to promote loser cell elimination. Here, the authors provide for the first time a very convincing experimental measurement and validation of this prediction. Moreover, their modelling approach goes far beyond what was performed before in terms of exploration of conditions promoting compressibility, and their experimental data point at alternative mechanisms that may contribute to mechanical competition.

Strengths:

- Original methodologies to perform systematic characterisation of mechanical properties of Ras cells during cell competition, which include a novel method to measure bulk compressibility.<br /> - A very extensive theoretical exploration of the parameters promoting cell compaction in the context of competition.

We thank the reviewer for their detailed and thoughtful assessment of our study and for recognizing the originality of our methodologies, including the novel bulk compressibility measurement technique and the extensive theoretical exploration of parameters influencing mechanical competition. We are pleased that the reviewer finds our experimental validation and modeling approach convincing and acknowledges the relevance of our findings in advancing the understanding of mechanical cell competition. We will carefully address all the points raised to further clarify and strengthen the manuscript.

Weaknesses:

- Most of the theoretical focus is centred on the bulk compressibility, but so far does not really explain the final fate of the transformed cells. Classic cell competition scenario (including the one involving active Ras cells) lead to the elimination of one cell population either by cell extrusion/cell death or global delamination. This aspect is absolutely not explored in this article, experimentally or theoretically, and as such it is difficult to connect all the observables with the final outcome of cell competition. For instance, higher compressibility may not lead to loser status if the cells can withstand high density without extruding compared to the WT cells (and could even completely invert the final outcome of the competition). Down the line, and as suggested in most of the previous models/experiments, the relationship between pressure/density and extrusion/death will be the key factor that determine the final outcome of competition. However, there is absolutely no characterisation of cell death/cell extrusion in the article so far.

We thank the reviewer for highlighting this important point. We agree that understanding the relationship between pressure, density, and the final outcomes of cell competition, such as extrusion and cell death, is crucial to connecting the mechanical properties to competition outcomes. While extrusion and cell death have been extensively characterized in previous works (e.g., https://www.nature.com/articles/s41467-021-27896-z; https://www.nature.com/articles/ncb1853), we nevertheless recognize the need to address this aspect more explicitly in our study. To this end, we have indeed performed experiments to characterize cell extrusion and cell death under varying conditions of pressure and density. We will incorporate these data into the revised manuscript. These additions will provide a more comprehensive understanding of how mechanical imbalance drives cell competition and determine the final fate of transformed cells.

- While the compressibility measurement are very original and interesting, this bulk measurement could be explained by very different cellular processes, from modulation of cell shape, to cell extrusion and tissue multilayering (which by the way was already observed for active Ras cells, see for instance https://pubmed.ncbi.nlm.nih.gov/34644109/). This could change a lot the interpretation of this measurement and to which extend it can explain the compression observed in mixed culture. This compressibility measurement could be much more informative if coupled with an estimation of the change of cell aspect ratio and the rough evaluation of the contribution of cell shape changes versus alternative mechanisms.

We thank the reviewer for raising this important concern. In our model system and within the experimental timescale of our studies involving gel compression microscopy (GCM) experiments, we do not observe tissue multilayering and cell extrusion, as these measurements are performed on homogeneous populations (pure wild-type or pure transformed cell monolayer). However, to address the reviewer’s suggestion, we will include measurements of cell aspect ratio as well as images eliminating the possibility of multilayering/extrusion in the revised manuscript. These results will provide additional insights into the plausible contributions of cell shape changes. Furthermore, our newer results indicate that the compressibility differences arise from variations in the intracellular organization (changed in nuclear and cytoskeletal organization) between wild-type and transformed cells. While a detailed molecular characterization of these underlying mechanisms is beyond the scope of the current manuscript, we acknowledge its importance and plan to explore it in a future study. These revisions will clarify and strengthen the interpretation of our findings.

- So far, there is no clear explanation of why transformed Ras cells get more compacted in the context of mixed culture compared to pure Ras culture. Previously, the compaction of mutant Scribble cells could be explained by the higher homeostatic density of WT cells which impose their prefered higher density to Scribble mutant (see Wagstaff et al. 2016 or Gradeci et al 2021), however that is not the case of the Ras cells (which have even slightly higher density at confluency). If I understood properly, the Voronoid model assumes some directional movement of WT cell toward transformed which will actively compact the Ras cells through self-propelled forces (see supplementary methods), but this is never clearly discussed/described in the results section, while potentially being one essential ingredient for observing compaction of transformed cells. In fact, this was already described experimentally in the case of Scribble competition and associated with chemoattractant secretion from the mutant cells promoting directed migration of the WT (https://pubmed.ncbi.nlm.nih.gov/33357449/). It would be essential to show what happens in absence of directional propelled movement in the model and validate experimentally whether there is indeed directional movement of the WT toward the transformed cells. Without this, the current data does not really explain the competition process.

We introduced directional movement of wild-type cells towards neighbouring transformed cells (and a form of active force to be exerted by them), motivated by the tissue compressibility measurements from the Gel Compression Microscopy experiments (Fig. 4E-L). This allowed us to devise an equivalent method of measuring the material response to isotropic compression within the SPV model framework. While the role of directional propelled movement is an area of ongoing investigation and has not been explored extensively within the current study, we emphasize that even without directional propulsion in the model, our results demonstrate compressive stress or elevated pressure, and increased compaction within the transformed population under suitable conditions reported in this work (when k<1), exhibiting a greater tissue-level compressibility in the transformed cells compared to WT cells (Figs. 4C-D), thereby laying the ground for competition. To clarify these concerns, we will provide additional results as well as detailed discussions on the effect of cell movements in compression.

- Some of the data lack a bit of information on statistic, especially for all the stress microscopy and traction forces where we do no really know how representative at the stress patterns (how many experiment, are they average of several movies ? integrated on which temporal window ?)

We thank the reviewer for highlighting the need for additional details regarding the statistical representation of our stress microscopy and traction force data. We will address these concerns in the revised manuscript by providing clear descriptions of the number of experiments, the averaging methodology, and the temporal windows used for analysis. Currently, Figs. 2A and 2C represent data from single time points, as the traction and stress landscapes evolve dynamically as transformed cells begin extruding (as shown in Supplementary movie 1). In contrast, Fig. 2H represents data collected from several samples across three independent experiments, all measured at the 3-hour time point following doxycycline induction. This specific time point is critical because it captures the emergence of compressive stresses before extrusion begins, simplifying the analysis and ensuring consistency. We will ensure these details are clearly articulated in the revised text and figure legends.

Reviewer #2 (Public review):

The work by Gupta et al. addresses the role of tissue compressibility as a driver of cell competition. The authors use a planar epithelial monolayer system to study cell competition between wild type and transformed epithelial cells expressing HRasV12. They combine imaging and traction force measurements from which the authors propose that wild type cells generate compressive forces on transformed epithelial cells. The authors further present a novel setup to directly measure the compressibility of adherent epithelial tissues. These measurements suggest a higher compressibility of transformed epithelial cells, which is causally linked to a reduction in cell-cell adhesion in transformed cells. The authors support their conclusions by theoretical modelling using a self-Propelled Voronoi model that supports differences in tissue compressibility can lead to compression of the softer tissue type.

The experimental framework to measure tissue compressibility of adherent epithelial monolayers establishes a novel tool, however additional controls of this measurement appear required. Moreover, the experimental support of this study is mostly based on single representative images and would greatly benefit from additional data and their quantitative analysis to support the authors' conclusions. Specific comments are also listed in the following:

Major points:

It is not evident in Fig2A that traction forces increase along the interface between wild type and transformed populations and stresses in Fig2C also seem to be similar at the interface and surrounding cell layer. Only representative examples are provided and a quantification of sigma_m needs to be provided.

In Figure 1-3 only panel 2G and 2H provide a quantitative analysis, but it is not clear how many regions of interest and clusters of transform cells were quantified.

We thank the reviewer for their detailed comments and for highlighting the importance of additional quantitative analyses to support our conclusions. We appreciate their recognition of our novel experimental framework to measure tissue compressibility and the overall approach of our study. Regarding Fig. 2A and Fig. 2C, we acknowledge the need for further clarity. While the traction forces and stress patterns may not appear uniformly distinct at the interface in the representative images, these differences are more evident at specific time points before extrusion begins. Please note that the traction and stress landscapes evolve dynamically as transformed cells begin extruding (as shown in Supplementary movie 1). We will include a quantification of σ_m​ and additional data from multiple experiments to substantiate the observations and address this concern in the revised manuscript. Currently, the data in Fig. 2G and Fig. 2H represent several regions of interest and transformed cell clusters collected from three independent experiments, all analyzed at the 3-hour time point after doxycycline induction. This time point was chosen because it captures the compressive stress emergence without interference from extrusion processes, simplifying the analysis. We will expand these sections with detailed descriptions of the sample sizes and statistical analyses to ensure greater transparency and reproducibility. These revisions will provide a stronger quantitative foundation for our findings and address the reviewer's concerns.

Several statements appear to be not sufficiently justified and supported by data.<br /> For example the statement on pg 3. line 38 seems to lack supportive data 'This comparison revealed that the thickness of HRasV12-expressing cells was reduced by more than 1.7-fold when they were surrounded by wild type cells. These observations pointed towards a selective, competition-dependent compaction of HRasV12-expressing transformed cells but not control cells, in the intestinal villi of mice.'  Similarly, the statement about a cell area change of 2.7 fold (pg 3 line 47) lacks support by measurements.

We thank the reviewer for pointing out the need for more supportive data to justify several statements in the manuscript. Specifically, the observation regarding the reduction in the thickness of HRas^V12-expressing cells by more than 1.7-fold when surrounded by wild-type cells, and the statement about a 2.7-fold change in cell area, will be supported by detailed measurements. In the revised manuscript, we will include quantitative analyses with additional figures that clearly document these changes. These figures will provide representative images, statistical summaries, and detailed descriptions of the measurements to substantiate these claims. We appreciate the reviewer highlighting these areas and will ensure that all statements are robustly backed by data.

What is the rationale for setting 𝐾p = 1 in the model assumptions if clear differences in junctional membranes of transformed versus wild type cells occur, including dynamic ruffling? This assumption does not seem to be in line with biological observations.

While the specific role of K_p in the differences observed in the junctional membranes of transformed versus WT cells, including dynamical ruffling, is not directly studied in this work, our findings indicate that the lower junctional tension (weaker and less stable cellular junctions) in mutant cells is influenced primarily by competition in the dimensionless cell shape index within the model. This also suggests a larger preferred cell perimeter (P₀) for mutant cells, corresponding to their softer, unjammed state. Huang et al. (https://doi.org/10.1039/d3sm00327b) have previously argued that a high P₀ may, in some cases, result from elevated cortical tension along cell edges, or reflect weak membrane elasticity, implying a smaller K_p. While this connection could be an intriguing avenue for future exploration, we emphasize that K_p is not expected to alter any of the key findings or conclusions reported in this work. We will include any required analysis and corresponding discussions in the revised manuscript.

The novel approach to measure tissue compressibility is based on pH dependent hydrogels. As the pH responsive hydrogel pillar is placed into a culture medium with different conditions, an important control would be if the insertion of this hydrogel itself would change the pH or conditions of the culture assays and whether this alters tissue compressibility or cell adhesion. The authors could for example insert a hydrogel pillar of a smaller diameter that would not lead to compression or culture cells in a larger ring to assess the influence of the pillar itself.

We appreciate the reviewer’s insightful comment regarding the potential effects of the pH-responsive hydrogel pillar on the culture conditions and tissue compressibility. In our experiments, the expandable hydrogels are kept separate from the cells until the pH of the hydrogel is elevated to 7.4, ensuring that the hydrogel does not impact the culture environment. However, we acknowledge the concern and will include additional controls in the revised manuscript. Specifically, we will insert a hydrogel pillar with a smaller diameter that would not induce compression on culture cells in a larger ring to assess any potential influence of the hydrogel pillar itself. This will help to further validate our experimental setup.

The authors focus on the study of cell compaction of the transformed cells, but how does this ultimately lead to a competitive benefit of wild type cells? Is a higher rate of extrusion observed and associated with the compaction of transformed cells or is their cell death rate increased? While transformed cells seem to maintain a proliferative advantage it is not clear which consequences of tissue compression ultimately drive cell competition between wild type and transformed cells.

We thank the reviewer for highlighting this important point. We agree that understanding how tissue compression leads to a competitive advantage for wild type cells is crucial. While our current study focuses on the mechanical properties of transformed cells leading to the compaction and subsequent extrusion of the transformed cells, we recognize the need to explicitly connect these properties to the final outcomes of cell competition, such as extrusion or cell death. Although extrusion and cell death have been extensively characterized in previous studies (e.g., https://www.nature.com/articles/s41467-021-27896-z; https://www.nature.com/articles/ncb1853), we have indeed performed additional experiments to investigate the relationship between pressure, density, and these processes in our system. In the revised manuscript, we will include these new data, which will help to clarify how mechanical stress, driven by tissue compression, contributes to the competition between wild type and transformed cells and influences their eventual fate.

The argumentation that softer tissues would be more easily compressed is plausible. However, which mechanism do the authors suggest is generating the actual compressive stress to drive the compaction of transformed cells? They exclude a proliferative advantage of wild type cells, which other mechanisms will generate the compressive forces by wild type cells?

We thank the reviewer for raising this important question. As rightly pointed out by the reviewer indeed in our model system, we do not observe a proliferative advantage for the wild-type cells, and the compressive forces exerted by the wild-type cells are due to their intrinsic mechanical properties, such as lesser compressibility compared to the transformed cells. This difference in compressibility results in wild-type cells generating compressive stress at the interface with the transformed cells. Regarding the mechanism underlying the increased compressibility of the transformed cells, our newer findings indicate that the differences in compressibility arise from variations in the intracellular organization, specifically changes in nuclear and cytoskeletal organization between wild-type and transformed cells. While a detailed molecular characterization of these mechanisms is beyond the scope of the current manuscript, we acknowledge its significance and plan to investigate it in future work. We will, nevertheless, include a detailed discussion on the mechanism underlying the differential compressibility of wild-type and transformed cells in the revised manuscript.

eLife Assessment

In this important study, the authors combine innovative experimental approaches, including direct compressibility measurements and traction force analyses, with theoretical modeling to propose that wild-type cells exert compressive forces on softer HRasV12-transformed cells, influencing competition outcomes. The data generally provide solid evidence that transformed epithelial cells exhibit higher compressibility than wild-type cells, a property linked to their compaction during mechanical cell competition. However, the study would benefit from further characterization of how compression affects the behavior of HRasV12 cells and clearer causal links between compressibility and competition outcomes.

Reviewer #1 (Public review):

Summary:

In this article, Gupta and colleagues explore the parameters that could promote the elimination of active Ras cells when surrounded by WT cells. The elimination of active Ras cells by surrounding WT cells was previously described extensively and associated with a process named cell competition, a context dependant elimination of cells. Several mechanisms have been associated with competition, including more recently elimination processes based on mechanical stress. This was explored theoretically and experimentally and was either associated with differential growth and sensitivity to pressure and/or differences in homeostatic density/pressure. This was extensively validated for the case of Scribble mutant cells which are eliminated by WT MDCK cells due to their higher homeostatic density. However, there has been so far very little systematic characterisation of the mechanical parameters and properties of these different cell types and how this could contribute to mechanical competition.

Here, the authors used the context of active Ras cells in MDCK cells (with some observations in vivo in mice gut which are a bit more anecdotal) to explore the parameters causal to Ras cell elimination. Using for the first time traction force microscopy, stress microscopy combined with Bayesian inference, they first show that clusters of active Ras cells experience higher pressure compared to WT. Interestingly, this occurs in absence of differences in growth rate, and while Ras cells seems to have lower homeostatic density, in contractions with the previous models associated with mechanical cell competition. Using a self-propelled Voronoi model, they explored more systematically the conditions that will promote the compression of transformed cells, showing globally that higher Area compressibility and/or lower junctional tension are associated with higher compressibility. Using then an original and novel experimental method to measure bulk compressibility of cell populations, they confirmed that active Ras cells are globally twice more compressible than WT cells. This compressibility correlates with a disruption of adherens junctions. Accordingly, the higher pressure near transformed Ras cells can be completely rescued by increasing cell-cell adhesion through E-cad overexpression, which also reduces the compressibility of the transformed cells. Altogether, these results go along the lines of a previous theoretical work (Gradeci et al. eLife 2021) which was suggesting that reduced stiffness/higher compressibility was essential to promote loser cell elimination. Here, the authors provide for the first time a very convincing experimental measurement and validation of this prediction. Moreover, their modelling approach goes far beyond what was performed before in terms of exploration of conditions promoting compressibility, and their experimental data point at alternative mechanisms that may contribute to mechanical competition.

Strengths:

- Original methodologies to perform systematic characterisation of mechanical properties of Ras cells during cell competition, which include a novel method to measure bulk compressibility.<br /> - A very extensive theoretical exploration of the parameters promoting cell compaction in the context of competition.

Weaknesses:

- Most of the theoretical focus is centred on the bulk compressibility, but so far does not really explain the final fate of the transformed cells. Classic cell competition scenario (including the one involving active Ras cells) lead to the elimination of one cell population either by cell extrusion/cell death or global delamination. This aspect is absolutely not explored in this article, experimentally or theoretically, and as such it is difficult to connect all the observables with the final outcome of cell competition. For instance, higher compressibility may not lead to loser status if the cells can withstand high density without extruding compared to the WT cells (and could even completely invert the final outcome of the competition). Down the line, and as suggested in most of the previous models/experiments, the relationship between pressure/density and extrusion/death will be the key factor that determine the final outcome of competition. However, there is absolutely no characterisation of cell death/cell extrusion in the article so far.

- While the compressibility measurement are very original and interesting, this bulk measurement could be explained by very different cellular processes, from modulation of cell shape, to cell extrusion and tissue multilayering (which by the way was already observed for active Ras cells, see for instance https://pubmed.ncbi.nlm.nih.gov/34644109/). This could change a lot the interpretation of this measurement and to which extend it can explain the compression observed in mixed culture. This compressibility measurement could be much more informative if coupled with an estimation of the change of cell aspect ratio and the rough evaluation of the contribution of cell shape changes versus alternative mechanisms.

- So far, there is no clear explanation of why transformed Ras cells get more compacted in the context of mixed culture compared to pure Ras culture. Previously, the compaction of mutant Scribble cells could be explained by the higher homeostatic density of WT cells which impose their prefered higher density to Scribble mutant (see Wagstaff et al. 2016 or Gradeci et al 2021), however that is not the case of the Ras cells (which have even slightly higher density at confluency). If I understood properly, the Voronoid model assumes some directional movement of WT cell toward transformed which will actively compact the Ras cells through self-propelled forces (see supplementary methods), but this is never clearly discussed/described in the results section, while potentially being one essential ingredient for observing compaction of transformed cells. In fact, this was already described experimentally in the case of Scribble competition and associated with chemoattractant secretion from the mutant cells promoting directed migration of the WT (https://pubmed.ncbi.nlm.nih.gov/33357449/). It would be essential to show what happens in absence of directional propelled movement in the model and validate experimentally whether there is indeed directional movement of the WT toward the transformed cells. Without this, the current data does not really explain the competition process.

- Some of the data lack a bit of information on statistic, especially for all the stress microscopy and traction forces where we do no really know how representative at the stress patterns (how many experiment, are they average of several movies ? integrated on which temporal window ?)

Reviewer #2 (Public review):

The work by Gupta et al. addresses the role of tissue compressibility as a driver of cell competition. The authors use a planar epithelial monolayer system to study cell competition between wild type and transformed epithelial cells expressing HRasV12. They combine imaging and traction force measurements from which the authors propose that wild type cells generate compressive forces on transformed epithelial cells. The authors further present a novel setup to directly measure the compressibility of adherent epithelial tissues. These measurements suggest a higher compressibility of transformed epithelial cells, which is causally linked to a reduction in cell-cell adhesion in transformed cells. The authors support their conclusions by theoretical modelling using a self-Propelled Voronoi model that supports differences in tissue compressibility can lead to compression of the softer tissue type.

The experimental framework to measure tissue compressibility of adherent epithelial monolayers establishes a novel tool, however additional controls of this measurement appear required. Moreover, the experimental support of this study is mostly based on single representative images and would greatly benefit from additional data and their quantitative analysis to support the authors' conclusions. Specific comments are also listed in the following:

Major points:

It is not evident in Fig2A that traction forces increase along the interface between wild type and transformed populations and stresses in Fig2C also seem to be similar at the interface and surrounding cell layer. Only representative examples are provided and a quantification of sigma_m needs to be provided.

In Figure 1-3 only panel 2G and 2H provide a quantitative analysis, but it is not clear how many regions of interest and clusters of transform cells were quantified.

Several statements appear to be not sufficiently justified and supported by data.<br /> For example the statement on pg 3. line 38 seems to lack supportive data 'This comparison revealed that the thickness of HRasV12-expressing cells was reduced by more than 1.7-fold when they were surrounded by wild type cells. These observations pointed towards a selective, competition-dependent compaction of HRasV12-expressing transformed cells but not control cells, in the intestinal villi of mice.'<br /> Similarly, the statement about a cell area change of 2.7 fold (pg 3 line 47) lacks support by measurements.

What is the rationale for setting 𝐾p = 1 in the model assumptions if clear differences in junctional membranes of transformed versus wild type cells occur, including dynamic ruffling? This assumption does not seem to be in line with biological observations.

The novel approach to measure tissue compressibility is based on pH dependent hydrogels. As the pH responsive hydrogel pillar is placed into a culture medium with different conditions, an important control would be if the insertion of this hydrogel itself would change the pH or conditions of the culture assays and whether this alters tissue compressibility or cell adhesion. The authors could for example insert a hydrogel pillar of a smaller diameter that would not lead to compression or culture cells in a larger ring to assess the influence of the pillar itself.

The authors focus on the study of cell compaction of the transformed cells, but how does this ultimately lead to a competitive benefit of wild type cells? Is a higher rate of extrusion observed and associated with the compaction of transformed cells or is their cell death rate increased? While transformed cells seem to maintain a proliferative advantage it is not clear which consequences of tissue compression ultimately drive cell competition between wild type and transformed cells.

The argumentation that softer tissues would be more easily compressed is plausible. However, which mechanism do the authors suggest is generating the actual compressive stress to drive the compaction of transformed cells? They exclude a proliferative advantage of wild type cells, which other mechanisms will generate the compressive forces by wild type cells?

eLife Assessment

This manuscript presents a valuable study utilizing an in vitro organoid system to recapitulate the developmental process of the olfactory epithelium. The authors provided solid evidence indicating that a combination of niche factors can induce organoid development and give rise to multiple cell types. However, the calcium imaging part of the study could be seen as a limitation.

Reviewer #1 (Public review):

Summary:

Olfaction is fundamental to the survival and reproduction of animals, as they rely on olfactory sensory neurons (OSNs) in the olfactory epithelium (OE) to detect volatile chemical cues in their environment. Most mature OSNs adhere to the 'one neuron one receptor' rule, wherein each neuron selects a single receptor for expression from a large repertoire of olfactory receptor genes. The precise regulation of olfactory receptor expression is critical for accurate odorant recognition. Since the seminal discovery of olfactory receptors by Linda Buck and Richard Axel in 1991, substantial efforts have been made to elucidate the mechanisms underlying OSN differentiation and receptor expression. However, these processes remain incompletely understood. The development of in vitro olfactory epithelium organoids offers a promising platform to address these fundamental questions. The in vivo OE is composed of a complex array of cell types, which has posed a significant challenge for recapitulating its structure and function in vitro. Previous attempts to generate olfactory organoids from adult human or mouse OE cells yielded tissue containing OSNs, but these constructs were structurally distinct from the in vivo OE and lacked the characteristic pseudostratified epithelium.

In this study, Kazuya et al. successfully established olfactory epithelium organoids from E13.5 mouse embryonic OE stem cells, which developed into a pseudostratified structure closely resembling the native OE. They further examined the influence of different cultural conditions on OE differentiation, confirming the pivotal role of niche factors in promoting OSN development. Through immunofluorescence staining and single-cell RNA sequencing, they demonstrated that the organoids encompass a diverse range of cell types analogous to those present in the in vivo OE. Notably, calcium imaging revealed that the organoids were functionally responsive to odorants, and single-cell transcriptomic analysis showed that the majority of mature OSNs conformed to the 'one neuron one receptor' rule. Using these organoids, the authors performed a preliminary investigation into the developmental trajectories of OSNs, developed a tool to predict subpopulations of mature OSNs, and identified novel markers associated with OSN maturation. Collectively, the data provide compelling evidence for the reliability and utility of this olfactory organoid model. Further in-depth analyses may enable readers to better assess and utilize this tool to advance the study of olfactory biology.

Strengths:

The authors developed and established olfactory epithelium organoids, with immunofluorescence imaging confirming the presence of a pseudostratified structure similar to that of the in vivo olfactory epithelium, representing a significant advancement. Single-cell sequencing and calcium imaging further demonstrated the utility of these organoids, as they contain multiple cell types analogous to the in vivo olfactory epithelium. Importantly, they are physiologically functional, capable of responding to odor stimuli.

Weakness:

Although the authors have made significant progress in the technique, there are some gaps in understanding its underlying principles. First, it remains unclear what specific characteristics of E13.5 embryonic olfactory stem cells enable them to generate organoids in vitro that more closely resemble the in vivo olfactory epithelium, compared to adult mouse olfactory stem cells. Second, it is not clearly defined which specific cell type(s) from the embryonic olfactory epithelium give rise to these organoids, and the efficiency of organoid formation from the isolated cells also warrants further clarification.

Reviewer #2 (Public review):

Summary:

Suzuki and colleagues aim to develop an in vitro organoid system to recapitulate the developmental process of the olfactory epithelium. The authors have succeeded in using a combination of niche factors to induce organoid development, which gives rise to multiple cell types including those with characteristics of mature olfactory sensory neurons. By comparing different cultural media in inducing lineage specification in the organoids, the authors show that the niche factors play an important role in the neuronal lineage whereas serum promotes the development of the respiratory epithelium. The authors further utilized single-cell RNASeq and trajectory analysis to demonstrate that the organoids recapitulate the developmental process of the olfactory epithelium and that some of the factory sensory neurons express only one receptor type per cell. Using these analyses, the authors proposed that a specific set of guidance modules are associated with individual receptor types to enable the formation of the factory map.

Strengths:

The strength of the paper is that the authors have demonstrated that olfactory epithelium organoids can develop from dissociated cells from embryonic or tissue. This provides a valuable tool for studying the development of processes of the factory epithelium in vitro. Defining various factors in the media that influence the development trajectories of various cell types also provides valuable information to guide further development of the method. Single-cell RNA-Seq experiments provide information about the developmental processes of the olfactory system.

Weaknesses:

The manuscript is also marked by a number of weaknesses. The premise of the studies is not well argued. The authors set out to use organoid culture to study the developmental process in order to unravel the mechanisms of single receptor choice, and its role in setting up the factory map. However, the paper has mostly focused on characterizing the organization rather than providing insights into the problem. The statement that the organoids can develop from single cells is misleading, because it's mostly likely that organoids develop after the dissociated cells form aggregates before developing into organoids. It is not known whether coarsely separated tissue chunks can develop into organoids with the same characteristics. Re-aggregation of the cells to form organoids is in and of itself is interesting. Unfortunately, the heterogeneity of the cells and how they contribute to the development of overnight is not explored. There is also a missed opportunity to compare single-cell RNASeq data from this study with existing ones. The in vitro system is likely to be different from embryonic development. It is critical to compare and determine how much the organoid is recapitulating the development of the OSNs in vivo. There are a number of comprehensive datasets from the OE in addition to that presented in the Fletcher paper. Finally, the quality of the functional assay (calcium imaging) of factory sensory neurons is poor. Experiments are of high quality are needed to verify the results.

Major points:

(1) Adding FBS in organoid culture medium has been shown to negatively affect the organoid formation and growth. Previous OE organoids culture method did not use FBS. Also, day 10 is an odd choice to compare the two conditions after showing day 20 of NF+ culture shows a better differentiation state. It is not known whether and how the differentiation may be different on day 20. Moreover, comparing Figure 2R to 2S, FBS treatment alone appears to have not only more Foxj1+ cells but also more Tuj1+ cells than NFs/FBS. This is inconsistent with the model. The authors should provide statistics for Tuj1+ cells as well.

(2) As opposed to the statement in the manuscript, Plxnb2 had been shown to be expressed by the OSNs (Mclntyre et al. 2010; JNR), specifically in immature OSNs. It would be important to mention that Plxnb2 is expressed in OMP+ OSNs in the OE organoid system and its potential reasons to better guide the readers of the system mimicking the in vivo OSNs. Similarly, OSN expression of Cdh2 has been shown by Akins and colleagues. As Plxnb2 showed an expression pattern (immunofluorescence) with an anterior-posterior axis while Cdh2 expression level was not, it would be informative to show the odorant receptor types regarding the expression pattern of Plxnb2 (versus that of Cdh2) using single cell RNAseq data4.

(3) There is no real layering of the organoids, although some cells show biases toward one side or the other in some regions of the organoid. The authors should not make a sweeping claim that the organoids establish layered structures.

(4) Figure 2P, it is clear whether OMP is present in the cell bodies. The signal is not very convincing. Even the DAPI signal does not seem to be on a comparable scale compared to Figures 2N and 2O.

(5) Annotation of the cell types in different single-cell RNA-Seq analysis. The iOSN is only marked in Figure 3A. In the marker expression panel, it appears that those marked as mOSN have high GAP43, which are an iOSN marker. These discrepancies are not detailed nor discussed.

(6) The authors should merge the single-cell datasets from day 10 organoids cultured in NF-medium and FBS-medium to compare their differences.

(7) The quality of the calcium imaging experiment is poor. Labeling and experimental details are not provided. The concentration of IVA, the manner of its delivery, and delivery duration are not provided. How many ROIs have been imaged, and what percentage of them responded to IVA? Do they respond to more than one odor? Do they respond to repeated delivery? There is no control for solution osmolarity. Cell body response was not recorded. Given that only a small number of cells express a receptor, it seems extraordinary that these axons respond to IVA receptors. The authors should also determine whether IVA receptor genes are found in their dataset.

Reviewer #3 (Public review):

Summary:

The present work by Suzuki et al seeks to develop a new embryonic olfactory epithelium organoid culture model, to study OR gene expression and mechanisms involved in epithelium-to-bulb targeting. They characterize an organoid culture derived from E13 mouse olfactory tissue, using RT-qPCR, immunostaining, limited calcium imaging, and single-cell RNA-seq. Main findings show that the cultures produce major olfactory cell types; many olfactory neurons express a single OR; scSeq analysis identifies transcriptional programs associated with specific OR class expressions that may help define mechanisms involved in projection to specific bulb sites (glomeruli).

Strengths:

The organoid model is generally well-characterized and may be a useful approach for studying this question and other problems, such as basal cell lineage choice or damage and repair mechanisms. Overall, the paper is well-written, and the figures are of high quality.

The cultures, produced from E13 mice, appear to produce HBCs, GBCs, neurons, and non-neural cells, providing an important tool. I think a really interesting question is: when do HBCs first appear in these cultures? Developmentally, in rodents, HBCs do not arise until near the end of gestation, and the OE cell populations are instead made from a more GBC-like cell (keratin negative, p63 negative) that proliferates as an apical or basal progenitor. The cell type and architectural descriptions used here repeatedly are really descriptions of the adult OE, yet the cultures are made from E13 mouse olfactory epithelium. Perhaps an important question could be addressed by this model - how this specific adult reserve epithelial stem cell (the HBC) is generated remains unclear. HBCs are a reserve multipotential cell that reconstitutes the entire olfactory epithelium in adults following severe injury, yet is not present during embryonic development until after the epithelium has been largely generated.

Weaknesses:

The paper should discuss the transcriptional programs identified here that correlate with OR class expression in the context of findings from Tsukahara et al, Cell 2021. Tsukahara identified from in vivo olfactory neuron scSeq fixed gene expression programs defining olfactory neuron position in AP or DV axes correlating highly with OR expression.

While the current findings do define the expression of putative targeting, guidance or adhesion molecules in specific OR-expressing neurons in culture, the current results do not provide any experimental evidence that glomerulus targeting is actually mediated by these factors. Further discussion of this limitation may be helpful, along with a discussion of additional approaches to explore these questions.

Calcium imaging: it is not clear why isovaleric acid was chosen as a stimulus for Ca imaging. Is it's known receptor expressed widely in these cultures? Why not use a cocktail of odorants, to activate a broader range of ORs, as has been widely used in in vitro calcium imaging studies of olfactory neurons? Can you show positive control activation (i.e. high potassium)?

How many unique ORs are identified as expressed in the cultures? Figure 5 indicates only 78 genes. Since mice express about 1200 ORs, is this a limitation? How many replicates (individual cells) are found to express each of the ORs? Again, Figure 5 suggests only 202 cells are OR+? Is this enough to define the gene expression programs reliably associated with a given OR or OR class? More detail on this analysis would be helpful.

eLife Assessment

This manuscript reports on an FLIM-based calcium biosensor, G-CaFLITS. It represents an important contribution to the field of genetically-encoded fluorescent biosensors, and will serve as a practical tool for the FLIM imaging community. The paper provides convincing evidence of G-CaFLITS's photophysical properties and its advantages over previous biosensors such as Tq-Ca-FLITS. Although the benefits of G-Ca-FLITS over Tq-Ca-FLITS are limited by the relatively small wavelength shift, it presents some advantages in terms of compatibility with available instrumentation and brightness consistency.

Reviewer #1 (Public review):

Summary:

van der Linden et al. report on the development of a new green-fluorescent sensor for calcium, following a novel rational design strategy based on the modification of the cyan-emissive sensor mTq2-CaFLITS. Through a mutational strategy similar to the one used to convert EGFP into EYFP, coupled with optimization of strategic amino acids located in proximity of the chromophore, they identify a novel sensor, G-CaFLITS. Through a careful characterization of the photophysical properties in vitro and the expression level in cell cultures, the authors demonstrate that G-CaFLITS combines a large lifetime response with a good brightness in both the bound and unbound states. This relative independence of the brightness on calcium binding, compared with existing sensors that often feature at least one very dim form, is an interesting feature of this new type of sensors, which allows for a more robust usage in fluorescence lifetime imaging. Furthermore, the authors evaluate the performance of G-CaFLITS in different subcellular compartments and under two-photon excitation in Drosophila. While the data appears robust and the characterization thorough, the interpretation of the results in some cases appears less solid, and alternative explanations cannot be excluded.

Strengths:

- The approach is innovative and extends the excellent photophysical properties of the mTq2-based to more red-shifted variants. While the spectral shift might appear relatively minor, as the authors correctly point out, it has interesting practical implications, such as the possibility to perform FLIM imaging of calcium using widely available laser wavelengths, or to reduce background autofluorescence, which can be a significant problem in FLIM.<br /> - The screening was simple and rationally guided, demonstrating that, at least for this class of sensors, a careful choice of screening positions is an excellent strategy to obtain variants with large FLIM responses without the need of high-throughput screening.<br /> - The description of the methodologies is very complete and accurate, greatly facilitating the reproduction of the results by others, or the adoption of similar methods. This is particularly true for the description of the experimental conditions for optimal screening of sensor variants in lysed bacterial cultures.<br /> - The photophysical characterization is very thorough and complete, and the vast amount of data reported in the supporting information is a valuable reference for other researchers willing to attempt a similar sensor development strategy. Particularly well done is the characterization of the brightness in cells, and the comparison on multiple parameters with existing sensors.<br /> - Overall, G-CaFLITS displays excellent properties for a FLIM sensor: very large lifetime change, bright emission in both forms and independence from pH in the physiological range.

Weaknesses:

- The paper demonstrates the application of G-CaFLITS in various cellular sub-compartments without providing direct evidence that the sensor's response is not affected by the targeting. Showing at least that the lifetime values in the saturated state are similar in all compartments would improve the robustness of the claims.<br /> - In some cases, the interpretation of the results is not fully convincing, leaving alternative hypotheses as a possibility. This is particularly the case for the claim of the origin of the strongly reduced brightness of G-CaFLITS in Drosophila. The explanation of the intensity changes of G-CaFLITS also shows some inconsistency with the basic photophysical characterization.<br /> - While the claims generally appear robust, in some cases they are conveyed with a lack of precision. Several sentences in the introduction and discussion could be improved in this regard. Furthermore, the use of the signal-to-noise ratio as a means of comparison between sensors appears to be imprecise, since it is dependent on experimental conditions.

Reviewer #2 (Public review):

Summary:

Van der Linden et al. describe the addition of the T203Y mutation to their previously described fluorescence lifetime calcium sensor Tq-Ca-FLITS to shift the fluorescence to green emission. This mutation was previously described to similarly red-shift the emission of green and cyan FPs. Tq-Ca-FLITS_T203Y behaves as a green calcium sensor with opposite polarity compared with the original (lifetime goes down upon calcium binding instead of up). They then screen a library of variants at two linker positions and identify a variant with slightly improved lifetime contrast (Tq-Ca-FLITS_T203Y_V27A_N271D, named G-Ca-FLITS). The authors then characterize the performance of G-Ca-FLITS relative to Tq-Ca-FLITS in purified protein samples, in cultured cells, and in the brains of fruit flies.

Strengths:

This work is interesting as it extends their prior work generating a calcium indicator scaffold for fluorescent protein-based lifetime sensors with large contrast at a single wavelength, which is already being adopted by the community for production of other FLIM biosensors. This work effectively extends that from cyan to green fluorescence. While the cyan and green sensors are not spectrally distinct enough (~20-30nm shift) to easily multiplex together, it at least shifts the spectra to wavelengths that are more commonly available on commercial microscopes.

The observations of organellar calcium concentrations were interesting and could potentially lead to new biological insight if followed up.

Weaknesses:

The new G-Ca-FLITS sensor doesn't appear to be significantly improved in performance over the original Tq-Ca-FLITS, no specific benefits are demonstrated.

Although it was admirable to attempt in vivo demonstration in Drosophila with these sensors, depolarizing the whole brain with high potassium is not a terribly interesting or physiological stimulus and doesn't really highlight any advantages of their sensors; G-Ca-FLITS appears to be quite dim in the flies.

Reviewer #3 (Public review):

Summary:

The authours present a variant of a previously described fluorescence lifetime sensor for calcium. Much of the manuscript describes the process of developing appropriate assays for screening sensor variants, and thorough characterization of those variants (inherent fluorescence characteristics, response to calcium and pH, comparisons to other calcium sensors). The final two figures show how the sensor performs in cultured cells and in vivo drosophila brains.

Strengths:

The work is presented clearly and the conclusion (this is a new calcium sensor that could be useful in some circumstances) is supported by the data.

Weaknesses:

There are probably few circumstances where this sensor would facilitate experiments (calcium measurements) that other sensors would prove insufficient.

eLife Assessment

This paper presents useful findings that misfolded proteins in the nucleus can impair proteasomal degradation and activate p53. The results supporting the findings are largely solid, but incomplete. The manuscript could be strengthened by including more quantitative data analyses and additional experimentation/discussions on the mechanism of p53 activation by misfolded nuclear proteins. The work will be interesting primarily to scientists studying protein homeostasis.

Joint Public Review:

Summary of the work:

This manuscript defines the differential stress response signaling induced by nuclear and cytoplasmic protein misfolding. To accomplish this, the authors used superfolder GFP fused to a destabilized FKBP protein-bearing targeting signal for cytosolic or nuclear localization. When cells were grown in the presence of the ligand Shield-1, this protein was stable, allowing fluorescence of the GFP protein. Upon removal of Shield-1, the FKBP protein is unfolded targeting the entire fusion protein to proteasomal degradation. Using this approach, they performed RNAseq to probe similarities and differences in transcriptional responses to the accumulation of unfolded proteins in the cytosol or nucleus. As expected, many of the pathways upregulated in both datasets involved protein homeostasis pathways such as the proteasome and cytosolic chaperones. The increase in proteasome subunits correlated with the stabilization of Nrf1 under these conditions, suggesting that protein misfolding might induce proteasome subunits through an Nrf1-dependent mechanism, but this was not explicitly tested. In contrast, the authors report that the p53-dependent transcriptional response was selectively induced by protein misfolding stress in the nucleus, but not the cytosol. Deletion of p53 blocked this increase, indicating that this response is attributable to p53 stabilization. The increased p53 transcriptional activity corresponded with the stabilization of p53 and its target p21 in cells subjected to nuclear but not cytosolic protein misfolding stress. Using a reporter of nuclear proteasome activity, they show that nuclear proteasome activity is reduced in cells following protein misfolding stress in the nucleus, indicating that the stabilization of p53 (and other transcription factors such as NRF1) might be attributed to reduced proteasomal degradation. Additionally, the authors showed that nuclear misfolding stress also induces cell cycle arrest. However, this effect was not dependent on p53 deletion, indicating that this is mediated by other unknown mechanisms.

Major strengths and weaknesses of the methods and results:

The findings reported here define specific transcriptional outputs induced by targeted protein misfolding stress in the nucleus and cytosol, revealing new insights into the organelle-specific stress signaling. The approach is interesting and effective at revealing cellular responses induced by compartment-specific protein misfolding stress.

One major weakness of the study is the lack of mechanistic follow-up for the transcriptional study. For example, what is the mechanistic basis for p53 stabilization by nuclear-destabilized domain (Nuc DD)? Is this entirely caused by diminished nuclear degradation activity as shown in Figure 6 or are there additional factors to be considered? If limited proteasome degradation capacity is the main reason for p53 upregulation, wouldn't the authors also see stabilization of other short-lived transcription factors? The fact that Nrf1 and Nrf2 are also stabilized by Nuc DD is consistent with the authors' hypothesis. On the other hand, if Nuc DD also affects other short-lived transcription factors such as c-fos or c-myc via proteasome inhibition, why did the gene expression analysis only pick up the p53 pathway as the one differentially regulated by Nuc DD? Would this imply that only p53 is specifically targeted by the nuclear proteasome, whereas other short-lived transcription factors are degraded either by the cytosolic proteasome or by both nuclear and cytosolic proteasome like Nrf1? Is there any evidence in the literature that supports this speculation? Additionally, how does Nuc DD affect the UPS system in the nucleus? Does it clog the proteasome directly or affect other assisting factors like chaperones or ubiquitinating enzymes? Lastly, it isn't clear what the functional implications of p53 stabilization would be for cells subjected to nuclear protein misfolding stress, particularly as the small effect on cell cycle arrest is not dependent on p53. In the end, the lack of mechanistic and/or functional follow-up reduces the overall importance of this manuscript. While the reviewers do not expect the authors to answer all these questions by experiments, additional work/clarifications/discussions along these lines would significantly improve the paper (see the recommendations).

Another major weakness is the lack of statistical analysis (SA) to better support their conclusions. In fact, no SA was provided for many figures even though the authors tried to make many comparisons.

The failure of the DD reporter to mount a significant heat shock response was puzzling. The presence of non-native proteins is the primary trigger for the heat shock response, but the authors acknowledge that inducible chaperones such as Hspa1a/b and Hsp90aa1 were not significantly changed in their system (page 8). Could this suggest a problem with the approach? What exactly is the nature of the stress mounted by Nuc DD?

The cell cycle data presented in Figure 5 is less robust, particularly as the p53 data in panels C and D was collected only once.

The Western blot data shown in Figure 6 does not have quantification to show how representative the blot is and how robust the changes in protein levels are over time. Western blots are known to be variable with different replicates and therefore the authors need to mention the number of biological repeats represented by the blot.

eLife Assessment

This is a valuable polymer model that provides insight into the origin of macromolecular mixed and demixed states within transcription clusters. The well-performed and clearly presented simulations will be of interest to those studying gene expression in the context of chromatin. While the study is generally solid, it could benefit from a more direct comparison with existing experimental data sets as well as further discussion of the limits of the underlying model assumptions.

Reviewer #1 (Public review):

This manuscript discusses from a theory point of view he mechanisms underlying the formation of specialized or mixed factories. To investigate this, a chromatin polymer model was developed to mimic the chromatin binding-unbinding dynamics of various complexes of transcription factors (TFs).

The model revealed that both specialized (i.e., demixed) and mixed clusters can emerge spontaneously, with the type of cluster formed primarily determined by cluster size. Non-specific interactions between chromatin and proteins were identified as the main factor promoting mixing, with these interactions becoming increasingly significant as clusters grow larger.

These findings, observed in both simple polymer models and more realistic representations of human chromosomes, reconcile previously conflicting experimental results. Additionally, the introduction of different types of TFs was shown to strongly influence the emergence of transcriptional networks, offering a framework to study transcriptional changes resulting from gene editing or naturally occurring mutations.

Overall I think this is an interesting paper discussing a valuable model of how chromosome 3D organisation is linked to transcription. I would only advise the authors to polish and shorten their text to better highlight their key findings and make it more accessible to the reader.

Reviewer #2 (Public review):

Summary:

With this report, I suggest what are in my opinion crucial additions to the otherwise very interesting and credible research manuscript "Cluster size determines morphology of transcription factories in human cells".

Strengths:

The manuscript in itself is technically sound, the chosen simulation methods are completely appropriate the figures are well-prepared, the text is mostly well-written spare a few typos. The conclusions are valid and would represent a valuable conceptual contribution to the field of clustering, 3D genome organization and gene regulation related to transcription factories, which continues to be an area of most active investigation.

Weaknesses:

However, I find that the connection to concrete biological data is weak. This holds especially given that the data that are needed to critically assess the applicability of the derived cross-over with factory size is, in fact, available for analysis, and the suggested experiments in the Discussion section are actually done and their results can be exploited. In my judgement, unless these additional analysis are added to a level that crucial predictions on TF demixing and transcriptional bursting upon TU clustering can be tested, the paper is more fitted for a theoretical biophysics venue than for a biology journal.

Major points

(1) My first point concerns terminology. The Merriam-Webster dictionary describes morphology as the study of structure and form. In my understanding, none of the analyses carried out in this study actually address the form or spatial structuring of transcription factories. I see no aspects of shape, only size. Unless the authors want to assess actual shapes of clusters, I would recommend to instead talk about only their size/extent. The title is, by the same argument, in my opinion misleading as to the content of this study.

(2) Another major conceptual point is the choice of how a single TF:pol particle in the model relates to actual macromolecules that undergo clustering in the cell. What about the fact that even single TF factories still contain numerous canonical transcription factors, many of which are also known to undergo phase separation? Mediator, CDK9, Pol II just to name a few. This alone already represents phase separation under the involvement of different species, which must undergo mixing. This is conceptually blurred with the concept of gene-specific transcription factors that are recruited into clusters/condensates due to sequence-specific or chromatin-epigenetic-specific affinities. Also, the fact that even in a canonical gene with a "small" transcription factory there are numerous clustering factors takes even the smallest factories into a regime of several tens of clustering macromolecules. It is unclear to me how this reality of clustering and factory formation in the biological cell relates to the cross-over that occurs at approximately n=10 particles in the simulations presented in this paper.

(3) The paper falls critically short in referencing and exploiting for analysis existing literature and published data both on 3D genome organization as well as the process of cluster formation in relation to genomic elements. In terms of relevant literature, most of the relevant body of work from the following areas has not been included:

(i) mechanisms of how the clustering of Pol II, canonical TFs, and specific TFs is aided by sequence elements and specific chromatin states

(ii) mechanisms of TF selectivity for specific condensates and target genomic elements

(iii) most crucially, existing highly relevant datasets that connect 3D multi-point contacts with transcription factor identity and transcriptional activity, which would allow the authors to directly test their hypotheses by analysis of existing data

Here, especially the data under point iii are essential. The SPRITE method (cited but not further exploited by the authors), even in its initial form of publication, would have offered a data set to critically test the mixing vs. demixing hypothesis put forward by the authors. Specifically, the SPRITE method offers ordered data on k-mers of associated genomic elements. These can be mapped against the main TFs that associate with these genomic elements, thereby giving an account of the mixed / demixed state of these k-mer associations. Even a simple analysis sorting these associations by the number of associated genomic elements might reveal a demixing transition with increasing association size k. However, a newer version of the SPRITE method already exists, which combines the k-mer association of genomic elements with the whole transcriptome assessment of RNAs associated with a particular DNA k-mer association. This can even directly test the hypotheses the authors put forward regarding cluster size, transcriptional activation, correlation between different transcription units' activation etc.

To continue, the Genome Architecture Mapping (GAM) method from Ana Pombo's group has also yielded data sets that connect the long-range contacts between gene-regulatory elements to the TF motifs involved in these motifs, and even provides ready-made analyses that assess how mixed or demixed the TF composition at different interaction hubs is. I do not see why this work and data set is not even acknowledged? I also strongly suggest to analyze, or if they are already sufficiently analyzed, discuss these data in the light of 3D interaction hub size (number of interacting elements) and TF motif composition of the involved genomic elements.

Further, a preprint from the Alistair Boettiger and Kevin Wang labs from May 2024 also provides direct, single-cell imaging data of all super-enhancers, combined with transcription detection, assessing even directly the role of number of super-enhancers in spatial proximity as a determinant of transcriptional state. This data set and findings should be discussed, not in vague terms but in detailed terms of what parts of the authors' predictions match or do not match these data.

For these data sets, an analysis in terms of the authors' key predictions must be carried out (unless the underlying papers already provide such final analysis results). In answering this comment, what matters to me is not that the authors follow my suggestions to the letter. Rather, I would want to see that the wealth of available biological data and knowledge that connects to their predictions is used to their full potential in terms of rejecting, confirming, refining, or putting into real biological context the model predictions made in this study.

References for point (iii):

RNA promotes the formation of spatial compartments in the nucleus<br /> https://www.cell.com/cell/fulltext/S0092-8674(21)01230-7?dgcid=raven_jbs_etoc_email

Complex multi-enhancer contacts captured by genome architecture mapping<br /> https://www.nature.com/articles/nature21411

Cell-type specialization is encoded by specific chromatin topologies<br /> https://www.nature.com/articles/s41586-021-04081-2

Super-enhancer interactomes from single cells link clustering and transcription<br /> https://www.biorxiv.org/content/10.1101/2024.05.08.593251v1.full

For point (i) and point (ii), the authors should go through the relevant literature on Pol II and TF clustering, how this connects to genomic features that support the cluster formation, and also the recent literature on TF specificity. On the last point, TF specificity, especially the groups of Ben Sabari and Mustafa Mir have presented astonishing results, that seem highly relevant to the Discussion of this manuscript.

(4) Another conceptual point that is a critical omission is the clarification that there are, in fact, known large vs. small transcription factories, or transcriptional clusters, which are specific to stem cells and "stressed cells". This distinction was initially established by Ibrahim Cisse's lab (Science 2018) in mouse Embryonic Stem Cells, and also is seen in two other cases in differentiated cells in response to serum stimulus and in early embryonic development:

Mediator and RNA polymerase II clusters associate in transcription-dependent condensates<br /> https://www.science.org/doi/10.1126/science.aar4199

Nuclear actin regulates inducible transcription by enhancing RNA polymerase II clustering<br /> https://www.science.org/doi/10.1126/sciadv.aay6515

RNA polymerase II clusters form in line with surface condensation on regulatory chromatin<br /> https://www.embopress.org/doi/full/10.15252/msb.202110272

If "morphology" should indeed be discussed, the last paper is a good starting point, especially in combination with this additional paper:

Chromatin expansion microscopy reveals nanoscale organization of transcription and chromatin<br /> https://www.science.org/doi/10.1126/science.ade5308

(5) The statement "scripts are available upon request" is insufficient by current FAIR standards and seems to be non-compliant with eLife requirements. At a minimum, all, and I mean all, scripts that are needed to produce the simulation outcomes and figures in the paper, must be deposited as a publicly accessible Supplement with the article. Better would be if they would be structured and sufficiently documented and then deposited in external repositories that are appropriate for the sharing of such program code and models.

Reviewer #3 (Public review):

Summary:<br /> In this work, the authors present a chromatin polymer model with some specific pattern of transcription units (TUs) and diffusing TFs; they simulate the model and study TFclustering, mixing, gene expression activity, and their correlations. First, the authors designed a toy polymer with colored beads of a random type, placed periodically (every 30 beads, or 90kb). These colored beads are considered a transcription unit (TU). Same-colored TUs attract with each other mediated by similarly colored diffusing beads considered as TFs. This led to clustering (condensation of beads) and correlated (or anti-correlation) "gene expression" patterns. Beyond the toy model, when authors introduce TUs in a specific pattern, it leads to emergence of specialized and mixed cluster of different TFs. Human chromatin models with realistic distribution of TUs also lead to the mixing of TFs when cluster size is large.

Strengths:<br /> This is a valuable polymer model for chromatin with a specific pattern of TUs and diffusing TF-like beads. Simulation of the model tests many interesting ideas. The simulation study is convincing and the results provide solid evidence showing the emergence of mixed and demixed TF clusters within the assumptions of the model.

Weaknesses:<br /> Weakness of the work: The model has many assumptions. Some of the assumptions are a bit too simplistic. Concerns about the work are detailed below:

The authors assume that when the diffusing beads (TFs) are near a TU, the gene expression starts. However, mammalian gene expression requires activation by enhancer-promoter looping and other related events. It is not a simple diffusion-limited event. Since many of the conclusions are derived from expression activity, will the results be affected by the lack of looping details?

Authors neglect protein-protein interactions. Without protein-protein interactions, condensate formation in natural systems is unlikely to happen.

What is described in this paper is a generic phenomenon; many kinds of multivalent chromatin-binding proteins can form condensates/clusters as described here. For example, if we replace different color TUs with different histone modifications and different TFs with Hp1, PRC1/2, etc, the results would remain the same, wouldn't they? What is specific about transcription factor or transcription here in this model?<br /> What is the logic of considering 3kb chromatin as having a size of 30 nm? See Kadam et al. (Nature Communications 2023). Also, DNA paint experimental measurement of 5kb chromatin is greater than 100 nm (see work by Boettiger et al.).

eLife Assessment

The role of ACVR2A is potentially of importance to both the biology of trophoblast cells and to the pathogenesis of preeclampsia. In this manuscript, the authors have taken a useful first step towards better understanding this protein using a loss of function model in trophoblast cell lines and then examining invasion, proliferation, and transcription in these cells. At present, the results of this study are only based on the observation of in vitro phenotypes, and the strength of the invasion data is somewhat weak, given the confounding effect on proliferation. The study is currently incomplete as there is a lack of direct evidence on how target factors participate in the occurrence of placental structural disorders and diseases through potential downstream pathways.

Reviewer #1 (Public review):

Summary:

This study has preliminarily revealed the role of ACVR2A in trophoblast cell function, including its effects on migration, invasion, proliferation, and clonal formation, as well as its downstream signaling pathways.

Strengths:

The use of multiple experimental techniques, such as CRISPR/Cas9-mediated gene knockout, RNA-seq, and functional assays (e.g., Transwell, colony formation, and scratch assays), is commendable and demonstrates the authors' effort to elucidate the molecular mechanisms underlying ACVR2A's regulation of trophoblast function. The RNA-seq analysis and subsequent GSEA findings offer valuable insights into the pathways affected by ACVR2A knockout, particularly the Wnt and TCF7/c-JUN signaling pathways.

Weaknesses:

The molecular mechanisms underlying this study require further exploration through additional experiments. While the current findings provide valuable insights into the role of ACVR2A in trophoblast cell function and its involvement in the regulation of migration, invasion, and proliferation, further validation in both in vitro and in vivo models is needed. Additionally, more experiments are required to establish the functional relevance of the TCF7/c-JUN pathway and its clinical significance, particularly in relation to pre-eclampsia. Additional techniques, such as animal models and more advanced clinical sample analyses, would help strengthen the conclusions and provide a more comprehensive understanding of the molecular pathways involved.

Reviewer #2 (Public review):

Summary:

ACVR2A is one of a handful of genes for which significant correlations between associated SNPs and the incidences of preeclampsia have been found in multiple populations. It is one of the TGFB family receptors, and multiple ligands of ACVR2A, as well as its coreceptors and related inhibitors, have been implicated in placental development, trophoblast invasion, and embryo implantation. This useful study builds on this knowledge by showing that ACVR2A knockout in trophoblast-related cell lines reduces trophoblast invasion, which could tie together many of these observations. Support for this finding is incomplete, as reduced proliferation may be influencing the invasion results. The implication of cross-talk between the WNT and ACRV2A/SMAD2 pathways is an important contribution to the understanding of the regulation of trophoblast function.

Strengths:

(1) ACVR2A is one of very few genes implicated in preeclampsia in multiple human populations, yet its role in pathogenesis is not very well studied and this study begins to address that hole in our knowledge.

(2) ACVR2A is also indirectly implicated in trophoblast invasion and trophoblast development via its connections to many ligands, inhibitors, and coreceptors, suggesting its potential importance.

(3) The authors have used multiple cell lines to verify their most important observations.

Weaknesses:

(1) There are a number of claims made in the introduction without attribution. For example, there are no citations for the claims that family history is a significant risk factor for PE, that inadequate trophoblast invasion of spiral arteries is a key factor, and that immune responses, and renin-angiotensin activity are involved.

(2) The introduction states "As a receptor for activin A, ACVR2A..." It's important to acknowledge that ACVR2A is also the receptor for other TGFB family members, with varying affinities and coreceptors. Several TGFB family members are known to regulate trophoblast differentiation and invasion. For example, BMP2 likely stimulates trophoblast invasion at least in part via ACVR2A (PMID 29846546).

(3) An alternative hypothesis for the potential role of ACVR2A in preeclampsia is its functions in the endometrium. In the mouse ACVR2A knockout in the uterus (and other progesterone receptor-expressing cells) leads to embryo implantation failure.

(4) In the description of the patient population for placental sample collections, preeclampsia is defined only by hypertension, and this is described as being in accordance with ACOG guidelines. ACOG requires a finding of hypertension in combination with either proteinuria or one of the following: thrombocytopenia, elevated creatinine, elevated liver enzymes, pulmonary, edema, and new onset unresponsive headache.

(5) I believe that Figures 1a and 1b are data from a previously published RNAseq dataset, though it is not entirely clear in the text. The methods section does not include a description of the analysis of these data undertaken here. It would be helpful to include at least a brief description of the study these data are taken from - how many samples, how were the PE/control groups defined, gestational age range, where is it from, etc. For the heatmap presented in B, what is the significance of the other genes/ why are they being shown? If the purpose of these two panels is to show differential expression specifically of ACVR2A in this dataset, that could be shown more directly.

(6) More information is needed in the methods section to understand how the immunohistochemistry was quantified. "Quantitation was performed" is all that is provided. Was staining quantified across the whole image or only in anchoring villous areas? How were HRP & hematoxylin signals distinguished in ImageJ? How was the overall level of HRP/DAB development kept constant between the NC and PE groups?

(7) In Figure 1E it is not immediately obvious to many readers where the EVT are. It is probably worth circling or putting an arrow to the little region of ACVR2A+ EVT that is shown in the higher magnification image in Figure 1E. These are actually easier to see in the pictures provided in the supplement Figure 1. Of note, the STB is also staining positive. This is worth pointing out in the results text.

(8) It is not possible to judge whether the IF images in 1F actually depict anchoring villi. The DAPI is really faint, and it's high magnification, so there isn't a lot of context. Would it be possible to include a lower magnification image that shows where these cells are located within a placental section? It is also somewhat surprising that this receptor is expressed in the cytoplasm rather than at the cell surface. How do the authors explain this?

(9) The results text makes it sound like the data in Figure 2A are from NCBI & Protein atlas, but the legend says it is qPCR from this lab. The methods do not detail how these various cell lines were grown; only HTR-SVNeo cell culture is described. Similarly, JAR cells are used for several experiments and their culture is not described.

(10) Under RT-qPCR methods, the phrase "cDNA reverse transcription cell RNA was isolated..." does not make any sense.

(11) The paragraph beginning "Consequently, a potential association..." is quite confusing. It mentions analyzing ACVR2A expression in placentas, but then doesn't point to any results of this kind and repeats describing the results in Figure 2a, from various cell lines.

(12) The authors should acknowledge that the effect of the ACVR2A knockout on proliferation makes it difficult to draw any conclusions from the trophoblast invasion assays. That is, there might be fewer migrating or invading cells in the knockout lines because there are fewer cells, not because the cells that are there are less invasive. Since this is a central conclusion of the study, it is a major drawback.

(13) The legend and the methods section do not agree on how many fields were selected for counting in the transwell invasion assays in Figure 3C. The methods section and the graph do not match the number of replicate experiments in Figure 3D (the number of replicate experiments isn't described for 3C).

(14) Discussion says "Transcriptome sequencing analysis revealed low ACVR2A expression in placental samples from PE patients, consistent with GWAS results across diverse populations." The authors should explain this briefly. Why would SNPs in ACVR2A necessarily affect levels of the transcript?

(15) "The expression levels of ACVR2A mRNA were comparable to those of tumor cells such as A549. This discovery suggested a potential pivotal role of ACVR2A in the biological functions of trophoblast cells, especially in the nurturing layer." Alternatively, ACVR2A expression resembles that of tumors because the cell lines used here are tumor cells (JAR) or immortalized cells (HTR8). These lines are widely used to study trophoblast properties, but the discussion should at least acknowledge the possibility that the behavior of these cells does not always resemble normal trophoblasts.

(16) The authors should discuss some of what is known about the relationship between the TCF7/c-JUN pathway and the major signaling pathway activated by ACVR2A, Smad 2/3/4. The Wnt and TGFB family cross-talk is quite complex and it has been studied in other systems.

eLife Assessment

This important study introduces a biologically constrained model of telencephalic area of adult zebrafish to highlight the significance of precisely balanced memory networks in olfactory processing. The authors provide compelling evidence that their model performs better in multiple situations (for e.g. in terms of network stability and shaping the geometry of representations), compared to traditional attractor networks and persistent activity. The work supports recent studies reporting functional E/I subnetworks in several sensory cortexes, and will be of interest to both theoretical and experimental neuroscientists studying network dynamics based on structured excitatory and inhibitory interactions.

Reviewer #1 (Public review):

Summary:

Meissner-Bernard et al present a biologically constrained model of telencephalic area of adult zebrafish, a homologous area to the piriform cortex, and argue for the role of precisely balanced memory networks in olfactory processing.

This is interesting as it can add to recent evidence on the presence of functional subnetworks in multiple sensory cortices. It is also important in deviating from traditional accounts of memory systems as attractor networks. Evidence for attractor networks has been found in some systems, like in the head direction circuits in the flies. However, the presence of attractor dynamics in other modalities, like sensory systems, and their role in computation has been more contentious. This work contributes to this active line of research in experimental and computational neuroscience by suggesting that, rather than being represented in attractor networks and persistent activity, olfactory memories might be coded by balanced excitation-inhibitory subnetworks.

Strengths:

The main strength of the work is in: (1) direct link to biological parameters and measurements, (2) good controls and quantification of the results, and (3) comparison across multiple models.

(1) The authors have done a good job of gathering the current experimental information to inform a biological-constrained spiking model of the telencephalic area of adult zebrafish. The results are compared to previous experimental measurements to choose the right regimes of operation.<br /> (2) Multiple quantification metrics and controls are used to support the main conclusions, and to ensure that the key parameters are controlled for - e.g. when comparing across multiple models.<br /> (3) Four specific models (random, scaled I / attractor, and two variant of specific E-I networks - tuned I and tuned E+I) are compared with different metrics, helping to pinpoint which features emerge in which model.

In the revised manuscript, the authors have also:<br /> (a) made a good effort to provide a mechanistic explanation of their results (especially on the mechanism underlying medium amplification in specific E/I network models);<br /> (b) performed a systematic analysis of the parameter space by changing different parameters of E and I neurons (specifically showing that different time constants of E and I neurons do not change the results and therefore the main effects result from connectivity);<br /> (c) added further analysis and discussion on the potential functional and computational significance of balanced specific E-I subnetworks.

These additions substantially strengthen the study, presenting compelling evidence for how networks with specific E-I structure can underpin olfactory processing and memory representations. The findings have potential implications that extend beyond the olfactory system and may be applicable to other neural systems and species.

Reviewer #2 (Public review):

Summary:

The authors conducted a comparative analysis of four networks, varying in the presence of excitatory assemblies and the architecture of inhibitory cell assembly connectivity. They found that co-tuned E-I assemblies provide network stability and a continuous representation of input patterns (on locally constrained manifolds), contrasting with networks with global inhibition that result in attractor networks.

Strengths:

The findings presented in this paper are very interesting and cutting-edge. The manuscript effectively conveys the message and presents a creative way to represent high-dimensional inputs and network responses. Particularly, the result regarding the projection of input patterns onto local manifolds and continuous representation of input/memory is very Intriguing and novel. Both computational and experimental neuroscientists would find value in reading the paper.

Weaknesses:

Intuitively, classification (decodability) in discrete attractor networks is much better than in networks with continuous representations. This could also be shown in Figure 5B, along with the performance of the random and tuned E-I networks. The latter networks have the advantage of providing network stability compared to the Scaled I network, but at the cost of reduced network salience and, therefore, reduced input decodability. Thus, tuned E-I networks cannot always perform better than any other network.

Reviewer #3 (Public review):

Summary:

This work investigates computational consequences of assemblies containing both excitatory and inhibitory neurons (E/I assembly) in a model with parameters constrained by experimental data from the telencephalic area Dp of zebrafish. The authors show how this precise E/I balance shapes the geometry of neuronal dynamics in comparison to unstructured networks and networks with more global inhibitory balance. Specifically, E/I assemblies lead to the activity being locally restricted onto manifolds - a dynamical structure in-between high-dimensional representations in unstructured networks and discrete attractors in networks with global inhibitory balance. Furthermore, E/I assemblies lead to smoother representations of mixtures of stimuli while those stimuli can still be reliably classified, and allows for more robust learning of additional stimuli.

Strengths:

Since experimental studies do suggest that E/I balance is very precise and E/I assemblies exist, it is important to study the consequences of those connectivity structures on network dynamics. The authors convincingly show that E/I assemblies lead to different geometries of stimulus representation compared to unstructured networks and networks with global inhibition. This finding might open the door for future studies for exploring the functional advantage of these locally defined manifolds, and how other network properties allow to shape those manifolds.

The authors also make sure that their spiking model is well-constrained by experimental data from the zebrafish pDp. Both, spontaneous and odor stimulus triggered spiking activity is within the range of experimental measurements. But the model is also general enough to be potentially applied to findings in other animal models and brain regions.

Weaknesses:

All my previous points have been addressed.

Author response:

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

The revised manuscript contains new results and additional text. Major revisions:

(1) Additional simulations and analyses of networks with different biophysical parameters and with identical time constants for E and I neurons (Methods, Supplementary Fig. 5).

(2) Additional simulations and analyses of networks with modifications of connectivity parameters to further analyze effects of E/I assemblies on manifold geometry (Supplementary Fig. 6).

(3) Analysis of synaptic current components (Figure 3 D-F; to analyze mechanism of modest amplification in Tuned networks). 

(4) More detailed explanation of pattern completion analysis (Results).

(5) Analysis of classification performance of Scaled networks (Supplementary Fig.8).

(6) Additional analysis (Figure 5D-F) and discussion (particularly section “Computational functions of networks with E/I assemblies”) of functional benefits of continuous representations in networks with E-I assemblies. 

Public Reviews: 

Reviewer #1 (Public Review): 

Summary: 

Meissner-Bernard et al present a biologically constrained model of telencephalic area of adult zebrafish, a homologous area to the piriform cortex, and argue for the role of precisely balanced memory networks in olfactory processing. 

This is interesting as it can add to recent evidence on the presence of functional subnetworks in multiple sensory cortices. It is also important in deviating from traditional accounts of memory systems as attractor networks. Evidence for attractor networks has been found in some systems, like in the head direction circuits in the flies. However, the presence of attractor dynamics in other modalities, like sensory systems, and their role in computation has been more contentious. This work contributes to this active line of research in experimental and computational neuroscience by suggesting that, rather than being represented in attractor networks and persistent activity, olfactory memories might be coded by balanced excitation-inhibitory subnetworks. 

Strengths: 

The main strength of the work is in: (1) direct link to biological parameters and measurements, (2) good controls and quantification of the results, and (3) comparison across multiple models. 

(1) The authors have done a good job of gathering the current experimental information to inform a biological-constrained spiking model of the telencephalic area of adult zebrafish. The results are compared to previous experimental measurements to choose the right regimes of operation. 

(2) Multiple quantification metrics and controls are used to support the main conclusions and to ensure that the key parameters are controlled for - e.g. when comparing across multiple models.  (3) Four specific models (random, scaled I / attractor, and two variant of specific E-I networks - tuned I and tuned E+I) are compared with different metrics, helping to pinpoint which features emerge in which model. 

Weaknesses: 

Major problems with the work are: (1) mechanistic explanation of the results in specific E-I networks, (2) parameter exploration, and (3) the functional significance of the specific E-I model. 

(1) The main problem with the paper is a lack of mechanistic analysis of the models. The models are treated like biological entities and only tested with different assays and metrics to describe their different features (e.g. different geometry of representation in Fig. 4). Given that all the key parameters of the models are known and can be changed (unlike biological networks), it is expected to provide a more analytical account of why specific networks show the reported results. For instance, what is the key mechanism for medium amplification in specific E/I network models (Fig. 3)? How does the specific geometry of representation/manifolds (in Fig. 4) emerge in terms of excitatory-inhibitory interactions, and what are the main mechanisms/parameters? Mechanistic account and analysis of these results are missing in the current version of the paper. 

We agree that further mechanistic insights would be of interest and addressed this issue at different levels:

(1) Biophysical parameters: to determine whether network behavior depends on specific choices of biophysical parameters in E and I neurons we equalized biophysical parameters across neuron types. The main observations are unchanged, suggesting that the observed effects depend primarily on network connectivity (see also response to comment [2]).

(2) Mechanism of modest amplification in E/I assemblies: analyzing the different components of the synaptic currents demonstrate that the modest amplification of activity in Tuned networks results from an “imperfect” balance of recurrent excitation and inhibition within assemblies (see new Figures 3D-F and text p.7). Hence, E/I co-tuning substantially reduces the net amplification in Tuned networks as compared to Scaled networks, thus preventing discrete attractor dynamics and stabilizing network activity, but a modest amplification still occurs, consistent with biological observations.

(3) Representational geometry: to obtain insights into the network mechanisms underlying effects of E/I assemblies on the geometry of population activity we tested the hypothesis that geometrical changes depend, at least in part, on the modest amplification of activity within E/I assemblies (see Supplementary Figure 6). We changed model parameters to either prevent the modest amplification in Tuned networks (increasing I-to-E connectivity within assemblies) or introduce a modest amplification in subsets of neurons by other mechanisms (concentration-dependent increase in the excitability of pseudo-assembly neurons; Scaled I networks with reduced connectivity within assemblies). Manipulations that introduced a modest, input-dependent amplification in neuronal subsets had geometrical effects similar to those observed in Tuned networks, whereas manipulations that prevented a modest amplification abolished these effects (Supplementary Figure 6). Note however that these manipulations generated different firing rate distributions. These results provide a starting point for more detailed analyses of the relationship between network connectivity and representational geometry (see p.12).

In summary, our additional analyses indicate that effects of E/I assemblies on representational geometry depend primarily on network connectivity, rather than specific biophysical parameters, and that the resulting modest amplification of activity within assemblies makes an important contribution. Further analyses may reveal more specific relationships between E/I assemblies and representational geometry, but such analyses are beyond the scope of this study.

(2) The second major issue with the study is a lack of systematic exploration and analysis of the parameter space. Some parameters are biologically constrained, but not all the parameters. For instance, it is not clear what the justification for the choice of synaptic time scales are (with E synaptic time constants being larger than inhibition: tau_syn_i = 10 ms, tau_syn_E = 30 ms). How would the results change if they are varying these - and other unconstrained - parameters? It is important to show how the main results, especially the manifold localisation, would change by doing a systematic exploration of the key parameters and performing some sensitivity analysis. This would also help to see how robust the results are, which parameters are more important and which parameters are less relevant, and to shed light on the key mechanisms.  

We thank the reviewer for raising this point. We chose a relatively slow time constant for excitatory synapses because experimental data indicate that excitatory synaptic currents in Dp and piriform cortex contain a prominent NMDA component. Nevertheless, to assess whether network behavior depends on specific choices of biophysical parameters in E and I neurons, we have performed additional simulations with equal synaptic time constants and equal biophysical parameters for all neurons. Each neuron also received the same number of inputs from each population (see revised Methods). Results were similar to those observed previously (Supplementary Fig.5 and p.9 of main text). We therefore conclude that the main effects observed in Tuned networks cannot be explained by differences in biophysical parameters between E and I neurons but is primarily a consequence of network connectivity.

(3) It is not clear what the main functional advantage of the specific E-I network model is compared to random networks. In terms of activity, they show that specific E-I networks amplify the input more than random networks (Fig. 3). But when it comes to classification, the effect seems to be very small (Fig. 5c). Description of different geometry of representation and manifold localization in specific networks compared to random networks is good, but it is more of an illustration of different activity patterns than proving a functional benefit for the network. The reader is still left with the question of what major functional benefits (in terms of computational/biological processing) should be expected from these networks, if they are to be a good model for olfactory processing and learning. 

One possibility for instance might be that the tasks used here are too easy to reveal the main benefits of the specific models - and more complex tasks would be needed to assess the functional enhancement (e.g. more noisy conditions or more combination of odours). It would be good to show this more clearly - or at least discuss it in relation to computation and function. 

In the previous manuscript, the analysis of potential computational benefits other than pattern classification was limited and the discussion of this issue was condensed into a single itemized paragraph to avoid excessive speculation. Although a thorough analysis of potential computational benefits exceeds the scope of a single paper, we agree with the reviewer that this issue is of interest and therefore added additional analyses and discussion.

In the initial manuscript we analyzed pattern classification primarily to investigate whether Tuned networks can support this function at all, given that they do not exhibit discrete attractor states. We found this to be the case, which we consider a first important result.

Furthermore, we found that precise balance of E/I assemblies can protect networks against catastrophic firing rate instabilities when assemblies are added sequentially, as in continual learning. Results from these simulations are now described and discussed in more detail (see Results p.11 and Discussion p.13).

In the revised manuscript, we now also examine additional potential benefits of Tuned networks and discuss them in more detail (see new Figure 5D-F and text p.11). One hypothesis is that continuous representations provide a distance metric between a given input and relevant (learned) stimuli. To address this hypothesis, we (1) performed regression analysis and (2) trained support vector machines (SVMs) to predict the concentration of a given odor in a mixture based on population activity. In both cases, Tuned E+I networks outperformed Scaled and _rand n_etworks in predicting the concentration of learned odors across a wide range mixtures (Figure 5D-F).  E/I assemblies therefore support the quantification of learned odors within mixtures or, more generally, assessments of how strongly a (potentially complex) input is related to relevant odors stored in memory. Such a metric assessment of stimulus quality is not well supported by discrete attractor networks because inputs are mapped onto discrete network states.

The observation that Tuned networks do not map inputs onto discrete outputs indicates that such networks do not classify inputs as distinct items. Nonetheless, the observed geometrical modifications of continuous representations support the classification of learned inputs or the assessment of metric relationships by hypothetical readout neurons. Geometrical modifications of odor representations may therefore serve as one of multiple steps in multi-layer computations for pattern classification (and/or other computations). In this scenario, the transformation of odor representations in Dp may be seen as related to transformations of representations between different layers in artificial networks, which collectively perform a given task (notwithstanding obvious structural and mechanistic differences between artificial and biological networks). In other words, geometrical transformations of representations in Tuned networks may overrepresent learned (relevant) information at the expense of other information and thereby support further learning processes in other brain areas. An obvious corollary of this scenario is that Dp does not perform odor classification per se based on inputs from the olfactory bulb but reformats representations of odor space based on experience to support computational tasks as part of a larger system. This scenario is now explicitly discussed (p.14).

Reviewer #2 (Public Review): 

Summary: 

The authors conducted a comparative analysis of four networks, varying in the presence of excitatory assemblies and the architecture of inhibitory cell assembly connectivity. They found that co-tuned E-I assemblies provide network stability and a continuous representation of input patterns (on locally constrained manifolds), contrasting with networks with global inhibition that result in attractor networks. 

Strengths: 

The findings presented in this paper are very interesting and cutting-edge. The manuscript effectively conveys the message and presents a creative way to represent high-dimensional inputs and network responses. Particularly, the result regarding the projection of input patterns onto local manifolds and continuous representation of input/memory is very Intriguing and novel. Both computational and experimental neuroscientists would find value in reading the paper. 

Weaknesses: 

that have continuous representations. This could also be shown in Figure 5B, along with the performance of the random and tuned E-I networks. The latter networks have the advantage of providing network stability compared to the Scaled I network, but at the cost of reduced network salience and, therefore, reduced input decodability. The authors may consider designing a decoder to quantify and compare the classification performance of all four networks. 

We have now quantified classification by networks with discrete attractor dynamics (Scaled) along with other networks. However, because the neuronal covariance matrix for such networks is low rank and not invertible, pattern classification cannot be analyzed by QDA as in Figure 5B. We therefore classified patterns from the odor subspace by template matching, assigning test patterns to one of the four classes based on correlations (see Supplementary Figure 8). As expected, Scaled networks performed well, but they did not outperform Tuned networks. Moreover, the performance of Scaled networks, but not Tuned networks, depended on the order in which odors were presented to the network. This hysteresis effect is a direct consequence of persistent attractor states and decreased the general classification performance of Scaled networks (see Supplementary Figure 8 for details). These results confirm the prediction that networks with discrete attractor states can efficiently classify inputs, but also reveal disadvantages arising from attractor dynamics. Moreover, the results indicate that the classification performance of Tuned networks is also high under the given task conditions, which simulate a biologically realistic scenario.

We would also like to emphasize that classification may not be the only task, and perhaps not even a main task, of Dp/piriform cortex or other memory networks with E/I assemblies. Conceivably, other computations could include metric assessments of inputs relative to learned inputs or additional learning-related computations. Please see our response to comment (3) of reviewer 1 for a further discussion of this issue. 

Networks featuring E/I assemblies could potentially represent multistable attractors by exploring the parameter space for their reciprocal connectivity and connectivity with the rest of the network. However, for co-tuned E-I networks, the scope for achieving multistability is relatively constrained compared to networks employing global or lateral inhibition between assemblies. It would be good if the authors mentioned this in the discussion. Also, the fact that reciprocal inhibition increases network stability has been shown before and should be cited in the statements addressing network stability (e.g., some of the citations in the manuscript, including Rost et al. 2018, Lagzi & Fairhall 2022, and Vogels et al. 2011 have shown this).  

We thank the reviewer for this comment. We now explicitly discuss multistability (see p. 12) and refer to additional references in the statements addressing network stability.

Providing raster plots of the pDp network for familiar and novel inputs would help with understanding the claims regarding continuous versus discrete representation of inputs, allowing readers to visualize the activity patterns of the four different networks. (similar to Figure 1B). 

We thank the reviewer for this suggestion. We have added raster plots of responses to both familiar and novel inputs in the revised manuscript (Figure 2D and Supplementary Figure 4A).

Reviewer #3 (Public Review): 

Summary: 

This work investigates the computational consequences of assemblies containing both excitatory and inhibitory neurons (E/I assembly) in a model with parameters constrained by experimental data from the telencephalic area Dp of zebrafish. The authors show how this precise E/I balance shapes the geometry of neuronal dynamics in comparison to unstructured networks and networks with more global inhibitory balance. Specifically, E/I assemblies lead to the activity being locally restricted onto manifolds - a dynamical structure in between high-dimensional representations in unstructured networks and discrete attractors in networks with global inhibitory balance. Furthermore, E/I assemblies lead to smoother representations of mixtures of stimuli while those stimuli can still be reliably classified, and allow for more robust learning of additional stimuli. 

Strengths: 

Since experimental studies do suggest that E/I balance is very precise and E/I assemblies exist, it is important to study the consequences of those connectivity structures on network dynamics. The authors convincingly show that E/I assemblies lead to different geometries of stimulus representation compared to unstructured networks and networks with global inhibition. This finding might open the door for future studies for exploring the functional advantage of these locally defined manifolds, and how other network properties allow to shape those manifolds. 

The authors also make sure that their spiking model is well-constrained by experimental data from the zebrafish pDp. Both spontaneous and odor stimulus triggered spiking activity is within the range of experimental measurements. But the model is also general enough to be potentially applied to findings in other animal models and brain regions. 

Weaknesses: 

I find the point about pattern completion a bit confusing. In Fig. 3 the authors argue that only the Scaled I network can lead to pattern completion for morphed inputs since the output correlations are higher than the input correlations. For me, this sounds less like the network can perform pattern completion but it can nonlinearly increase the output correlations. Furthermore, in Suppl. Fig. 3 the authors show that activating half the assembly does lead to pattern completion in the sense that also non-activated assembly cells become highly active and that this pattern completion can be seen for Scaled I, Tuned E+I, and Tuned I networks. These two results seem a bit contradictory to me and require further clarification, and the authors might want to clarify how exactly they define pattern completion. 

We believe that this comment concerns a semantic misunderstanding and apologize for any lack of clarity. We added a definition of pattern completion in the text: “…the retrieval of the whole memory from noisy or corrupted versions of the learned input.”. Pattern completion may be assessed using different procedures. In computational studies, it is often analyzed by delivering input to a subset of the assembly neurons which store a given memory (partial activation). Under these conditions, we find recruitment of the entire assembly in all structured networks, as demonstrated in Supplementary Figure 3. However, these conditions are unlikely to occur during odor presentation because the majority of neurons do not receive any input.

Another more biologically motivated approach to assess pattern completion is to gradually modify a realistic odor input into a learned input, thereby gradually increasing the overlap between the two inputs. This approach had been used previously in experimental studies (references added to the text p.6). In the presence of assemblies, recurrent connectivity is expected to recruit assembly neurons (and thus retrieve the stored pattern) more efficiently as the learned pattern is approached. This should result in a nonlinear increase in the similarity between the evoked and the learned activity pattern. This signature was prominent in Scaled networks but not in Tuned or rand networks. Obviously, the underlying procedure is different from the partial activation of the assembly described above because input patterns target many neurons (including neurons outside assemblies) and exhibit a biologically realistic distribution of activity. However, this approach has also been referred to as “pattern completion” in the neuroscience literature, which may be the source of semantic confusion here. To clarify the difference between these approaches we have now revised the text and explicitly described each procedure in more detail (see p.6). 

The authors argue that Tuned E+I networks have several advantages over Scaled I networks. While I agree with the authors that in some cases adding this localized E/I balance is beneficial, I believe that a more rigorous comparison between Tuned E+I networks and Scaled I networks is needed: quantification of variance (Fig. 4G) and angle distributions (Fig. 4H) should also be shown for the Scaled I network. Similarly in Fig. 5, what is the Mahalanobis distance for Scaled I networks and how well can the Scaled I network be classified compared to the Tuned E+I network? I suspect that the Scaled I network will actually be better at classifying odors compared to the E+I network. The authors might want to speculate about the benefit of having networks with both sources of inhibition (local and global) and hence being able to switch between locally defined manifolds and discrete attractor states. 

We agree that a more rigorous comparison of Tuned and Scaled networks would be of interest. We have added the variance analysis (Fig 4G) and angle distributions (Fig. 4H) for both Tuned I and Scaled networks. However, the Mahalanobis distances and Quadratic Discriminant Analysis cannot be applied to Scaled networks because their neuronal covariance matrix is low rank and not invertible_. To nevertheless compare these networks, we performed template matching by assigning test patterns to one of the four odor classes based on correlations to template patterns (Supplementary Figure 8; see also response to the first comment of reviewer 2). Interestingly, _Scaled networks performed well at classification but did not outperform Tuned networks, and exhibited disadvantages arising from attractor dynamics (Supplementary Figure 8; see also response to the first comment of reviewer 2). Furthermore, in further analyses we found that continuous representational manifolds support metric assessments of inputs relative to learned odors, which cannot be achieved by discrete representations. These results are now shown in Figure 5D-E and discussed explicitly in the text on p.11 (see also response to comment 3 of reviewer 1).

We preferred not to add a sentence in the Discussion about benefits of networks having both sources of inhibition_,_ as we find this a bit too speculative.

At a few points in the manuscript, the authors use statements without actually providing evidence in terms of a Figure. Often the authors themselves acknowledge this, by adding the term "not shown" to the end of the sentence. I believe it will be helpful to the reader to be provided with figures or panels in support of the statements.  

Thank you for this comment. We have provided additional data figures to support the following statements:

“d_M was again increased upon learning, particularly between learned odors and reference classes representing other odors (Supplementary Figure 9)”

“decreasing amplification in assemblies of Scaled networks changed transformations towards the intermediate behavior, albeit with broader firing rate distributions than in Tuned networks (Supplementary Figure 6 B)”  

Recommendations for the authors:

Reviewer #1 (Recommendations For The Authors): 

Meissner-Bernard et al present a biologically constrained model of telencephalic area of adult zebrafish, a homologous area to the piriform cortex, and argue for the role of precisely balanced memory networks in olfactory processing. 

This is interesting as it can add to recent evidence on the presence of functional subnetworks in multiple sensory cortices. It is also important in deviating from traditional accounts of memory systems as attractor networks. Evidence for attractor networks has been found in some systems, like in the head direction circuits in the flies. However, the presence of attractor dynamics in other modalities, like sensory systems, and their role in computation has been more contentious. This work contributes to this active line of research in experimental and computational neuroscience by suggesting that, rather than being represented in attractor networks and persistent activity, olfactory memories might be coded by balanced excitation-inhibitory subnetworks. 

The paper is generally well-written, the figures are informative and of good quality, and multiple approaches and metrics have been used to test and support the main results of the paper. 

The main strength of the work is in: (1) direct link to biological parameters and measurements, (2) good controls and quantification of the results, and (3) comparison across multiple models. 

(1) The authors have done a good job of gathering the current experimental information to inform a biological-constrained spiking model of the telencephalic area of adult zebrafish. The results are compared to previous experimental measurements to choose the right regimes of operation. 

(2) Multiple quantification metrics and controls are used to support the main conclusions and to ensure that the key parameters are controlled for - e.g. when comparing across multiple models.   (3) Four specific models (random, scaled I / attractor, and two variant of specific E-I networks - tuned I and tuned E+I) are compared with different metrics, helping to pinpoint which features emerge in which model. 

Major problems with the work are: (1) mechanistic explanation of the results in specific E-I networks, (2) parameter exploration, and (3) the functional significance of the specific E-I model. 

(1) The main problem with the paper is a lack of mechanistic analysis of the models. The models are treated like biological entities and only tested with different assays and metrics to describe their different features (e.g. different geometry of representation in Fig. 4). Given that all the key parameters of the models are known and can be changed (unlike biological networks), it is expected to provide a more analytical account of why specific networks show the reported results. For instance, what is the key mechanism for medium amplification in specific E/I network models (Fig. 3)? How does the specific geometry of representation/manifolds (in Fig. 4) emerge in terms of excitatory-inhibitory interactions, and what are the main mechanisms/parameters? Mechanistic account and analysis of these results are missing in the current version of the paper. 

Precise balancing of excitation and inhibition in subnetworks would lead to the cancellation of specific dynamical modes responsible for the amplification of responses (hence, deviating from the attractor dynamics with an unstable specific mode). What is the key difference in the specific E/I networks here (tuned I or/and tuned E+I) which make them stand between random and attractor networks? Excitatory and inhibitory neurons have different parameters in the model (Table 1). Time constants of inhibitory and excitatory synapses are also different (P. 13). Are these parameters causing networks to be effectively more excitation dominated (hence deviating from a random spectrum which would be expected from a precisely balanced E/I network, with exactly the same parameters of E and I neurons)? It is necessary to analyse the network models, describe the key mechanism for their amplification, and pinpoint the key differences between E and I neurons which are crucial for this. 

To address these comments we performed additional simulations and analyses at different levels. Please see our reply to comment (1) of the public review (reviewer 1) for a detailed description. We thank the reviewer for these constructive comments.

(2) The second major issue with the study is a lack of systematic exploration and analysis of the parameter space. Some parameters are biologically constrained, but not all the parameters. For instance, it is not clear what the justification for the choice of synaptic time scales are (with E synaptic time constants being larger than inhibition: tau_syn_i = 10 ms, tau_syn_E = 30 ms). How would the results change if they are varying these - and other unconstrained - parameters? It is important to show how the main results, especially the manifold localisation, would change by doing a systematic exploration of the key parameters and performing some sensitivity analysis. This would also help to see how robust the results are, which parameters are more important and which parameters are less relevant, and to shed light on the key mechanisms.  

We thank the reviewer for this comment. We have now carried out additional simulations with equal time constants for all neurons. Please see our reply to the public review for more details (comment 2 of reviewer 1).

(3) It is not clear what the main functional advantage of the specific E-I network model is compared to random networks. In terms of activity, they show that specific E-I networks amplify the input more than random networks (Fig. 3). But when it comes to classification, the effect seems to be very small (Fig. 5c). Description of different geometry of representation and manifold localization in specific networks compared to random networks is good, but it is more of an illustration of different activity patterns than proving a functional benefit for the network. The reader is still left with the question of what major functional benefits (in terms of computational/biological processing) should be expected from these networks, if they are to be a good model for olfactory processing and learning. 

One possibility for instance might be that the tasks used here are too easy to reveal the main benefits of the specific models - and more complex tasks would be needed to assess the functional enhancement (e.g. more noisy conditions or more combination of odours). It would be good to show this more clearly - or at least discuss it in relation to computation and function.

Please see our reply to the public review (comment 3 of reviewer 1).

Specific comments: 

Abstract: "resulting in continuous representations that reflected both relatedness of inputs and *an individual's experience*" 

It didn't become apparent from the text or the model where the role of "individual's experience" component (or "internal representations" - in the next line) was introduced or shown (apart from a couple of lines in the Discussion) 

We consider the scenario that that assemblies are the outcome of an experience-dependent plasticity process. To clarify this, we have now made a small addition to the text: “Biological memory networks are thought to store information by experience-dependent changes in the synaptic connectivity between assemblies of neurons.”.

P. 2: "The resulting state of "precise" synaptic balance stabilizes firing rates because inhomogeneities or fluctuations in excitation are tracked by correlated inhibition" 

It is not clear what the "inhomogeneities" specifically refers to - they can be temporal, or they can refer to the quenched noise of connectivity, for instance. Please clarify what you mean. 

The statement has been modified to be more precise: “…“precise” synaptic balance stabilizes firing rates because inhomogeneities in excitation across the population or temporal variations in excitation are tracked by correlated inhibition…”.

P. 3 (and Methods): When odour stimulus is simulated in the OB, the activity of a fraction of mitral cells is increased (10% to 15 Hz) - but also a fraction of mitral cells is suppressed (5% to 2 Hz). What is the biological motivation or reference for this? It is not provided. Is it needed for the results? Also, it is not explained how the suppressed 5% are chosen (e.g. randomly, without any relation to the increased cells?). 

We thank the reviewer for this comment. These changes in activity directly reflect experimental observations. We apologize that we forgot to include the references reporting these observations (Friedrich and Laurent, 2001 and 2004); this is now fixed.

In our simulation, OB neurons do not interact with each other, and the suppressed 5% were indeed randomly selected. We changed the text in Methods accordingly to read: “An additional 75 randomly selected mitral cells were inhibited” 

P. 4, L. 1-2: "... sparsely connected integrate-and-fire neurons with conductance-based synapses (connection probability {less than or equal to}5%)." 

Specify the connection probability of specific subtypes (EE, EI, IE, II).  

We now refer to the Methods section, where this information can be found. 

“... conductance-based synapses (connection probability ≤5%, Methods)”  

P. 4, L. 6-7: "Population activity was odor-specific and activity patterns evoked by uncorrelated OB inputs remained uncorrelated in Dp (Figure 1H)" 

What would happen to correlated OB inputs (e.g. as a result of mixture of two overlapping odours) in this baseline state of the network (before memories being introduced to it)? It would be good to know this, as it sheds light on the initial operating regime of the network in terms of E/I balance and decorrelation of inputs.  

This information was present in the original manuscript at (Figure 3) but we improved the writing to further clarify this issue: “ (…) we morphed a novel odor into a learned odor (Figure 3A), or a learned odor into another learned odor (Supplementary Figure 3B), and quantified the similarity between morphed and learned odors by the Pearson correlation of the OB activity patterns (input correlation). We then compared input correlations to the corresponding pattern correlations among E neurons in Dp (output correlation). In rand networks, output correlations increased linearly with input correlations but did not exceed them (Figure 3B and Supplementary Figure 3B)”

P. 4, L. 12-13: "Shuffling spike times of inhibitory neurons resulted in runaway activity with a probability of ~80%, .."   Where is this shown? 

(There are other occasions too in the paper where references to the supporting figures are missing). 

We now provide the statistics: “Shuffling spike times of inhibitory neurons resulted in runaway activity with a probability of 0.79 ± 0.20”

P. 4: "In each network, we created 15 assemblies representing uncorrelated odors. As a consequence, ~30% of E neurons were part of an assembly ..." 

15 x 100 / 4000 = 37.5% - so it's closer to 40% than 30%. Unless there is some overlap? 

Yes: despite odors being uncorrelated and connectivity being random, some neurons (6 % of E neurons) belong to more than one assembly.

P. 4: "When a reached a critical value of ~6, networks became unstable and generated runaway activity (Figure 2B)." 

Can this transition point be calculated or estimated from the network parameters, and linked to the underlying mechanisms causing it? 

We thank the reviewer for this interesting question. The unstability arises when inhibitions fails to counterbalance efficiently the increased recurrent excitation within Dp. The transition point is difficult to estimate, as it can depend on several parameters, including the probability of E to E connections, their strength, assembly size, and others. We have therefore not attempted to estimate it analytically.

P. 4: "Hence, non-specific scaling of inhibition resulted in a divergence of firing rates that exhausted the dynamic range of individual neurons in the population, implying that homeostatic   global inhibition is insufficient to maintain a stable firing rate distribution." 

I don't think this is justified based on the results and figures presented here (Fig. 2E) - the interpretation is a bit strong and biased towards the conclusions the authors want to draw. 

To more clearly illustrate the finding that in Scaled networks, assembly neurons are highly active (close to maximal realistic firing rates) whereas non-assembly neurons are nearly silent we have now added Supplementary Fig. 2B. Moreover, we have toned down the text: “Hence, non-specific scaling of inhibition resulted in a large and biologically unrealistic divergence of firing rates (Supplementary Figure 2B) that nearly exhausted the dynamic range of individual neurons in the population, indicating that homeostatic global inhibition is insufficient to maintain a stable firing rate distribution”

P. 5, third paragraph: Description of Figure 2I, inset is needed, either in the text or caption. 

The inset is now referred to in the text: ”we projected synaptic conductances of each neuron onto a line representing the E/I ratio expected in a balanced network (“balanced axis”) and onto an orthogonal line (“counter-balanced axis”; Figure 2I inset, Methods).”

P. 5, last paragraph: another example of writing about results without showing/referring to the corresponding figures: 

"In rand networks, firing rates increased after stimulus onset and rapidly returned to a low baseline after stimulus offset. Correlations between activity patterns evoked by the same odor at different time points and in different trials were positive but substantially lower than unity, indicating high variability ..." 

And the continuation with similar lack of references on P. 6: 

"Scaled networks responded to learned odors with persistent firing of assembly neurons and high pattern correlations across trials and time, implying attractor dynamics (Hopfield, 1982; Khona and Fiete, 2022), whereas Tuned networks exhibited transient responses and modest pattern correlations similar to rand networks." 

Please go through the Results and fix the references to the corresponding figures on all instances. 

We thank the reviewer for pointing out these overlooked figure references, which are now fixed.

P. 8: "These observations further support the conclusion that E/I assemblies locally constrain neuronal dynamics onto manifolds." 

As discussed in the general major points, mechanistic explanation in terms of how the interaction of E/I dynamics leads to this is missing. 

As discussed in the reply to the public review (comment 3 of reviewer 1), we have now provided more mechanistic analyses of our observations.

P. 9: "Hence, E/I assemblies enhanced the classification of inputs related to learned patterns."   The effect seems to be very small. Also, any explanation for why for low test-target correlation the effect is negative (random doing better than tuned E/I)? 

The size of the effect (plearned – pnovel = 0.074; difference of means; Figure 5C) may appear small in terms of absolute probability, but it is substantial relative to the maximum possible increase (1 – p_novel =  0.133; Figure 5C). The fact that for low test-target correlations the effect is negative is a direct consequence of the positive effect for high test-target correlations and the presence of 2 learned odors in the 4-way forced choice task. 

P. 9: "In Scaled I networks, creating two additional memories resulted in a substantial increase   in firing rates, particularly in response to the learned and related odors"   Where is this shown? Please refer to the figure. 

We thank the reviewer again for pointing this out. We forgot to include a reference to the relevant figure which has now been added in the revised manuscript (Figure 6C).

P. 10: "The resulting Tuned networks reproduced additional experimental observations that were not used as constraints including irregular firing patterns, lower output than input correlations, and the absence of persistent activity" 

It is difficult to present these as "additional experimental observations", as all of them are negative, and can exist in random networks too - hence cannot be used as biological evidence in favour of specific E/I networks when compared to random networks. 

We agree with the reviewer that these additional experimental observations cannot be used as biological evidence favouring Tuned E+I networks over random networks. We here just wanted to point out that additional observations which we did not take into account to fit the model are not invalidating the existence of E-I assemblies in biological networks. As assemblies tend to result in persistent activity in other types of networks, we feel that this observation is worth pointing out.

Methods: 

P. 13: Describe the parameters of Eq. 2 after the equation. 

Done.

P. 13: "The time constants of inhibitory and excitatory synapses were 10 ms and 30 ms, respectively." 

What is the (biological) justification for the choice of these parameters? 

How would varying them affect the main results (e.g. local manifolds)? 

We chose a relatively slow time constant for excitatory synapses because experimental data indicate that excitatory synaptic currents in Dp and piriform cortex contain a prominent NMDA component. We have now also simulated networks with equal time constants for excitatory and inhibitory synapses and equal biophysical parameters for excitatory and inhibitory neurons, which did not affect the main results (see also reply to the public review: comment 2 of reviewer 1).

P. 14: "Care was also taken to ensure that the variation in the number of output connections was low across neurons"   How exactly?

More detailed explanations have now been added in the Methods section: “connections of a presynaptic neuron y to postsynaptic neurons x were randomly deleted when their total number exceeded the average number of output connections by ≥5%, or added when they were lower by ≥5%.“

Reviewer #2 (Recommendations For The Authors): 

Congratulations on the great and interesting work! The results were nicely presented and the idea of continuous encoding on manifolds is very interesting. To improve the quality of the paper, in addition to the major points raised in the public review, here are some more detailed comments for the paper: 

(1) Generally, citations have to improve. Spiking networks with excitatory assemblies and different architectures of inhibitory populations have been studied before, and the claim about improved network stability in co-tuned E-I networks has been made in the following papers that need to be correctly cited: 

• Vogels TP, Sprekeler H, Zenke F, Clopath C, Gerstner W. 2011. Inhibitory Plasticity Balances Excitation and Inhibition in Sensory Pathways and Memory Networks. Science 334:1-7. doi:10.1126/science.1212991 (mentions that emerging precise balance on the synaptic weights can result in the overall network stability) 

• Lagzi F, Bustos MC, Oswald AM, Doiron B. 2021. Assembly formation is stabilized by Parvalbumin neurons and accelerated by Somatostatin neurons. bioRxiv doi: https://doi.org/10.1101/2021.09.06.459211 (among other things, contrasts stability and competition which arises from multistable networks with global inhibition and reciprocal inhibition)   • Rost T, Deger M, Nawrot MP. 2018. Winnerless competition in clustered balanced networks: inhibitory assemblies do the trick. Biol Cybern 112:81-98. doi:10.1007/s00422-017-0737-7 (compares different architectures of inhibition and their effects on network dynamics) 

• Lagzi F, Fairhall A. 2022. Tuned inhibitory firing rate and connection weights as emergent network properties. bioRxiv 2022.04.12.488114. doi:10.1101/2022.04.12.488114 (here, see the eigenvalue and UMAP analysis for a network with global inhibition and E/I assemblies) 

Additionally, there are lots of pioneering work about tracking of excitatory synaptic inputs by inhibitory populations, that are missing in references. Also, experimental work that show existence of cell assemblies in the brain are largely missing. On the other hand, some references that do not fit the focus of the statements have been incorrectly cited. 

The authors may consider referencing the following more pertinent studies on spiking networks to support the statement regarding attractor dynamics in the first paragraph in the Introduction (the current citations of Hopfield and Kohonen are for rate-based networks): 

• Wong, K.-F., & Wang, X.-J. (2006). A recurrent network mechanism of time integration in perceptual decisions. Journal of Neuroscience, 26(4), 1314-1328. https://doi.org/10.1523/JNEUROSCI.3733-05.2006 

• Wang, X.-J. (2008). Decision making in recurrent neuronal circuits. Neuron, 60(2), 215-234. https://doi.org/10.1016/j.neuron.2008.09.034  

• F. Lagzi, & S. Rotter. (2015). Dynamics of competition between subnetworks of spiking neuronal networks in the balanced state. PloS One. 

• Goldman-Rakic, P. S. (1995). Cellular basis of working memory. Neuron, 14(3), 477-485. 

• Rost T, Deger M, Nawrot MP. 2018. Winnerless competition in clustered balanced networks: inhibitory assemblies do the trick. Biol Cybern 112:81-98. doi:10.1007/s00422-017-0737-7. 

• Amit DJ, Tsodyks M (1991) Quantitative study of attractor neural network retrieving at low spike rates: I. substrate-spikes, rates and neuronal gain. Network 2:259-273. 

• Mazzucato, L., Fontanini, A., & La Camera, G. (2015). Dynamics of Multistable States during Ongoing and Evoked Cortical Activity. Journal of Neuroscience, 35(21), 8214-8231. 

We thank the reviewer for the references suggestions. We have carefully reviewed the reference list and made the following changes, which we hope address the reviewer’s concerns:

(1) We adjusted References about network stability in co-tuned E-I networks.

(2) We added the Lagzi & Rotter (2015), Amit et al. (1991), Mazzucato et al. (2015) and GoldmanRakic (1995) papers in the Introduction as studies on attractor dynamics in spiking neural networks. We preferred to omit the two X.J Wang papers, as they describe attractors in decision making rather than memory processes.

(3) We added the Ko et al. 2011 paper as experimental evidence for assemblies in the brain. In our view, there are few experimental studies showing the existence of cell assemblies in the brain, which we distinguish from cell ensembles, group of coactive neurons. 

(4) We also included Hennequin 2018, Brunel 2000, Lagzi et al. 2021 and Eckmann et al. 2024, which we had not cited in the initial manuscript.

(5) We removed the Wiechert et al. 2010 reference as it does not support the statement about geometry-preserving transformation by random networks.

(2) The gist of the paper is about how the architecture of inhibition (reciprocal vs. global in this case) can determine network stability and salient responses (related to multistable attractors and variations) for classification purposes. It would improve the narrative of the paper if this point is raised in the Introduction and Discussion section. Also see a relevant paper that addresses this point here: 

Lagzi F, Bustos MC, Oswald AM, Doiron B. 2021. Assembly formation is stabilized by Parvalbumin neurons and accelerated by Somatostatin neurons. bioRxiv doi: https://doi.org/10.1101/2021.09.06.459211 

Classification has long been proposed to be a function of piriform cortex and autoassociative memory networks in general, and we consider it important. However, the computational function of Dp or piriform cortex is still poorly understood, and we do not focus only on odor classification as a possibility. In fact, continuous representational manifolds also support other functions such as the quantification of distance relationships of an input to previously memorized stimuli, or multi-layer network computations (including classification). In the revised manuscript, we have performed additional analyses to explore these notions in more detail, as explained above (response to public reviews, comment 3 of reviewer 1). Furthermore, we have now expanded the discussion of potential computational functions of Tuned networks and explicitly discuss classification but also other potential functions. 

(3) A plot for the values of the inhibitory conductances in Figure 1 would complete the analysis for that section. 

In Figure 1, we decided to only show the conductances that we use to fit our model, namely the afferent and total synaptic conductances. As the values of the inhibitory conductances can be derived from panel E, we refrained from plotting them separately for the sake of simplicity. 

(4) How did the authors calculate correlations between activity patterns as a function of time in Figure 2E, bottom row? Does the color represent correlation coefficient (which should not be time dependent) or is it a correlation function? This should be explained in the Methods section. 

The color represents the Pearson correlation coefficient between activity patterns within a narrow time window (100 ms). We updated the Figure legend to clarify this: “Mean correlation between activity patterns evoked by a learned odor at different time points during odor presentation. Correlation coefficients were calculated between pairs of activity vectors composed of the mean firing rates of E neurons in 100 ms time bins. Activity vectors were taken from the same or different trials, except for the diagonal, where only patterns from different trials were considered.”

(5) Figure 3 needs more clarification (both in the main text and the figure caption). It is not clear what the axes are exactly, and why the network responses for familiar and novel inputs are different. The gray shaded area in panel B needs more explanation as well.  

We thank the reviewer for the comment. We have improved Figure 3A, the figure caption, as well as the text (see p.6). We hope that the figure is now clearer.

(6) The "scaled I" network, known for representing input patterns in discrete attractors, should exhibit clear separation between network responses in the 2D PC space in the PCA plots. However, Figure 4D and Figure 6D do not reflect this, as all network responses are overlapped. Can the authors explain the overlap in Figure 4D? 

In Figure 4D, activity of Scaled networks is distributed between three subregions in state space that are separated by the first 2 PCs. Two of them indeed correspond to attractor states representing the two learned odors while the third represents inputs that are not associated with these attractor states. To clarify this, please see also the density plot in Figure 4E. The few datapoints between these three subregions are likely outliers generated by the sequential change in inputs, as described in Supplementary Figure 8C.

(7) The reason for writing about the ISN networks is not clear. Co-tuned E-I assemblies do not necessarily have to operate in this regime. Also, the results of the paper do not rely on any of the properties of ISNs, but they are more general. Authors should either show the paradoxical effect associated with ISN (i.e., if increasing input to I neurons decreases their responses) or show ISN properties using stability analysis (See computational research conducted at the Allen Institute, namely Millman et al. 2020, eLife ). Currently, the paper reads as if being in the ISN regime is a necessary requirement, which is not true. Also, the arguments do not connect with the rest of the paper and never show up again. Since we know it is not a requirement, there is no need to have those few sentences in the Results section. Also, the choice of alpha=5.0 is extreme, and therefore, it would help to judge the biological realism if the raster plots for Figs 2-6 are shown.

We have toned down the part on ISN and reduced it to one sentence for readers who might be interested in knowing whether activity is inhibition-stabilized or not. We have also added the reference to the Tsodyks et al. 1997 paper from which we derive our stability analysis. The text now reads “Hence, pDp_sim entered a balanced state during odor stimulation (Figure 1D, E) with recurrent input dominating over afferent input, as observed in pDp (Rupprecht and Friedrich, 2018). Shuffling spike times of inhibitory neurons resulted in runaway activity with a probability of 0.79 ± 0.20, demonstrating that activity was inhibition-stabilized (Sadeh and Clopath, 2020b, Tsodyks et al., 1997).”  

We have now also added the raster plots as suggested by the reviewer (see Figure 2D, Supplementary Figure 1 G, Supplementary Figure 4). We thank the reviewer for this comment.

(8) In the abstract, authors mention "fast pattern classification" and "continual learning," but in the paper, those issues have not been addressed. The study does not include any synaptic plasticity. 

Concerning “continual learning” we agree that we do not simulate the learning process itself. However, Figure 6 show results of a simulation where two additional patterns were stored in a network that already contained assemblies representing other odors. We consider this a crude way of exploring the end result of a “continual learning” process. “Fast pattern classification” is mentioned because activity in balanced networks can follow fluctuating inputs with high temporal resolution, while networks with stable attractor states tend to be slow. This is likely to account for the occurrence of hysteresis effects in Scaled but not Tuned networks as shown in Supplementary

Fig. 8.

(9) In the Introduction, the first sentence in the second paragraph reads: "... when neurons receive strong excitatory and inhibitory synaptic input ...". The word strong should be changed to "weak".

Also, see the pioneering work of Brunel 2000. 

In classical balanced networks, strong excitatory inputs are counterbalanced by strong inhibitory inputs, leading to a fluctuation-driven regime. We have added Brunel 2000.

(10) In the second paragraph of the introduction, the authors refer to studies about structural co-tuning (e.g., where "precise" synaptic balance is mentioned, and Vogels et al. 2011 should be cited there) and functional co-tuning (which is, in fact, different than tracking of excitation by inhibition, but the authors refer to that as co-tuning). It makes it easier to understand which studies talk about structural co-tuning and which ones are about functional co-tuning. The paper by Znamenski 2018, which showed both structural and functional tuning in experiments, is missing here. 

We added the citation to the now published paper by Znamenskyi et al. (2024).  

(11) The third paragraph in the Introduction misses some references that address network dynamics that are shaped by the inhibitory architecture in E/I assemblies in spiking networks, like Rost et al 2018 and Lagzi et al 2021. 

These references have been added.

(12) The last sentence of the fourth paragraph in the Introduction implies that functional co-tuning is due to structural co-tuning, which is not necessarily true. While structural co-tuning results in functional co-tuning, functional co-tuning does not require structural co-tuning because it could arise from shared correlated input or heterogeneity in synaptic connections from E to I cells.  

We generally agree with the reviewer, but we are uncertain which sentence the reviewer refers to.

We assume the reviewer refers to the last sentence of the second (rather than the fourth paragraph), which explicitly mentions the “…structural basis of E/I co-tuning…”. If so, we consider this sentence still correct because the “structural basis” refers not specifically to E/I assemblies, but also includes any other connectivity that may produce co-tuning, including the connectivity underlying the alternative possibilities mentioned by the reviewer (shared correlated input or heterogeneity of synaptic connections).

(13) In order to ensure that the comparison between network dynamics is legit, authors should mention up front that for all networks, the average firing rates for the excitatory cells were kept at 1 Hz, and the background input was identical for all E and I cells across different networks.

We slightly revised the text to make this more clear “We (…) uniformly scaled I-to-E connection weights by a factor of χ until E population firing rates in response to learned odors matched the corresponding firing rates in rand networks, i.e., 1 Hz”

(14) In the last paragraph on page 5, my understanding was that an individual odor could target different cells within an assembly in different trials to generate trial to trail variability. If this is correct, this needs to be mentioned clearly. 

This is not correct, an odor consists of 150 activated mitral cells with defined firing rates. As now mentioned in the Methods, “Spikes were then generated from a Poisson distribution, and this process was repeated to create trial-to-trial variability.”

(15) The last paragraph on page 6 mentions that the four OB activity patterns were uncorrelated but if they were designed as in Figure 4A, dues to the existing overlap between the patterns, they cannot be uncorrelated. 

This appears to be a misunderstanding. We mention in the text (and show in Figure 4B) that the four odors which “… were assigned to the corners of a square…” are uncorrelated.  The intermediate odors are of course not uncorrelated. We slightly modified the corresponding paragraph (now on page 7) to clarify this: “The subspace consisted of a set of OB activity patterns representing four uncorrelated pure odors and mixtures of these pure odors. Pure odors were assigned to the corners of a square and mixtures were generated by selecting active mitral cells from each of the pure odors with probabilities depending on the relative distances from the corners (Figure 4A, Methods).”

(16) The notion of "learned" and "novel" odors may be misleading as there was no plasticity in the network to acquire an input representation. It would be beneficial for the authors to clarify that by "learned," they imply the presence of the corresponding E assembly for the odor in the network, with the input solely impacting that assembly. Conversely, for "novel" inputs, the input does not target a predefined assembly. In Figure 2 and Figure 4, it would be especially helpful to have the spiking raster plots of some sample E and I cells.  

As suggested by the reviewer, we have modified the existing spiking raster plots in Figure 2, such that they include examples of responses to both learned and novel odors. We added spiking raster plots showing responses of I neurons to the same odors in Supplementary Figure 1F, as well as spiking raster plots of E neurons in Supplementary Figure 4A. To clarify the usage of “learned” and “novel”, we have added a sentence in the Results section: “We thus refer to an odor as “learned” when a network contains a corresponding assembly, and as “novel” when no such assembly is present.”.

(17) In the last paragraph of page 8, can the authors explain where the asymmetry comes from? 

As mentioned in the text, the asymmetry comes from the difference in the covariance structure of different classes. To clarify, we have rephrased the sentence defining the Mahalanobis distance: 

“This measure quantifies the distance between the pattern and the class center, taking into account covariation of neuronal activity within the class. In bidirectional comparisons between patterns from different classes, the mean dM may be asymmetric if neural covariance differs between classes.”

(18) The first paragraph of page 9: random networks are not expected to perform pattern classification, but just pattern representation. It would have been better if the authors compared Scaled I network with E/I co-tuned network. Regardless of the expected poorer performance of the E/I co-tuned networks, the result would have been interesting. 

Please see our reply to the public review (reviewer 2).

(19) Second paragraph on page 9, the authors should provide statistical significance test analysis for the statement "... was significantly higher ...". 

We have performed a Wilcoxon signed-rank test, and reported the p-value in the revised manuscript (p < 0.01). 

(20) The last sentence in the first paragraph on page 11 is not clear. What do the authors mean by "linearize input-output functions", and how does it support their claim? 

We have now amended this sentence to clarify what we mean: “…linearize the relationship between the mean input and output firing rates of neuronal populations…”.

(21) In the first sentence of the last paragraph on page 11, the authors mentioned “high variability”, but it is not clear compared with which of the other 3 networks they observed high variability.

Structurally co-tuned E/I networks are expected to diminish network-level variability. 

“High variability” refers to the variability of spike trains, which is now mentioned explicity in the text. We hope this more precise statement clarifies this point.

(22) Methods section, page 14: "firing rates decreased with a time constant of 1, 2 or 4 s". How did they decrease? Was it an implementation algorithm? The time scale of input presentation is 2 s and it overlaps with the decay time constant (particularly with the one with 4 s decrease).  

Firing rates decreased exponentially. We have added this information in the Methods section.

Reviewer #3 (Recommendations For The Authors): 

In the following, I suggest minor corrections to each section which I believe can improve the manuscript. 

- There was no github link to the code in the manuscript. The code should be made available with a link to github in the final manuscript. 

The code can be found here: https://github.com/clairemb90/pDp-model. The link has been added in the Methods section.

Figure 1: 

- Fig. 1A: call it pDp not Dp. Please check if this name is consistent in every figure and the text. 

Thank you for catching this. Now corrected in Figure 1, Figure 2 and in the text.

- The authors write: "Hence, pDpsim entered an inhibition-stabilized balanced state (Sadeh and Clopath, 2020b) during odor stimulation (Figure 1D, E)." and then later "Shuffling spike times of inhibitory neurons resulted in runaway activity with a probability of ~80%, demonstrating that activity was indeed inhibition-stabilized. These results were robust against parameter variations (Methods)." I would suggest moving the second sentence before the first sentence, because the fact that the network is in the ISN regime follows from the shuffled spike timing result. 

Also, I'd suggest showing this as a supplementary figure. 

We thank the reviewer for this comment. We have removed “inhibition-stabilized” in the first sentence as there is no strong evidence of this in Rupprecht and Friedrich, 2018. And removed “indeed” in the second sentence. We also provided more detailed statistics. The text now reads “Hence, pDpsim entered a balanced state during odor stimulation (Figure 1D, E) with recurrent input dominating over afferent input, as observed in pDp (Rupprecht and Friedrich, 2018). Shuffling spike times of inhibitory neurons resulted in runaway activity with a probability of 0.79 ± 0.20, demonstrating that activity was inhibition-stabilized (Sadeh and Clopath, 2020b).”

Figure 2: 

- "... Scaled I networks (Figure 2H." Missing ) 

Corrected.

- The authors write "Unlike in Scaled I networks, mean firing rates evoked by novel odors were indistinguishable from those evoked by learned odors and from mean firing rates in rand networks (Figure 2F)." 

Why is this something you want to see? Isn't it that novel stimuli usually lead to high responses? Eg in the paper Schulz et al., 2021 (eLife) which is also cited by the authors it is shown that novel responses have high onset firing rates. I suggest clarifying this (same in the context of Fig. 3C). 

In Dp and piriform cortex, firing rates evoked by learned odors are not substantially different from firing rates evoked by novel odors. While small differences between responses to learned versus novel odors cannot be excluded, substantial learning-related differences in firing rates, as observed in other brain areas, have not been described in Dp or piriform cortex. We added references in the last paragraph of p.5. Note that the paper by Schulz et al. (2021) models a different type of circuit.  

- Fig. 2B: Indicate in figure caption that this is the case "Scaled I" 

This is not exactly the case “Scaled I”, as the parameter 𝝌𝝌 (increased I to E strength) is set to 1.

- Suppl Fig. 2I: Is E&F ever used in the manuscript? I couldn't find a reference. I suggest removing it if not needed. 

Suppl. Fig 2I E&F is now Suppl Fig.1G&H. We now refer to it in the text: “Activity of networks with E assemblies could not be stabilized around 1 Hz by increasing connectivity from subsets of I neurons receiving dense feed-forward input from activated mitral cells (Supplementary Figure 1GH; Sadeh and Clopath, 2020).”

Figure 3: 

- As mentioned in my comment in the public review section, I find the arguments about pattern completion a little bit confusing. For me it's not clear why an increase of output correlations over input correlations is considered "pattern completion" (this is not to say that I don't find the nonlinear increase of output correlations interesting). For me, to test pattern completion with second-order statistics one would need to do a similar separation as in Suppl Fig. 3, ie measuring the pairwise correlation at cells in the assembly L that get direct input from L OB with cells in the assembly L that do not get direct input from OB. If the pairwise correlations of assembly cells which do not get direct input from OB increase in correlations, I would consider this as pattern completion (similar to the argument that increase in firing rate in cells which are not directly driven by OB are considered a sign of pattern completion). 

Also, for me it now seems like that there are contradictory results, in Fig. 3 only Scaled I can lead to pattern completion while in the context of Suppl. Fig. 3 the authors write "We found that assemblies were recruited by partial inputs in all structured pDpsim networks (Scaled and Tuned) without a significant increase in the overall population activity (Supplementary Figure 3A)."   I suggest clarifying what the authors exactly mean by pattern completion, why the increase of output correlations above input correlations can be considered as pattern completion, and why the results differs when looking at firing rates versus correlations. 

Please see our reply to the public review (reviewer 3).

- I actually would suggest adding Suppl. Fig. 3 to the main figure. It shows a more intuitive form of pattern completion and in the text there is a lot of back and forth between Fig. 3 and Suppl. Fig. 3 

We feel that the additional explanations and panels in Fig.3 should clarify this issue and therefore prefer to keep Supplementary Figure 3 as part of the Supplementary Figures for simplicity.  

- In the whole section "We next explored effects of assemblies ... prevented strong recurrent amplification within E/I assemblies." the authors could provide a link to the respective panel in Fig. 2 after each statement. This would help the reader follow your arguments. 

We thank the reviewer for pointing this out. The references to the appropriate panels have been added. 

- Fig. 3A: I guess the x-axis has been shifted upwards? Should be at zero. 

We have modified the x-axis to make it consistent with panels B and C.  

- Fig. 3B: In the figure caption, the dotted line is described as the novel odor but it is actually the unit line. The dashed lines represent the reference to the novel odor. 

Fixed.

- Fig. 3C: The " is missing for Pseudo-Assembly N

Fixed.

- "...or a learned odor into another learned odor." Have here a ref to the Supplementary Figure 3B.

Added.

Figure 4:   

- "This geometry was largely maintained in the output of rand networks, consistent with the notion that random networks tend to preserve similarity relationships between input patterns (Babadi and Sompolinsky, 2014; Marr, 1969; Schaffer et al., 2018; Wiechert et al., 2010)." I suggest adding here reference to Fig. 4D (left). 

Added.

- Please add a definition of E/I assemblies. How do the authors define E/I assemblies? I think they consider both, Tuned I and Tuned E+I as E/I assemblies? In Suppl. Fig. 2I E it looks like tuned feedforward input is defined as E/I assemblies. 

We thank the reviewer for pointing this out. E/I assemblies are groups of E and I neurons with enhanced connectivity. In other words, in E/I assemblies, connectivity is enhanced not only between subsets of E neurons, but also between these E neurons and a subset of I neurons. This is now clarified in the text: “We first selected the 25 I neurons that received the largest number of connections from the 100 E neurons of an assembly. To generate E/I assemblies, the connectivity between these two sets of neurons was then enhanced by two procedures.”. We removed “E/I assemblies” in Suppl. Fig.2, where the term was not used correctly, and apologize for the confusion.

- Suppl. Fig. 4: Could the authors please define what they mean by "Loadings" 

The loadings indicate the contribution of each neuron to each principal component, see adjusted legend of Suppl. Fig. 4: “G. Loading plot: contribution of neurons to the first two PCs of a rand and a Tuned E+I network (Figure 4D).”

- Fig. 4F: The authors might want to normalize the participation ratio by the number of neurons (see e.g. Dahmen et al., 2023 bioRxiv, "relative PR"), so the PR is bound between 0 and 1 and the dependence on N is removed. 

We thank the reviewer for the suggestion, but we prefer to use the non-normalized PR as we find it more easily interpretable (e.g. number of attractor states in Scaled networks).

- Fig. 4G&H: as mentioned in the public review, I'd add the case of Scaled I to be able to compare it to the Tuned E+I case. 

As already mentioned in the public review, we thank the reviewer for this suggestion, which we have implemented.

- Figure caption Fig. 4H "Similar results were obtained in the full-dimensional space." I suggest showing this as a supplemental panel. 

Since this only adds little information, we have chosen not to include it as a supplemental panel to avoid overloading the paper with figures.

Figure 5: 

- As mentioned in the public review, I suggest that the authors add the Scaled I case to Fig. 5 (it's shown in all figures and also in Fig. 6 again). I guess for Scaled I the separation between L and M will be very good? 

Please see our reply to the public review (reviewer 3).

- Fig. 5A&B: I am a bit confused about which neurons are drawn to calculate the Mahalanobis distance. In Fig. 5A, the schematic indicates that the vector B from which the neurons are drawn is distinct from the distribution Q. For the example of odor L, the distribution Q consists of pure odor L with odors that have little mixtures with the other odors. But the vector v for odor L seems to be drawn only from odors that have slightly higher mixtures (as shown in the schematic in Fig. 5A). Is there a reason to choose the vector v from different odors than the distribution Q? 

The distribution Q and the vector v consist of activity patterns across the same neurons in response to different odors. The reason to choose a different odor for v was to avoid having this test datapoint being included in the distribution Q. We also wanted Q to be the same for all test datapoints. 

What does "drawn from whole population" mean? Does this mean that the vectors are drawn from any neuron in pDp? If yes, then I don't understand how the authors can distinguish between different odors (L,M,O,N) on the y-axis. Or does "whole population" mean that the vector is drawn across all assemblies as shown in the schematic in Fig. 5A and the case "neurons drawn from (pseudo-) assembly" means that the authors choose only one specific assembly? In any case, the description here is a bit confusing, I think it would help the reader to clarify those terms better.  

Yes, “drawn from whole population” means that we randomly draw 80 neurons from the 4000 E neurons in pDp. The y-axis means that we use the activity patterns of these neurons evoked by one of the 4 odors (L, M, N, O) as reference. We have modified the Figure legend to clarify this: “d_M was computed based on the activity patterns of 80 E neurons drawn from the four (pseudo-) assemblies (top) or from the whole population of 4000 E neurons (bottom). Average of 50 draws.”

- Suppl Fig. 5A: In the schematic the distance is called d_E(\bar{Q},\bar{V}) while the colorbar has d_E(\bar{Q},\bar{Q}) with the Qs in different color. The green Q should be a V. 

We thank the reviewer for spotting this mistake, it is now fixed.

- Fig. 5: Could the authors comment on the fact that a random network seems to be very good in classifying patterns on it's own. Maybe in the Discussion? 

The task shown in Figure 5 is a relatively easy one, a forced-choice between four classes which are uncorrelated. In Supplementary Figure 9, we now show classification for correlated classes, which is already much harder.

Figure 6: 

- Is the correlation induced by creating mixtures like in the other Figures? Please clarify how the correlations were induced. 

We clarified this point in the Methods section: “The pixel at each vertex corresponded to one pure odor with 150 activated and 75 inhibited mitral cells (…) and the remaining pixels corresponded to mixtures. In the case of correlated pure odors (Figure 6), adjacent pure odors shared half of their activated and half of their inhibited cells.”. An explicit reference to the Methods section has also been added to the figure legend.

- Fig. 6C (right): why don't we see the clear separation in PC space as shown in Fig. 4? Is this related to the existence of correlations? Please clarify. 

Yes. The assemblies corresponding to the correlated odors X and Y overlap significantly, and therefore responses to these odors cannot be well separated, especially for Scaled networks. We added the overlap quantification in the Results section to make this clear. “These two additional assemblies had on average 16% of neurons in common due to the similarity of the odors.”

- "Furthermore, in this regime of higher pattern similarity, dM was again increased upon learning, particularly between learned odors and reference classes representing other odors (not shown)." Please show this (maybe as a supplemental figure). 

We now show the data in Supplementary Figure 9.

Discussion: 

- The authors write: "We found that transformations became more discrete map-like when amplification within assemblies was increased and precision of synaptic balance was reduced. Likewise, decreasing amplification in assemblies of Scaled networks changed transformations towards the intermediate behavior, albeit with broader firing rate distributions than in Tuned networks (not shown)." 

Where do I see the first point? I guess when I compare in Fig. 4D the case of Scaled I vs Tuned E+I, but the sentence above sounds like the authors showed this in a more step-wise way eg by changing the strength of \alpha or \beta (as defined in Fig. 1). 

Also I think if the authors want to make the point that decreasing amplification in assemblies changes transformation with a different rate distribution in scaled vs tuned networks, the authors should show it (eg adding a supplemental figure).