Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The reviewers agree that the manuscript reports an interesting and original observation in gastruloids. However there is currently no evidence to propose that such a mechanism would be present in embryos. Additionally, there is a consensus that the methods are not sufficiently explained, the reproducibility is not clearly quantified, and some claims would require a larger number of aggregates/cells to be solid.

Reviewer #3:

This is an interesting study addressing a very relevant and exciting topic. The study investigates the contribution of auditory subcortical nuclei and the cochleae using physiological recordings while listeners differentiated words in different noisy-speech conditions. It is a valuable approach to consider contiguous measures along the auditory pathway during a single behavioral measurement.

However, I have several substantial concerns with the design, conceptualization, data analysis and interpretation of the results. I have had challenges to understand the hypotheses and rationale behind this study. A number of experimental paradigms have been employed, including peripheral/brainstem physiological measure, as well as cortical auditory responses during active versus 'passive' listening. Different noise conditions were tested but it is not clear to me what rationale was behind these stimulus choices. The authors claim that "our data comparing active and passive listening conditions highlight a categorical distinction between speech manipulation, a difference between processing a single, but degraded, auditory stream (vocoded speech) and parsing a complex acoustic scene to hear out a stream from multiple competing and spectrally similarly sounds" (lines 401-403). This seems like too much of a mouthful. I cannot see that the data support this pretty broad interpretation.

Despite maintaining iso-difficulty between vocoded vs speech-in-noise (SIN) conditions, the authors neither address (a) the fundamental differences in understanding vocoded vs. SIN speech nor (b) any theoretical basis for how the noise manifests in vocoded speech. If the tasks are indeed so obviously 'categorically' different - then it should not be surprising they engage different processing (the 'denoising' may not be comparable). I would prefer much more clearly defined and targeted hypotheses and a justification of the specific stimulus and paradigm choices to test such hypotheses. It appears to me that numerous measures have been obtained (reflecting in fact very different processes along the auditory pathway) and then it has been attempted to make up some coherent conclusions from these data - but the assumptions are not clear, the data are very complex and many aspects of the discussion are speculative. To me, the most interesting element is the reversal of the MOCR behavior in the attended vs ignored conditions. However, ignoring a stimulus is not a passive task! It would have been interesting to also see cortical unattended results.

Overall, I'm struggling with this study that touches upon various concepts and paradigms (efferent feedback, active vs. passive listening, neural representation of listening effort, modeling of efferent signal processing, stream segregation, speech-in-noise coding, peripheral vs cortical representations...) where each of them in isolation already provides a number of challenges and has been discussed controversially. In my view, it would be more valuable to specify and clarify the research question and focus on those paradigms that can help verify or falsify the research hypotheses.

Reviewer #2:

This is a highly ambitious study, combining a great number of physiological measures and behavioral conditions. The stated aim is to investigate the role of the descending auditory system in (degraded) speech perception. Unfortunately, the study was not designed with a clear a priori hypothesis, but instead collected a large number of measures, which were fitted together post-hoc into a particular interpretation, based on a selective subset of the data. Even more problematically, the experimental design is based on a fundamentally flawed premise, which undermines the validity of the interpretation. A final practical problem is that the most important comparison is made between conditions that were measured in separate experiments, with different participants. Given the notoriously poor reproducibility of across studies of these measures in this research field (suggesting large inter-individual variations), this casts a serious doubt on the interpretability of the observed difference.

Specific comments:

1) A core premise of the experiment is that the non-invasive measures recorded in response to click sounds in one ear provide a direct measure of top-down modulation of responses to the speech sounds presented to the opposite ear. This is not acknowledged anywhere in the paper, and is simply not justifiable. The click and speech stimuli in the different ears will activate different frequency ranges and neural sources in the auditory pathway, as will the various noises added to the speech sounds. Furthermore, the click and speech sounds play completely different roles in the task, which makes identical top-down modulation illogical. The situation is further complicated by the fact that the clicks, speech and noise will each elicit MOCR activation in both ipsi- and contralateral ears via different crossed and uncrossed pathways, which implies different MOCR activation in the two ears.

2) The vocoded conditions were recorded from a different group of participants than the masked speech conditions. Comparing between these two, which forms the essential point in this paper, is therefore highly confounded by inter-individual differences, which we know are substantial for these measures. More generally, the high variability of results in this research field should caution any strong conclusions based on comparing just these two experiments. A more useful approach would have been to perform the exact same task in the two experiments, to examine the reproducibility.

3) The interpretation presented here is essentially incompatible with the anti-masking model for the MOCR that first started of this field of research, in which the noise response is suppressed more than the signal, which is contradictory to the findings and model presented here, which suggest no role for the MOCR in improving speech in noise perception.

4) The analysis of measures becomes increasingly selective and lacking in detail as the paper progresses: numerous 'outliers' are removed from the ABR recordings, with very uneven numbers of outliers between conditions. ABRs were averaged across conditions with no explicit justification. The statistical analysis of the ABRs is flawed as it does not compare across conditions (vocoded vs masked) but only within each condition separately (active v passive) - from which no across-condition difference can be inferred. The model simulation includes only 3 out of 9 active conditions. For the cortical responses, again only 3 conditions are discussed, with little apparent relevance.

5) The assumption that changes in non-invasive measures, which represent a selective, random, mixed and jumbled by-product of underlying physiological processes, can be linked causally to auditory function, i.e. that changes in these responses necessarily have a definable and directional functional correlate in perception, is very tenuous and needs to be treated with much more caution.

Reviewer #1:

This preprint investigates neural mechanisms for processing degraded speech, in particular regarding efferent feedback. The authors thereby study two main types of speech degradations: noise vocoded speech and speech in background noise. Efferent feedback is assessed by recording click-evoked otoacoustic emissions as well as click-evoked brainstem responses, and the measurements are taken when the degraded speech is attended as well as when it is ignored. In addition, the authors also measure cortical responses to speech onsets. They find that these measures are affected by the two types of speech degradation in very different ways. In particular, for the noise vocoded speech, the click-evoked otoacoustic emissions are reduced when the speech is attended than when it is ignored. The opposite behaviour emerges when subjects listen to speech in background noise. The authors rationalise these different mechanisms through a computational model, which, as they show, can exhibit similar properties.

Unfortunately, many of the obtained results suffer from a lack of proper controls, which renders them rather inconclusive. In addition, important details of the experimental methodology are not properly described.

1) An important aspect of assessing the efferent feedback through the CEOAEs and ABRs is to ensure that different stimuli have equal intensity. The authors write in the methodology that the speech stimuli were presented at 75 dB SPL. However, it is not stated if this applies to the speech stimuli only, such that the stimuli that include background noise would have a higher intensity, or to the net stimuli. If the intensity of the speech signals alone had been kept at 75 dB SPL while the background noise had been increased, this would render the net signal louder and influence the MOCR. In addition, it would have been better to determine the loudness of the signals according to frequency weighting of the human auditory system, especially regarding the vocoded speech, to ensure equal loudness. If that was not done, how can the authors control for differences in perceived loudness resulting from the different stimuli?

2) Many of the p-values that show statistical significance are actually near the threshold of 0.05 (such as in the paragraph lines 147-181). This is particularly concerning due to the large number of statistical tests that were carried out. The authors state in the Methods section that they used the Bonferroni correction to account for multiple comparisons. This is in principle adequate, but the authors do not detail what number of multiple comparisons they used for the correction for each of the tests. This should be spelled out, so that the correction for multiple comparisons can be properly verified.

3) Line 184-203: It is not clear what speech material is being discussed. Is it the noise vocoded speech, the speech in either type of background noise, or these data taken together?

4) Line 202-203: The authors write that "the ABR data suggest different brain mechanisms are tapped across the different speech manipulations in order to maintain iso-performance levels". It is not clear what evidence supports this conclusion. In particular, from Figure 1D, it appears plausible that the effects seen in the auditory brainstem may be entirely driven by the MOCR effect. To see this, please note that absence of statistical significance does not imply that there is no effect. In particular, although some differences between active and passive listening conditions are non-significant, this may be due to noise, which may mask significant effects. Importantly, where there are significant differences between the active and the passive scenario, they are in the same direction for the different measures (CEOAEs, Wave III, Wave V). Of course, that does not mean that nothing else might happen at the brainstem level, but the evidence for this is lacking.

5) The way the output from the computational model is analyzed appears to bias the results towards the author's preferred conclusion. In particular, the authors use the correlation between the simulated neural output for a degraded speech signal, say speech in noise, and the neural output to the speech signal in quiet with the efferent feedback activated. They then compute how this correlation changes when the degraded speech signal is processed by the computational model with or without efferent feedback. However, the way the correlation is computed clearly biases the results to favor processing by a model with efferent feedback. The result that the noise-vocoded speech has a higher correlation when processed with the efferent feedback on is therefore entirely expected, and not a revelation of the computational model. More surprising is the observation that, for speech in noise, the correlation value is larger without the efferent feedback. This could due to the scaling of loudness of the acoustic input (see point 1), but more detail is needed to pin this down. In summary, the computational model unfortunately does not allow for a meaningful conclusion.

6) The experiment on the ERPs in relation to the speech onsets is not properly controlled. In particular, the different acoustics of the considered speech signals -- speech in quiet, vocoded speech, speech in background noise -- will cause differences in excitation within the cochlea which will then affect every subsequent processing stage, from the brainstem and on to the cortex, thereby leading to different ERPs. As an example, babble noise allows for 'dip listening', while with its flat envelope speech-shaped noise does not. Analyzing differences in the ERPs with the goal of relating these to something different than the purely acoustic differences, such as to attention, would require these acoustic differences to be controlled, which is not the case in the current results.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The authors address a very important and timely research question, namely whether, and if so, how, efferent feedback contributes to the neural processing of degraded speech. However, the reviewers have identified significant problems with the experimental design and the data analysis, as well as with the conceptualization and the interpretation of the findings.

Reviewer #3:

This manuscript by Yu et al. explores the potential predictive value of Hyperpolarized 13C MRI and DCE-MRI in detecting early response of ICB. 2 mouse tumor models with different sensitivities to ICB were used in the study. Early changes in tumor glycolysis and necrosis were evaluated via [1-13C] pyruvate and [1,4-13C2] fumarate MRI, and perfusion/permeability state could be reflected by DCE-MRI. While the paper describes several intriguing pieces of data concerns below limit enthusiasm:

1) Figure 1A-C. Tumor growth curves in the anti-PD-L1 and anti-PD-L1 plus anti-CTLA4 groups appear to be steadily increasing, albeit at a slightly delayed pace than the control treated tumors. Most reports showed that PD-1/PD-L1 blockade results in tumor clearance in MC38 model, particularly when the treatment was started at small tumor sizes as presented in Figure 1A. The combination of anti-PD-L1 and anti-CTLA4 antibodies displayed more effective clearance of MC38 tumors. That is not the case here, where tumors are growing progressively throughout.

2) Figure 2A. I am surprised that CD4 T cells were barely detected in MC38 and B16 tumors. An example gating strategy must be shown, including an isotype or FMO control for each of the antibodies used.

3) Figure 3A. Given the therapeutic effect relies on the blockad of the binding between PD-1 and PD-L1, a careful assessment of the contribution of PD-1 binding to the metabolic change of tumor cells should be performed to provide clarity.

4) The microenvironment and structure of transplanted tumors are quite different from spontaneous tumor models, which are similar to human tumors. To demonstrate the clinical relevance of these findings, the authors will need to show more results in spontaneous tumor models or human tumors.

Reviewer #2:

Saida et al. performed multi-modal imaging to detect the early response to immune checkpoint blockade (ICB) therapy in murine models. This non-invasive method is attractive to monitor ICB response, thus it is valuable to discover relevant biomarkers in preclinical animal models before potential application in clinics. In ICB sensitive MC38 model, the authors identified increased cell death and intratumor perfusion/permeability, by 13C fumarate MRI and DCE MRI, respectively. While these descriptive results are interesting, this referee has a concern for the limited conceptual advance brought by this manuscript.

Major comment:

In recent years, new MRI technology has been shown to be promising to study pathophysiological changes, particularly in the metabolic field. To identify the efficacy of ICB, particularly at the early stage of treatment, is an important issue in immunotherapy. Thus the authors have chosen two murine models with a purpose to discover potential biomarkers with MRI. For metabolism, the author focused on glycolysis. In ICB sensitive MC38 model, no glycolytic changes were observed. Can the authors further clarify the role of glycolytic changes in ICB sensitive models? For instance, by using another ICB sensitive model; checking ECAR by using ex vivo digested tumor cells.

Reviewer #1:

The identification and validation of non-invasive imaging biomarkers for early response to cancer immunotherapy is a research hotspot. Dr. Krishna and colleagues proposed a potential combination of [1-13C] pyruvate-based detection of glycolysis, [1,4-13C2] fumarate-based analysis of necrosis, and Gd-DTPA-based quantification of perfusion/permeability with MRI technologies. To make the conclusions more convincing, some major issues should be carefully addressed.

1) It is a bit unfair to compare two different tumor models (MC38 colon cancer versus B16 melanoma). Reasonable solutions can be: 1) to compare good responders versus bad responders in the same type of cancer; 2) to compare ICB resilient tumor cell clones versus ICB sensitive clones, which originate from the same parental cell lines. To test whether these potential biomarkers can be generalized to multiple cancer types. Several tumor models should be tested.

2) It seems that the authors didn't test these parameters at different time points. As delayed response can be frequently observed in ICB, it is recommended to monitor tumor-bearing mice at different time points. These recorded parameters can be correlated to the therapeutic outcomes, once the whole tumor growth kinetics is finalized.

3) It is not accurate to consider the area of necrosis as the equivalent of immunogenic cell death.

4) Were any of these findings validated in a small cohort of cancer patients?

5) With radioactive probe-based analysis of glycolysis, it is difficult to judge whether metabolic changes were from tumor cells or from tumor-infiltrating immune cells. Ex vivo seahorse-based analyses of ECAR and OCR do not resemble in situ metabolic status of tumor cell.

6) Once glycolysis is reduced, OXPHOS and fatty acid oxidation may be switched on. A systemic analysis of the metabolic programs may be necessary. Mechanistic explorations on why these parameters correlate with late therapeutic outcomes is weak.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

A major concern is that the two transplantable murine tumor models used in this study may not be appropriate: it is odd to compare the therapeutic efficacy of ICB in colon cancer versus that in melanoma; the responsiveness of MC38 tumors seem to be much less than a series of reports; the composition of immune cells in the tumor microenvironment seems to be a bit abnormal; and the reviewers also have concerns on whether these transplantable tumor models can mimic human cancer patients.

Reviewer #3:

The manuscript by Gann et al., investigates whether theta-burst TMS stimulation (TBS) of the DLPFC can alter hippocampal and striatal activity during a sequence-learning task (SRTT). Across two experiments, the authors provide a well-powered investigation of this question using MRS and fMRI. The first experiment describes a nice approach for selecting an anatomically accurate brain region, whilst the second experiment uses a robust 4-session within-subject design. The study is clearly written and has some very interesting results, with the authors concluding that it provides the first experimental evidence that brain stimulation can alter motor learning-related functional responses in the striatum and hippocampus. As described below, I believe the interpretation of these results is overstated and would be better framed in the context of the other changes across the brain (it was not a specific effect between DLPFC and hippocampus/striatum) and also several clear negative effects (behaviour, MRS, fMRI).

1) Interpretation of the results given the lack of a behavioural effect: I do appreciate the authors discussion of this, however the lack of a behavioural effect makes me wonder whether the imaging results are over interpreted. Generally, I found the negative results (behaviour, MRS, aspects of connectivity) to be understated and the positive results to be overstated, even though the positive results, linking DLPFC stimulation to changes in striatum and hippocampus, required a far more nuanced analysis of the data (Figure 6). The results seem to suggest that TBS has a general (and somewhat inconsistent) effect on connectivity across the brain rather than a specific effect on DLPFC-hippocampus/striatum connectivity. Given these issues, I believe a more cautious interpretation of the results are required in which it is not concluded multiple times that DLPFC brain stimulation can alter motor learning-related functional responses in the striatum and hippocampus without making clear this was in the context of other changes across the brain and also several clear negative effects. The manuscript would be improved if a more balanced picture were provided throughout.

2) Use of iTBS vs cTBS: By using these TMS conditions, we do not know what the normal brain activation pattern is for the sequence task. Although the authors have provided a good attempt at trying to interpret these results, as a reader it was difficult to comprehend the somewhat inconsistent results across the two TMS conditions. The manuscript would have benefited from a sham/null TMS condition.

3) Consistency of results for experiment 1: Although this experiment provides a nice mechanism to determine TMS location, the details of these results need to be more substantial. In particular, for the conjunction analysis, the reader needs to understand how consistent this effect (Figure 1B) was across participants. Does every participant show this conjunction map or what percentage of participants show this map? This feels like an important thing to report, and then possibly base a power analysis on for Experiment 2 i.e. how many participants do we expect to see the predicted TMS results given the % of participants who show this conjunction map?

4) Clarity of results for experiment 2: I found it difficult to follow the results for experiment 2, especially from page 17. I appreciate the authors refer to the methods but I think a little more explanation of the methodology within the results is warranted. In addition, it got pretty difficult to follow the results relating task (seq vs random), stimulation (iTBS vs cTBS) and their interaction. Maybe more informative sub-titles would help?

5) Interpretation of BOLD activity: Given recent work (https://elifesciences.org/articles/55241 ) could the authors discuss what increases and decreases in BOLD activity represent within a learning context? Is a decrease or increase beneficial?

-Why do the authors keep using the term 'proof of concept'?

-Figure 7B: which line is cTBS and iTBS?

Reviewer #2:

Gann and colleagues report the effect of iTBS and cTBS of DLPFC on GABA+, BOLD-activity, and functional connectivity during sequence learning (SRTT). Despite finding no difference between the brain stimulation conditions on behavioral performance, the authors report widespread differences in BOLD-activity and functional connectivity between intermittent and continuous TBS. The key result (reported in Figure 6), is a complex difference between the stimulation conditions and the GABA+ change in DLPFC with i) the learning-related activity in hippocampus and ii) the learning-related changes in functional connectivity between DLPFC and putamen. The authors affirm that these results are important, as they are the first to show an interaction between DLPFC stimulation, learning-related changes in MRS, and BOLD-activity change in the hippocampus and striatum.

The authors have undertaken a mammoth effort in running this study. The targeted brain stimulation appears to have been conducted in an exemplary fashion, and the integration of multiple MR modalities is impressive. Nonetheless, I feel that the lack of a control group in the study design is a major concern and makes interpreting the study's results challenging. In addition, I have several reservations regarding the analysis that should be addressed before this work is suitable for publication.

General comments:

1) This study does not include a control group, and all conclusions are drawn based on the comparison between inhibitory and excitatory TBS protocols. A control condition is necessary to put the difference between the i/cTBS differences in perspective. Without this perspective, it is challenging to interpret the directionality and magnitude of the effects reported in this study.

2) The authors stress that the major contribution of this work is revealing the effects of DLPFC stimulation on fMRI/MRS signals during/after learning (e.g., Abstract: line 43-45; Introduction: lines 102-104; Discussion: lines 498-500, 741-743). As it is written, this work is primarily interesting to the brain stimulation community. The article would be of substantially broader interest if the authors discussed their results with respect to the contribution of DLPFC to sequence learning, rather than as an exploratory investigation into the effect of brain stimulation.

Methodological/Analytical comments:

3) The small volume correction analysis and reporting has several issues. Throughout the results, the authors report analyses plotted on the whole brain, and do not make reference to any small volume correction being used (except for the results reported in Table 2). However, in the methods section, the authors report that analyses were conducted using small volume corrections (10mm spheres drawn around the points reported in Supplementary table 7). There are several problems here.

i) Most importantly, the authors use (by my count) 87 separate small volumes, and reconstructing the spheres from the coordinates in Supplemental table 7 shows that this mask covers a substantial portion of the brain. This seems highly unusual to me. However, it is not clear whether all of these small volumes were considered together, or whether they were each considered as an independent volume. In either case, the authors should report whether any of their results survive whole brain correction. Additionally, if the authors tested 87 regions independently, multiple corrections should be applied to account for all regions tested (0.05/87 = 0.00057 for the new FWE-corrected p-threshold). Alternatively, if the authors used this single mask for correction, they should provide a justification for using an analytical mask restricted in this way, which, again, seems highly unusual.

ii) In the main text and figures, the authors should note when small volume correction is being applied.

iii) In the whole brain figures, it should be made clear what voxels were considered for the analysis (e.g., by shading the brain that was outside the small volume).

4) The authors appear to have done two instances of spatial smoothing (8mm before fitting the GLM (line 1184), and 6mm on the resulting statistical map (line 1224)). Again, this seems highly unusual, and given that the majority of results are conducted within small volumes, it seems smoothing to this extent would introduce unwanted levels of spatial blurring. The authors should report the total smoothness of the image for all subjects (AFNI's 3dFWHMx can do this) and consider performing the group analyses without additional smoothing applied to the statistical maps.

5) Although Study 1 is obviously important to the manuscript, I think it is perhaps overstated and makes the present work difficult to parse. Specifically, it does not seem to be important for interpreting the effects of the stimulation during learning; rather, Study 1 is a means to localize a brain stimulation target (i.e., a methodological point). Further, in the methods section, the authors reveal that they constrained their search for a conjunctive target (connected to both Hippocampus and Striatum) to the superior frontal gyrus and middle frontal gyrus. Thus, the authors seemed to have "found what they were looking for", because they restricted their search to a fairly well circumscribed region before running this study. Taken together, the authors might consider moving these details entirely to the Methods section, and removing Study 1 and associated figure from the main text.

6) Are there any relationships between Glx levels and fMRI effects?

Reviewer #1:

This is a very ambitious and interesting study that uses a state-of-the art combination of multiple methods to provide new insights into functional network interactions during motor learning. However, I have several major concerns against the design and analyses that may have contributed to the overall very weak effects that are reported (mainly null effects in standard measures at the behavioural and neural network level). I also think that some of the conclusions are not justified given the partly non-significant and overall weak effects.

1) My main concern is that no baseline stimulation condition (sham TBS) was included. The authors address this in the discussion but I cannot agree with their argumentation. Without a baseline, it is impossible to assess whether each stimulation protocol had a significant impact on the outcome measures. For instance, it would be plausible that both protocols had opposite effects (which is also hypothesized by the authors) which were, however, only slightly or not significant from baseline. If cTBS slightly decreases connectivity and iTBS slightly increases it, this could result in a difference between both protocols that might not be observed when contrasting each protocol against baseline. Put differently, how do we know that these changes are meaningful and significantly different from zero (baseline)? I think this is especially important in the present study since the overall effects are weak and there is no significant modulation of behavior - so the functional / behavioral relevance of the observed modulation remains unclear. I think that without the inclusion of a baseline (sham), it is very hard to interpret the data.

2) Another main concern is that the reported effects are very weak and not properly corrected for multiple comparisons. I don't think that it is justified to apply small volume corrections for large-scale network effects and it seems that some of the results are at threshold. Given the weak effects in these analyses, in combination with the absence of any modulation in the "standard" analyses (fMRI, connectivity, behaviour, MRS only significant in exploratory post-hoc tests which are not well justified), I am not sure if the reported results are really reflecting any stimulation-induced modulations at all or mainly show some noise added by the TMS protocols. This of course affects the conclusions that can be drawn from the study.

3) There are a number of issues with the design that might have contributed to the weak findings. These include data loss (e.g. no MRS data for the hippocampal voxel) and somehow arbitrary sample sizes that are not well justified. I am also not sure why cortical excitability measures (MEPs) were performed after TBS because this is of minor importance and delayed the start of the fMRI sessions. Given that TBS effects are expected to decrease over time, I am not sure if this was necessary. Was the potential change of the TBS effects across session taken into account (e.g., by using a parametric modulation of the TMS effect)?

4) Given the overall weak effects the conclusions should be toned down. The discussion would further benefit from including additional work that demonstrated changes in remote subcortical regions and effective connectivity after TMS over a frontal area (e.g. Herz et al., J Neurosci 2014).

5) There is no modulatory effect of TBS on behaviour, which is surprising in light of previous neurostimulation studies on motor learning. I think the way this is sold in the discussion is a bit odd. I guess that initially, one would have expected a behavioural modulation that should ideally be correlated with any TBS induced changes in functional connectivity (or with the MRS data). If not, how would you be able to claim behavioural relevance? In the discussion, the absence of a behavioural modulation is sold as an advantage, I think this is not justified and should be toned down. Moreover, since the authors speculate about potential influences of TBS on motor consolidation, I was wondering if consolidation was assessed (which seems to be a relevant parameter here)?

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The main concerns with the study were three-fold. First, the absence of a control group makes it hard to draw conclusions about the effects of inhibitory and excitatory TBS protocols separately, limiting the appeal of the study. Secondly, the control for multiple statistical tests is not adequate - conducting 87 independent "small volume corrected" tests will lead to an inflated family-wise error rate. Finally, all reviewers were unanimous in judging the effects to be somewhat interesting, but rather weak - with the absence of an effect on behaviour and simpler standard fMRI and connectivity measures being as remarkable as the positive effects reported.

Reviewer #3:

Short-summary:

Children (wide range) and adults participated in 3 MEG-experiments with auditory oddball paradigms varying in task demands. The focus is on the child N250m. Results show that although the N250m was not attenuated by task differences, increased activation in the left hemisphere (for at least the standard stimulus in the gng-task) was associated with better performances in inhibition tasks. Since the N250m in children was mainly located in the temporal cortices, whereas activation in adults was present in other areas, notable the ACG, this suggests that children differ from adults in the mechanisms required for cognitive control, and rely longer on sensori-motor areas.

Positive: well-written, great pictures.

Major comments:

1) The proposed link between auditory skills and inhibition is poorly explained and requires more elaboration. They want to relate auditory processing to " cognitive skills" (line 22, 77). Yet cognitive skills are a broad construct, encompassing many skills and abilities, including for instance reading, but also executive functions, which includes inhibition (Miyake et al., 2000) . Actually why zoom in on inhibition? Is it as one of the three components of executive function (Miyake et al., 2000) or is it viewed as part of self-regulation (Nigg, 2017)? You refer to cognitive control (46/47)- which suggests the latter explanation - but this remains unclear. It would help the reader to use consistent terminology (e.g., inhibition, cognitive control, executive control, inhibitory control are used now), or to highlight the links between the related concepts. Moreover, there are many paradigms to test inhibition, why did you chose the one you chose (Littman & Takacs, 2017)? And you also examine the behavioral performance sin the inhibition-MEG task (line 303)? Why the additional focus on attention in the results?

2) Your summary of the two child components (N1m and N250m) predicts different findings with the relationships with inhibition. That is, the link between the child N1m and inhibition should be smaller/non-existent, while it is mainly in the N250m that you expect it. While your results prove evidence towards the latter, your analyses do not concern the first component. It would be stronger if you do.

3) The logic of having three different auditory-listening tasks, and one behavioral outcome measure was not entirely clear to me. It seems that the paper is addressing various aims (e.g., replicate earlier work showing that the N250m is unaffected by task parameters in children while it is only present in adults for active tasks; another is linking the N250 m across all three tasks, or only for one of the three, if so, which? related to inhibition, but only for children, or also adults?) it would help to be explicit about this. For instance, there is an MEG-inhibition task and a behavioral task. Were you going to relate performances to both?

4) Why is age a significant predictor in explaining SSRT performance when adding left hemisphere OB-deviant, but not when adding LH GNG-S? Moreover, isn't it surprising that increase in activation yields better SSRT scores when this component disappears in adults?

5) From an association one cannot infer causal relationships - such limitations need to be discussed in more detail. Results do not allow for concluding that a sustained response ' aid inhibitory performance' (line 624).

Reviewer #2:

In this study the authors sought to explore the relationship between a child-specific auditory evoked response (N250) and cognitive control, using a classic auditory oddball paradigm. Here the cognitive control was manipulated by varying the tasks that participants were instructed to do while listening to the oddball tone sequence: (a) ignore all sounds ("passive listening"), (b) respond to the standard tones ("go/no-go") and respond to the deviant tone (which was called "oddball task" in this study).

Using the combined MEG and EEG as well as MRI, they reported an association between the strength of N250 in the left hemisphere and the behavioural performance in the go/no-go task and a separate inhibition task. Based on this observation as well as the fact that N250 was only visually observed in the children's brain response, the authors claimed that when doing sound involved cognitive tasks, different neural mechanisms were employed by adults and children. Considering the difficulty in operating a MEG and EEG combined experiment on children (6-14 years), the large sample size (n=78) is very, very impressive and the task was carefully embedded in a children-friendly game, which showed that the authors did a lot of work for this project.

However, it is hard to generalise such a conclusion based on the current paradigm and the results reported here. I also found it's a bit hard to follow the logic in the original manuscript, not because of the language but I think it might need more thorough revision to better explain what exactly the authors hypothesize, why use this specific paradigm, and why analyse the data in these ways.

Major comments:

1) While the task "press a button to standard tone" is called go/no-go task, the task "press a button to deviant tone" is called an oddball task. Why is the latter not a go/no-go task? It's definitely ok to have different names for different blocks, and also to analyse the data in these two blocks separately to double check. However, I would not expect fundamental difference in these two blocks. (However, as mentioned later, the authors reported divergence between these two tasks).

2) The main finding "Left hemisphere auditory responses at 250ms predicts behavioural performance on inhibition tasks" was based on the observation that, the brain activity in the left hemisphere (independent of the task) was negatively correlated with the within-individual variance in RT and the error rate in the go/no-go task (where subjects were instructed to respond to the standard tones) and the reaction time in a separate inhibition task done outside of the scanner. Why smaller within-individual variance in RT means better performance? Someone could be consistently very slow and this should not be a better performer. I found this is confusing, especially that based on Table 3, there was no correlation between RT and the brain response strength.

3) The scatterplots in Figure 7 shows the correlation reported in Table 3. However, the correlation seems to be largely driven by a few outliers: about 5 subjects whose source amplitude was much more negative than the rest of the population. Why did these subjects have a particularly strong source amplitude? After excluding these five subjects' data, will the correlation remain significant?

4) This point is related to points (1) and (2). In table 3, left hemisphere response during passive listening was strongly correlated with ICV, ERR and SSRT, but in table 6, there were no more correlations for passive listening. Can the authors explain why there is a difference between two passive listening sessions which in theory should be the same? Again, if there is no difference between "press a button to standard tone" and "press a button to deviant tone" and the correlation observed in table 3 was robust, then we would expect to see the significant correlations in table 6 for ICV, ERR too, but it is not true. These together make the finding less convincing. If there is any misunderstanding, the authors still need to justify these clearly in the manuscript and further analysis would be helpful.

5) Interpretation of the result: Even if the association between the amplitude of N250 and the behavioural performance is proven robust and true, this doesn't mean that this activity "aid the inhibitory performance in children" (line 624). Correlation does not imply causation. The authors need to provide more direct evidence to support such a claim or consider re-wording.

6) Design of the task: a. The block order: Why was the task order fixed for all participants? b. It is unclear why the passive listening block has a different number of trials (300) compared to the other two active blocks (360).

7) Sample size: Although the large sample size used in this study is very impressive, it is unclear how this sample size was determined and why the sample size of two groups (children vs adults) was so different (children n=78, adults n=16). It is crucial to justify this difference in this study because the motivation of this study is based on the hypothesis that N250 is present in children but not in the adult.

8) The unequal number of samples in statistical analysis: Related to the last two points, it is unclear whether the number of trials/participants was equalised before running the statistical analysis in this study.

9) Handedness: As the authors themselves mentioned in the discussion, the effect in left hemisphere observed here could be related to the handedness. Then the authors should also report the handedness amongst the participants.

10) Analysis: It is generally unclear why the children's data were divided into two groups: above or below 10 years old. The authors need to explain their rationale behind this clearly before doing so.

11) Figure 3: Each sub-figure includes 6 different conditions and makes it very hard to visualise. Please consider plotting the results in pairs for comparison, also show error-bar and run proper time-series statistics on the result. Also, it is unclear which channels are selected based on the black and white cap image at the centre. Please visualise it differently, for example, colours.

Reviewer #1:

This study by van Bijnen et al. used MEG/EEG recordings to examine the behavioral relevance of auditory processing in children, with a specific focus on an auditory cortical component around 250 ms, which only occurs in children but not in adults. They demonstrate that this component, particularly in the left auditory regions, covaries with several behavioral measurements in children. They conclude that the results suggest a shift in cognitive control function from sensorimotor regions in children to prefrontal involvements in adults.

The study addresses an important question in both auditory neuroscience and developmental science and is carefully performed. The modified design for children is interesting. However, I am not quite convinced that the findings constitute a great breakthrough. Moreover, I have major concerns about the correlation analysis that would support the central claim in the paper, that is, the attentional inhibition relevance of the M250 component in the left auditory cortex.

Major:

1) The child-specific M250 component occurring in the auditory cortex is interesting, but as mentioned throughout the paper, this is a well established observation. This study provides some evidence for the behavioral correlates of the component, but I am not convinced that the correlations supports the unique function of the component in attentional inhibition and its development trajectory from children to adults. First, the author only focused on the M250 component and calculated its correlation to behavior and thus could not exclude that other components might also be involved in the process. I would suggest the authors to do the correlation throughout the time course to thoroughly seek the behavioral-related components. Second, even for the passive listening conditions when inhibition is not required, the M250 also correlated with some behavioral measurements in certain task (Table 3) ? Third, only the to-be-inhibited sound was analyzed so how could the results support that the component only correlates with attentional inhibition? I understand that the authors might want to avoid the motor confounding factors associated with attended sound, but without comparison or control analysis, the conclusion could not firmly hold. Finally, behavioral relevance analysis was only done on children but not adults.

2) The authors calculated correlations between the M250 component with a series of behavioral measurements. Is there any way to do multiple comparison correction? Moreover, the results are inconsistent across different comparisons (e.g., Table 3, Table 6). For example, several behavioral indexes correlated with neural component for both PL and GN conditions (Table 3) while only SSRT showed correlation with the component under OB condition. I would suggest a more fair analysis by performing a GLM analysis using all the behavioral measurements (not just select factors that showed significant partial correlation which I think is double dipping to some extent, e.g., table 4, 7) as predictors.

3) To support the developmental trajectory of the M250 component, the authors could also perform the behavioral correlation for adults and compare it to that for children, even the behavioral-relevant component might be different in time and occur in distinct brain regions.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

All the reviewers acknowledged the importance of the question the paper aims to address, the big sample size, and the interesting experimental design for children. The paper is also clear and well written. However, the reviewers raised several critical concerns that question the main conclusions, including the interpretation of the results (i.e., relation to inhibition in cognitive control), inconsistency across experiments (i.e., differences in the results between the two experiments), and analysis details (i.e., behavioral-neural correlations). The paper could also be improved by a reframing in which the hypotheses and rationale behind the experiments are better explained.

Reviewer #3:

Summary:

The authors evaluate functional implications of two B9D2 missense variants identified in an individual with Joubert syndrome, by engineering the variants into a C. elegans model system. Few studies have evaluated the functional consequences of patient variants in model systems (rather than null alleles). Overall, the experiments are elegant and rigorous. The functional defects evaluated include decreased and altered localization of the variant proteins at the TZ, altered TZ function, altered cilium function (dye filling and behavioral assays), and reduced TZ protein localization, especially for TMEM216. The functional effects of homozygous null, homozygous missense variants, and compound heterozygous missense variants are compared. While most of the conclusions are well-supported, the work does not connect the functional consequences in C. elegans to phenotypic severity in humans, a critical validation of methods to test pathogenicity of human variants.

Major comment:

The authors introduce the concept of using C. elegans for genotype-phenotype correlations in the Abstract and Introduction, but do not interrogate an allelic series from humans with more and less severe phenotypes. The claims of genotype-phenotype correlation could be de-emphasized (eliminated? restricted to C. elegans), or the work could be strengthened by including more of an allelic series including variants predicted to be more deleterious (p.Ser101Arg identified in families segregating a Meckel syndrome phenotype. and p.His5Gln identified in a family segregating a possible Meckel syndrome phenotype), less deleterious (the p.Leu36Pro variant in a possibly less severely affected person with JBTS, also published in the Bachmann-Gagescu paper), and benign (i.e. common variants that are found homozygous in population databases like gnomAD and are unlikely to impair B9D2 function). It seems that this would be a lot of additional work; however, the Discussion highlights "it should be possible to generate hundreds of alleles in a relatively short time frame at relatively low cost and manpower compared to other multicellular systems. The workflow to generate and characterize ciliopathy associated variants described here can also be extended to other conserved cilia genes and ciliopathies."

Other comments:

1) Important considerations for data presentation and statistical analysis:

-Use dot (or violin) plots rather than bar graphs to show data structure for length, intensity, and other measurements (see PMID 32346721). For the curves of linescan intensities, it would be helpful to include supplemental figures with all of individual curves to see their shapes and variability.

-t-tests on all data points together may over estimate statistical significance; consider whether it would be more appropriate to compare mean measurements for each animal (or median if the data are not normally distributed). At a minimum, list the number of cilia and the number of animals for each experiment.

2) Could the lower levels of mutant protein in the TZ be due to lower levels of total mutant protein? Although there is no MKSR-2 antibody, this could be evaluated by Western blots of mNG::MKSR-2/mNG::MKSR-2(P74S) and mNG::MKSR-2/mNG::MKSR-2(G155S) animals.

Reviewer #2:

In this manuscript, the authors analyzed the function of two pathogenic missense variants (P74S, G155S) of Joubert Syndrome protein B9D2/ mksr-2 using a C. elegans model. The data shows that both P74S and G155S mutations change the distribution of MKSR-2 on TZ and disrupt the structure and function of cilia in C. elegans, indicating that both mutations are pathogenic.

Characterizing the function of pathogenic mutations associated with ciliopathies is important for us to understand the function of ciliopathy genes and the pathogenesis of ciliopathies, therefore, the topic of the manuscript is very important and interesting.

The manuscript is well organized, and the data is of high experimental quality. However, there is a lack of new insights about the function of MKSR-2 protein or the formation of TZ.

Major concerns:

What are the possible mechanisms by which P74S and G155S mutations affect the function of MKSR-2? Do these mutations affect the interaction between MKSR-2 with other TZ proteins? I do think some (even a little) new insights into the function of MKSR-2 are needed.

Reviewer #1:

The experiments are elegant, take advantage of the strengths of the model and the conclusions are mostly supported by the results, even if the discussion should address potential limitations a little more. Overall, this is thorough work of potential high impact.

Major comments:

1) The authors test the localization of the mutant B9D2 protein at the base of the cilium, show decreased fluorescent signal and conclude that the patient mutations affect the TZ localization of the protein. It seems important to me to also demonstrate that the overall protein stability is not affected by measuring the protein levels by western blot if possible. The competition assay between wildtype and mutant alleles with and without transgene somewhat supports the presence of product from the mutant alleles, but an objective measure of the amount would further strengthen their point. (One could imagine that the G155S mutation leads to decreased protein stability with increased degradation and this may explain why it is more similar to the knock-out than the P74S allele?).

2) One major claim made by the authors is that the experiments allow to classify the severity of the effect caused by the individual mutations, showing that the G155S is more severe than P74S. What I find puzzling, is that the ultrastructural consequences on the TZ appear to be similar in both mutants, whereas the TZ gating function is affected only in the G155S mutant. How do the authors explain this discrepancy? If the morphology of the gate is affected similarly, why is the function not affected similarly? Maybe some quantification of the ultrastructural defects would show that the ZT is more disrupted in the G155S mutant?

3) A more detailed discussion of the differences between C.elegans and mammalian cilia appears necessary to me, since these difference may prove to limit the applicability of the proposed assays (for example differences in the basal body of C.elegans may limit this approach for basal body resident proteins? Even for the TZ, in humans mutations in only on TZ component cause phenotypes, while in worms, double mutants are necessary for most genes, suggesting differences in the function of the individual proteins or the structure of the TZ). Beyond the species differences, evidence is appearing for cell-type specific roles of ciliary proteins, so that results from one type of cilium (including those shown here in worms), do not necessarily guarantee that this holds true in all cilia types, which would limit the interpretation for patients with many different cilia types. This being said, I still support the relevance of the current work, but just think that these potential limitations should be mentioned in the discussion in a more detailed manner.

4) Figure 2D: the curve for the P74S mutant overlays with the WT curve with respect to height (fluorescence intensity) and length (x-axis). Does this not contradict panels A-C where the signal is weaker and shorter?

5) Figure 6C: my impression from the graphs is that nphp4 and cep290 are just as much affected as mks14 and mks6 in both P74S and G155S mutants? The text does not mention that mksr2 mutants have any effect on nphp4, cep290 or mks5 whereas the graphs do show a mild effect? Wouldn't this contradict the model of how the TZ is built? Figure 6D again seems to show a different result than Figure 6C (mainly for mks6)?

6) Statistics: correction for multiple testing should be performed everywhere (no pair-wise t-tests).

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The manuscript by Lange et al describes how C. elegans can be used to generate functional assays to interpret the significance of missense variants in known human ciliopathy genes. This work thus aims at being a proof-of-principle for a way to address the major problem of VUSs (variants of unknown significance) faced by human geneticists today and is therefore of high relevance to the field (even if no major novel biological insights with respect to ciliary biology are described). The reviewers agreed that characterizing the function of pathogenic mutations associated with ciliopathies is important for us to understand the function of ciliopathy genes and the pathogenesis of ciliopathies. The manuscript is well organized and the data are of high experimental quality.

Author Response:

All three reviewers agreed that establishing a link between a proteasome activator and heterochromatin stability was novel and intriguing. However, limited insight into the PA28-gamma mechanism of action (or possibly a new heterochromatin compaction mechanism) dampened reviewer enthusiasm. The reviewers offered many suggestions, including additional experiments, new controls, and structural changes to the Discussion, that we hope you find useful.

We would like to thank the reviewers for their suggestions and comments, which we will take into account to improve our manuscript as much as possible. As stressed by reviewers, our manuscript highlights a new and unexpected function of a proteasome regulator, PA28γ, in the regulation of heterochromatin compaction. We also provide evidences that this unexpected function of PA28γ is independent of its proteasome regulatory function. Moreover, we can show that PA28γ is required at least for proper maintenance of heterochromatin regions dependent on HP1 proteins, thereby providing a clear insight into the PA28γ mechanism of action on chromatin.

Reviewer #1:

In the manuscript entitled, "The 20S proteasome activator PA28γ controls the compaction of chromatin," Fesquet et al. establish a functional link between PA28γ and chromatin compaction in human cells. Previous work established a role for PA28γ in DNA repair and in chromosome stability through mitotic checkpoint regulation; however, a role, if any, for PA28γ in heterochromatin establishment/maintenance was not known. The authors use an elegant LacO-GFP system combined with PA28γ knockdown to support the possibility that this nuclear activator contributes to DNA packaging of repetitive DNA. A nucleosome proximity assay offers additional support that the most compacted chromatin is most sensitive to loss of PA28γ. Using a truncated version of PA28γ, the authors show that this chromatin function appears to be independent of its interaction with the 20S proteasome. ChIP-qPCR suggests that PA28γ binds repetitive DNA and ChIP-qPCR of PA28γ knockdown cells lose H3K9me and H4K20me, two silent heterochromatin marks. In addition to these data, the authors also attempt to establish that PA28γ and HP1β may work together to support heterochromatin formation/maintenance. The manuscript reports several intriguing pieces of data that have the potential to open new areas of inquiry into proteasome components and accessory factors in chromatin organization and remodeling. The potency of these key experiments, however, were diluted by unconvincing co-localization assays, poorly controlled PLA and ChIP-qPCR assays, and a highly speculative Discussion. Moreover, key controls were missing for several experiments (detailed below) that would have otherwise established the heterochromatin-specificity of PA28γ. Finally, important potential functional consequences of heterochromatin disruption, including chromosome segregation defects, transposable element proliferation, and accumulation of DNA damage, were not addressed while there was a focus instead on cell cycle without clear interpretations.

Major Comments:

1) Figure 2: The co-localization experiments were unconvincing - HP1β and PA28γ foci decorate most of the nucleus, making inferences about significant overlap difficult to grasp.

We fully agree with this criticism for Fig. 2A, in which classical indirect immunofluorescence (IF) and widefield microscopy were used. This is why in Fig. 2B, we set up a pre-extraction protocol of cells with a Triton X100 treatment, to remove almost all soluble proteins before cells fixation and IF. Then images were acquired as Z-stacks with an Airyscan confocal microscope, followed by a 3D reconstruction and analysis of the co-localization between PA28γ and PA28γ using Imaris co-localization software. This experiment highlighted that only a fraction of both endogenous proteins co-localize in the nucleus. Furthermore, we noted that the number of co-localization sites evidenced in Fig 2B (~32) was in the same range than the number of dots (~37) detected by another approach (is-PLA), suggesting that we can be confident with these results.

I also found the significance of the PLA assays difficult to discern. When both factors are so abundant in the nucleus, it seems inevitable to observe loss of proximity when one 'partner' is depleted. How do these data demonstrate the specificity of this potential proximity? A clearer explanation would be helpful.

PLA technique imposes numerous constraints to obtain a signal (i.e. distance less than 30-40 nm between the two epitopes, formation of a closed circular DNA template). As a control, we verified that the is-PLA approach gives specific signals between PA28γ and the 20S proteasome. Like PA28γ, the 20S proteasome is very abundant in the nucleus but only a small fraction of PA28γ interacts with the 20S proteasome by Co-IP (Jonik-Nowak, 2018). Consistent with this, less than 60 distinct PLA spots were detected in the nucleus between PA28γ and the 20S proteasome rather than a global nuclear PLA labeling suggesting that it is probably not the abundance of each protein tested that is responsible for PLA signal but rather, as suggested by this kind of techniques, their ability to interact.

Note that the PIP30 data were a distraction from the main thread - I recommend removing or explaining more clearly.

PIP30 is currently the only known regulator of PA28γ, for which we have previously shown a critical role in PA28γ interaction with different partners and localization (Jonik-Nowak, 2018). This is why we examined the potential requirement of PIP30 in this new chromatin regulatory function of PA28γ.

2) The ChIP-qPCR data were certainly exciting but the absence of a negative control locus made me wonder how specific this result was to DNA repeats.

As a control, we already used cyclin E2 promoter in our ChIP-qPCR for PA28γ. This led us to show that the detection of PPA28γ on heterochromatic repetitive DNA sequences is enriched by a factor of 2-3 as compared to this euchromatic loci bound by PA28γ. In a modified version of this manuscript, we will add other control loci located in euchromatin. We will also test these new loci as negative controls in ChIP-qPCR for H3K9me3 and H4K20me3.

3) The LacO-GFP data are really cool. Why didn't the authors not attempt to rescue compaction with a PA28γ transgene as was done for the FLIM-FRET?

Since, we could not obtain stable U20S-LacO-KO-PA28γ and -KO/KI-PA28γ cell lines, we decided to analyze the impact of PA28γ absence, using siRNA approaches. As it was shown that overexpression of PA28γ is sufficient to cause a disruption of Cajal Bodies (Cioce et al., 2006) and a decrease in the number of PML bodies (Zannini et al., 2009), and we also noticed in FRET-FLIM experiments that PA28γ expression level is critical for chromatin compaction, it is difficult to consider to overexpress a RNAi-resistant PA28γ protein in order to rescue the effect of the depleted endogenous protein.

4) Cell cycle data would be much more interesting if the authors set up a priori predictions based on Figures 1-5.

We agree with the comment, and we will correct it in the modified version of the manuscript.

5) The absence of any report of PA28γ KD/KO on genome instability was surprising.

As indicated in the manuscript, the potential effect of PA28γ depletion on genome stability has already been reported in the literature showing an increase in chromosomal instability (Zannini, 2008).

Loss of heterochromatin integrity is expected to compromise chromosome transmission/transposable element expression or insertions. Do the repeats to which PA28γ localizes upregulate upon PA28γ KD or KO? Does DNA damage signaling increase at the loci? These functional consequences would be rather more explicable that the S-phase result reported.

We did not detect any upregulation at these specific loci by RT-qPCR experiment using KO-PA28γ U2OS cells. Concerning the potential accumulation of DNA damage signaling at these loci in the absence of PA28γ, we have not studied this aspect because PA28γ depletion was reported to induce only a marked delay in DSB repair and not a DNA damage accumulation (Levy-Barda, 2011).

6) The histone mark ChIP-qPCR, like the PA28γ ChIP-qPCR, lacks a negative control locus/loci, again undermining the inference of specificity of PA28γ on heterochromatin.

We agree and these different control loci would be added in the modified version.

7) The LLPS paragraph in the discussion was weak - consider removing.

Yes, potentially. To be defined in the context of the modified version.

8) The speculation of 20S into foci does not add and, to my mind, detracts from the focus of the Discussion.

In the modified version of the manuscript, we will focus our study on endogenous proteins and therefore this aspect of the discussion concerning the 20S proteasome, and related to the overexpression of alpha4, will no longer be discussed.

Reviewer #2:

In this manuscript, Fesquet and colleagues describe an important role of the proteasome activator PA28-gamma in the compaction of chromatin. The authors first demonstrate that PA28-gamma colocalizes HP1-beta at nuclear foci induced by the ectopic expression of alpha-4 subunit of the 20S proteasome. They further show that a fraction of PA28-gamma colocalizes also with HP1-beta in cells without ectopic expression of the alpha-4. The authors then show that PA28-gamma is associated with heterochromatic regions and is required for the compaction of lacO array integrated at a pericentromeric region. They also performed the quantitative FLIM-FRET and demonstrate that PA28-gamma controls chromatin compaction in living cells, independently of its interaction with 20S proteasome. Finally, the authors show that PA29-gamma depletion leads to a decrease of heterochromatin marks, H3K9me3 and H4K20me3, at representative heterochromatic regions. From these findings they conclude that PA28-gamma contributes to chromatin compaction and heterochromatin formation.

Although PA28-gamma has been identified as an alternative component associated with 20S proteasome, its physiological roles remain obscure. The present study demonstrates that PA28-gamma is involved in chromatin compaction and heterochromatin formation. The results presented are in most cases of high quality and convincingly controlled. I have the following concerns that should be addressed by the authors.

Major points: 1) For the localization study (Fig. 1), the authors first show the colocalization of alpha-4, PA28-gamma, and HP1-beta in the nuclear foci induced by ectopic expression of alpha-4-GFP. While the authors point out the similarity of cell-cycle dependent patterns between the alpa-4 induced foci and HP1-beta foci (lines 135-138), this argument seems to be poorly reasoned.

We omitted to mention that we also tested the potential co-localization of alpha-4-GFP with different proteins associated with nuclear foci (SC35, PML PCNA, γH2AX) or BrdU-labelled replication foci without success, before to find a correlation with the accumulation of newly synthesized GFP-HP1β in nuclear foci.

The authors previously showed that ectopically expressed CFP-tagged alpha-7, another core component of 20S, accumulates into discrete nuclear foci, and the foci are colocalized with SC35, a well-characterized member of nuclear speckle (Baldin et al. MCB 2008). Considering that both alpha-4 and alpha-7 are core components of 20S proteasome, it is highly likely that the alpha-4-GFP- accumulating nuclear foci are corresponding to the nuclear speckles. If so, HP1-beta foci should be distinct from that of alpha-4-GFP foci. The authors should test the relationship between alpha-4-GFP foci and nuclear speckles, and if this would be the case, it might be better to omit the colocalization data using cells expressing alpha-4-GFP (Fig. 1) and start by potential colocalization of PA28-gamma and HP1-beta in cells without expressing alpha-4-GFP (Fig. 2).

As mentioned above alpha4-GFP did not co-localize with SC35, a marker of the nuclear speckles. When different alpha subunits of the 20S proteasome are overexpressed, only alpha7 and alpha4 show an accumulation in specific nuclear foci. This remains unclear but a possible explanation could be an alternative composition of alpha subunits in the 20S as previously reported for alpha4 (Padmanabhan A. et al., Assemnbly of an evolutionarily conserved alternative proteasome isoform in human cells, , 2016, Cell Reports). As this part of our study appears to confuse readers and to dilute the essential message of the manuscript, we are considering to exclude these data in the modified version.

2) Although the functional link between PA28-gamma and chromatin compaction seems quite interesting, it remains unclear how it contributes to the establishment of repressive histone marks such as H3K9me3 and H4K20me3. While the authors clearly show that 20S-binding-deficient PA28-gamma mutant (PA28-gamma ∆C) could restore the chromatin compaction defect caused by PA28-gamma KO, it is also possible that PA28-gamma controls the stability of factors involved in heterochromatin assembly. To exclude this possibility the authors should test whether PA28-gamma KD/KD does not affect the protein levels of core histone modifying enzymes and HP1 proteins by immunoblotting.

During this study we performed numerous immunoblots using anti-HP1 antibodies and we did not observe any significant variation of these proteins in KO-PA28γ cells. Furthermore, in an atempt to identify proteins whose stability could be controlled directly or indirectly by PA28γ, we performed a SILAC-based quantitative proteomic analysis comparing nuclear extracts from U2OS or HeLa wild type cells to U2OS- or HeLa KO-PA28γ cells. Under the tested conditions, we could not identify variation of the amount of factors involved in chromatin assembly, suggesting that the impact of PA28γ on chromatin organization is not driven by changes in the level of the important histone-modifying enzymes, nor core components of chromatin such as HP1 proteins.

Reviewer #3:

This manuscript explores the localization and function of a previously studied proteasome activator, PA28gamma. This protein is a nuclear activator of the 20S proteasome and is widely conserved during evolution, although largely absent in fungi. The authors report that (1) subunits of the 20S proteasome (alpha4 and alpha6) and GFP-tagged or endogenous PA28gamma colocalize with each other and with HP1beta in the nucleus, with HP1beta required for the localization of PA28gamma to nuclear foci, (2) depletion of PA28gamma results in decompaction of pericentromeric heterochromatin, and (3) use a FLIM-FRET based microscopy assay to show a broad role for PA28gamma in chromatin compaction, a function that PA28gamma shares with HP1beta. They also show that the C terminus of PA28gamma, which is required for its interaction with the 20S proteasome, is not required for its subnuclear localization or compaction functions, and that PA28gamma KO cells have reduced levels of H3K9me3 and H4K20me3 heterochromatin-associated histone modifications.

The identification of a role for PA28gamma in heterochromatin compaction and heterochromatin maintenance is interesting and raises intriguing possibilities about the role of this protein and the 20S proteasome in heterochromatic domains. The study is largely descriptive and does not provide new mechanistic insight into heterochromatin or PA28gamma. Although the experiments in the paper are of high quality and well-executed, they basically amount to identification of a new factor that affects heterochromatin stability. The fact that PA28gamma is a proteasome activator provides no mechanistic insight since the 20S proteasome does not seem to be required for the heterochromatin compaction function of PA28gamma.

The following suggestions may be helpful to the authors in preparing their manuscript for publication (in order of appearance).

1) The IP experiments in Figure 1D should be performed in the presence of nuclease (DNase/RNase A or benzonase) to test whether the interactions are bridged by RNA or DNA.

We actually tried several times to perform this IP experiments using notably benzonase. However, despite several attempts under various conditions, we could not obtain a clear and consistent answer to this question.

2) Figure 2. What percentage of PA28gamma and HP1beta foci overlap in the absence of alpha4 overexpression?

As indicated in the text, on average of 32 spot of co-localization between the two proteins were detected in Figure 2B and on average of 37 spots in is-PLA experiment (Figure 2C).

3) Figure 3. Does decompaction result in loss of silencing of heterochromatin targets such as HERV-K, LINE1, alpha satellite etc? Ideally, the authors should perform RNA-seq to provide a more complete picture of changes in gene expression as a result of PA28gamma depletion.

RT-qPCRs were performed on heterochromatin loci used for ChIP (HERV-K, L1 Line, SatII and alpha-sat) and no significant variation was observed. In order to determine whether the absence of PA28γ could affect gene expression, we performed a trancriptomic analysis using Affymetrix® Human Gene 2.1 ST Array Strip comparing mRNA expression in U2OS -WT and KO-PA28γ cells. This experiment revealed only very little variation between the two samples tested: 11 genes were up in KO-PA28γ (MFAP5 (Microfibrillar-associated protein 5), GLIPR1 (Glioma pathogenesis-related protein 1) and 9 that are still unannotated), and only 2 genes were significantly down: PSME3 (PA28γ) and MAGE-C1(Melanoma-associated antigen C1). These experiences led us to consider that PA28γ probably does not directly affect the level of transcription.

4) Based on experiments with PA28gamma-deltaC, which does not interact with the 20S proteasome, the authors conclude that the 20S proteasome is not required for the PA28gamma-mediated chromatin compaction. Although their IP data (Figure 4E) seem persuasive, a more convincing experiment would be to also perform the FRET assay for compaction with knockdown of subunits of the proteasome.

Knockdown of 20S proteasome subunits was not performed since in that condition all the proteasome family will be affected, and we already know that depletion of these proteins has several and pleiotropic effects (i.e. cell cycle progression), which could indirectly affect chromatin compaction.

5) Figure 6. It is critical that the effects on histone modifications are evaluated using siRNA KD (or other transient KD methods) of PA28g to complement the KO results. PA28gamma KOs have many defects including genome instability and aneuploidy that may affect K9me3 and K20me3 indirectly.

This is indeed a hypothesis that cannot be ruled out. But considering that these modifications (H3K9me3, H4K20me1/3) are crucial for the establishment of chromatin compaction and that the elimination of PA28γ (siRNA treatment) induces chromatin decompaction within 48h, it is reasonable to consider that the variation of these marks does not result from genome instability.

6) In general, the manuscript would benefit from the addition of genome-wide approaches such as ChIP-seq to gain broader insight into PA28gamma localization and general compaction functions.

We agree that the mapping of PA28γ distribution on non-repeated DNA sequences will be useful for the subsequent studies of PA28γ functions in DNA–related processes such as gene regulation. However, because of the difficulty to map HP1 proteins and heterochromatin regions by ChIP-seq, we do not believe that this approach will necessarily reinforce the current message of this first manuscript on the role of PA28γ in the regulation of heterochromatin compaction.

Reviewer #3:

This manuscript explores the localization and function of a previously studied proteasome activator, PA28gamma. This protein is a nuclear activator of the 20S proteasome and is widely conserved during evolution, although largely absent in fungi. The authors report that (1) subunits of the 20S proteasome (alpha4 and alpha6) and GFP-tagged or endogenous PA28gamma colocalize with each other and with HP1beta in the nucleus, with HP1beta required for the localization of PA28gamma to nuclear foci, (2) depletion of PA28gamma results in decompaction of pericentromeric heterochromatin, and (3) use a FLIM-FRET based microscopy assay to show a broad role for PA28gamma in chromatin compaction, a function that PA28gamma shares with HP1beta. They also show that the C terminus of PA28gamma, which is required for its interaction with the 20S proteasome, is not required for its subnuclear localization or compaction functions, and that PA28gamma KO cells have reduced levels of H3K9me3 and H4K20me3 heterochromatin-associated histone modifications.

The identification of a role for PA28gamma in heterochromatin compaction and heterochromatin maintenance is interesting and raises intriguing possibilities about the role of this protein and the 20S proteasome in heterochromatic domains. The study is largely descriptive and does not provide new mechanistic insight into heterochromatin or PA28gamma. Although the experiments in the paper are of high quality and well-executed, they basically amount to identification of a new factor that affects heterochromatin stability. The fact that PA28gamma is a proteasome activator provides no mechanistic insight since the 20S proteasome does not seem to be required for the heterochromatin compaction function of PA28gamma.

The following suggestions may be helpful to the authors in preparing their manuscript for publication (in order of appearance).

1) The IP experiments in Figure 1D should be performed in the presence of nuclease (DNase/RNase A or benzonase) to test whether the interactions are bridged by RNA or DNA.

2) Figure 2. What percentage of PA28gamma and HP1beta foci overlap in the absence of alpha4 overexpression?

3) Figure 3. Does decompaction result in loss of silencing of heterochromatin targets such as HERV-K, LINE1, alpha satellite etc? Ideally, the authors should perform RNA-seq to provide a more complete picture of changes in gene expression as a result of PA28gamma depletion.

4) Based on experiments with PA28gamma-deltaC, which does not interact with the 20S proteasome, the authors conclude that the 20S proteasome is not required for the PA28gamma-mediated chromatin compaction. Although their IP data (Figure 4E) seem persuasive, a more convincing experiment would be to also perform the FRET assay for compaction with knockdown of subunits of the proteasome.

5) Figure 6. It is critical that the effects on histone modifications are evaluated using siRNA KD (or other transient KD methods) of PA28g to complement the KO results. PA28gamma KOs have many defects including genome instability and aneuploidy that may affect K9me3 and K20me3 indirectly.

6) In general, the manuscript would benefit from the addition of genome-wide approaches such as ChIP-seq to gain broader insight into PA28gamma localization and general compaction functions.

Reviewer #2:

In this manuscript, Fesquet and colleagues describe an important role of the proteasome activator PA28-gamma in the compaction of chromatin. The authors first demonstrate that PA28-gamma colocalizes HP1-beta at nuclear foci induced by the ectopic expression of alpha-4 subunit of the 20S proteasome. They further show that a fraction of PA28-gamma colocalizes also with HP1-beta in cells without ectopic expression of the alpha-4. The authors then show that PA28-gamma is associated with heterochromatic regions and is required for the compaction of lacO array integrated at a pericentromeric region. They also performed the quantitative FLIM-FRET and demonstrate that PA28-gamma controls chromatin compaction in living cells, independently of its interaction with 20S proteasome. Finally, the authors show that PA29-gamma depletion leads to a decrease of heterochromatin marks, H3K9me3 and H4K20me3, at representative heterochromatic regions. From these findings they conclude that PA28-gamma contributes to chromatin compaction and heterochromatin formation.

Although PA28-gamma has been identified as an alternative component associated with 20S proteasome, its physiological roles remain obscure. The present study demonstrates that PA28-gamma is involved in chromatin compaction and heterochromatin formation. The results presented are in most cases of high quality and convincingly controlled. I have the following concerns that should be addressed by the authors.

Major points:

1) For the localization study (Fig. 1), the authors first show the colocalization of alpha-4, PA28-gamma, and HP1-beta in the nuclear foci induced by ectopic expression of alpha-4-GFP. While the authors point out the similarity of cell-cycle dependent patterns between the alpa-4 induced foci and HP1-beta foci (lines 135-138), this argument seems to be poorly reasoned. The authors previously showed that ectopically expressed CFP-tagged alpha-7, another core component of 20S, accumulates into discrete nuclear foci, and the foci are colocalized with SC35, a well-characterized member of nuclear speckle (Baldin et al. MCB 2008). Considering that both alpha-4 and alpha-7 are core components of 20S proteasome, it is highly likely that the alpha-4-GFP- accumulating nuclear foci are corresponding to the nuclear speckles. If so, HP1-beta foci should be distinct from that of alpha-4-GFP foci. The authors should test the relationship between alpha-4-GFP foci and nuclear speckles, and if this would be the case, it might be better to omit the colocalization data using cells expressing alpha-4-GFP (Fig. 1) and start by potential colocalization of PA28-gamma and HP1-beta in cells without expressing alpha-4-GFP (Fig. 2).

2) Although the functional link between PA28-gamma and chromatin compaction seems quite interesting, it remains unclear how it contributes to the establishment of repressive histone marks such as H3K9me3 and H4K20me3. While the authors clearly show that 20S-binding-deficient PA28-gamma mutant (PA28-gamma ∆C) could restore the chromatin compaction defect caused by PA28-gamma KO, it is also possible that PA28-gamma controls the stability of factors involved in heterochromatin assembly. To exclude this possibility the authors should test whether PA28-gamma KD/KD does not affect the protein levels of core histone modifying enzymes and HP1 proteins by immunoblotting.

Reviewer #1:

In the manuscript entitled, "The 20S proteasome activator PA28γ controls the compaction of chromatin," Fesquet et al. establish a functional link between PA28γ and chromatin compaction in human cells. Previous work established a role for PA28γ in DNA repair and in chromosome stability through mitotic checkpoint regulation; however, a role, if any, for PA28γ in heterochromatin establishment/maintenance was not known. The authors use an elegant LacO-GFP system combined with PA28γ knockdown to support the possibility that this nuclear activator contributes to DNA packaging of repetitive DNA. A nucleosome proximity assay offers additional support that the most compacted chromatin is most sensitive to loss of PA28γ. Using a truncated version of PA28γ, the authors show that this chromatin function appears to be independent of its interaction with the 20S proteasome. ChIP-qPCR suggests that PA28γ binds repetitive DNA and ChIP-qPCR of PA28γ knockdown cells lose H3K9me and H4K20me, two silent heterochromatin marks. In addition to these data, the authors also attempt to establish that PA28γ and HP1β may work together to support heterochromatin formation/maintenance. The manuscript reports several intriguing pieces of data that have the potential to open new areas of inquiry into proteasome components and accessory factors in chromatin organization and remodeling. The potency of these key experiments, however, were diluted by unconvincing co-localization assays, poorly controlled PLA and ChIP-qPCR assays, and a highly speculative Discussion. Moreover, key controls were missing for several experiments (detailed below) that would have otherwise established the heterochromatin-specificity of PA28γ. Finally, important potential functional consequences of heterochromatin disruption, including chromosome segregation defects, transposable element proliferation, and accumulation of DNA damage, were not addressed while there was a focus instead on cell cycle without clear interpretations.

Major Comments:

1) Figure 2: The co-localization experiments were unconvincing - HP1β and PA28γ foci decorate most of the nucleus, making inferences about significant overlap difficult to grasp. I also found the significance of the PLA assays difficult to discern. When both factors are so abundant in the nucleus, it seems inevitable to observe loss of proximity when one 'partner' is depleted. How do these data demonstrate the specificity of this potential proximity? A clearer explanation would be helpful. Note that the PIP30 data were a distraction from the main thread - I recommend removing or explaining more clearly.

2) The ChIP-qPCR data were certainly exciting but the absence of a negative control locus made me wonder how specific this result was to DNA repeats.

3) The LacO-GFP data are really cool. Why didn't the authors not attempt to rescue compaction with a PA28γ transgene as was done for the FLIM-FRET?

4) Cell cycle data would be much more interesting if the authors set up a priori predictions based on Figures 1-5.

5) The absence of any report of PA28γ KD/KO on genome instability was surprising. Loss of heterochromatin integrity is expected to compromise chromosome transmission/transposable element expression or insertions. Do the repeats to which PA28γ localizes upregulate upon PA28γ KD or KO? Does DNA damage signaling increase at the loci? These functional consequences would be rather more explicable that the S-phase result reported.

6) The histone mark ChIP-qPCR, like the PA28γ ChIP-qPCR, lacks a negative control locus/loci, again undermining the inference of specificity of PA28γ on heterochromatin.

7) The LLPS paragraph in the discussion was weak - consider removing.

8) The speculation of 20S into foci does not add and, to my mind, detracts from the focus of the Discussion.

Preprint Review

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Summary:

All three reviewers agreed that establishing a link between a proteasome activator and heterochromatin stability was novel and intriguing. However, limited insight into the PA28-gamma mechanism of action (or possibly a new heterochromatin compaction mechanism) dampened reviewer enthusiasm. The reviewers offered many suggestions, including additional experiments, new controls, and structural changes to the Discussion, that we hope you find useful.

Reviewer #3:

The paper "Morphology and local connectivity of the plis de passage in the superior temporal sulcus" is an interesting and thoughtful paper which uses modern tractography methods quite skillfully to examine whether the finer features of gyrification are related to connectivity patterns. This is an understudied area of research in human MRI because it deals with inter-individual variability, and so is time consuming, not well-suited to existing analysis pipelines, and requires a high level of neuroanatomical expertise. The methods, which included impressive inter-rater reliability and a nice control condition, were well-suited to the question. I also very much appreciated the discussion section, which covered anatomical, historical, evolutionary, and developmental considerations quite effectively and with clarity of language. Overall, the paper is well thought out and executed and a joy to read!

Below are some comments that could improve clarity for the reader:

-Figure 2 is a bit difficult to understand - to clarify that a and b are from the first brain, and b and c are from the second brain, the authors might consider labeling them or putting them in boxes. It might be helpful to add some arrows to help illustrate the "pinching" they describe.

-End of results, p. 19, final paragraph. The authors write "Second, there was generally an increasing number of U-shape fibers from the anterior to the posterior part of the STS." I don't think the authors tested this, so I would rephrase this to say "on visual inspection, it appears that there was an increase in...". I would also replace the word "fibers" with "streamlines".

Reviewer #2:

A new characterization of the "plis de passage"(PP) is proposed. The interest of this new definition is demonstrated in a cortical area where a huge amount of variability exists, hence it is very difficult to study. The results shown are convincing. The new connection established between PP and U-fibers contributes to the understanding of the link between gross anatomy and connectivity.

Several questions for clarification:

1) The distribution of the number of PP in STS is given in the results. Did you try to match the PP across the subjects, to try to define a stable model? In terms of the location of the PPs, is a model possible or their positions span the whole main branch of STS in a continuum? Did you try to study the relationships between PP and sulcal pits?

2) Did you try to clarify whether all dense clusters of U-fibers correspond to PP across subjects? Due to the random selection of the extremities of the control PPs, such clusters with different trajectories (not necessarily facing each other) could be missed by your procedure in controls?

3) Is there a link found between the superficiality of a PP and the extent of the shift of the two extremities along the sulcus (the S and C shapes)?

Reviewer #1:

The study aims to improve the anatomical characterisation of STS plis de passage (PPs). Morphologically, the authors use the geometry of the surrounding surface to reveal deep PPs, which might be buried. Structurally, they explore associations with short-range u-shape connectivity across the two banks of the STS. This methodological advancements follow from previous work on the central sulcus (e.g. Zlatkina et al., 2016, European JNS; Catani et al., 2012, Cortex). The authors provide detailed characterisation of these anatomical features in 90 individuals from the HCP dataset, and focus their analysis in differences across the two hemispheres. But the study stops short of showing how this impacts functional organisation or behaviour. Overall, the methodological advancement offered here is incremental relative to other studies, and very little insight is provided about the impact of these morphological features and their variations on STS functional organisation. Considering the HCP offers high quality functional data, including tasks specifically relating to STS function, as well other highly related data (e.g. twins), I thought the present manuscript missed numerous precious opportunities to leverage the present findings into more significant impact and innovation.

Major Comments:

1) The abstract and introduction highlight the importance of studying inter-individual variability in PPs. But the results do not address this variability, as all the results are dedicated to inter-hemispheric differences. What is the significance of inter-individual structural variance, and how is it informed by experience (the introduction suggests that these folding patterns are determined in utero?)? For example, are they more similar in twins? Is there any clear evidence that it determines functional organisation and behaviour? Clinical symptoms? Also, are the inter-individual variations observed specific to the STS? Or do they reflect 'trait' like foldiness of the cortex? None of these questions are explored empirically, and as such, the present findings offer very little advancement to our understanding of STS function and functionality.

2) I'm not sufficiently qualified to determine, but I have to wonder if the 'control PPs' are suitable, considering they are much smaller than the 'true PPs'? Considering the probabilistic nature of the analysis and the fact that the experimenters were not blinded as to which aspect of the sulcus was 'true' or 'control', some more consideration should be given to the appropriateness of this control.

3) The u-shape analysis requires histological confirmation, as demonstrated by Catani et al. for the central sulcus.

4) Nonsignificant results (e.g. between hemispheres) require further consideration - are the two hemispheres truly similar, or is the study underpowered to find such differences? Bayesian statistics can inform this question.

5) I found the discussion to be overly speculative, and in particular the part relating to functional implications to be overly speculative, considering the very modest innovative contribution the current study offered.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The reviewers very much appreciated the careful analysis, including very laborious manual segmentation. They agreed that the study provides a new level of detail of STS morphology that hasn’t been available to date. They also agreed that this characterisation has potential to support future research focusing on the inter-individual variability that is so common in this brain region. However, the study has not yet delivered on this promise, as the analysis is focused on inter-hemispheric differences across the group, without illuminating the impact of inter-individual morphological variability on the area's functional organisation or function.

Reviewer #3:

This is a very interesting paper that describes a novel zebrafish cardiac phenotyping pipeline consisting of high frequency echocardiography, cardiac magnetic resonance imaging (CMR) and micro-computed tomography (micro-CT). The work presented provides proof-of-principle that this suite of elegant techniques provides high resolution images of the adult fish heart. The concerns raised relate mainly to the adoption of this pipeline as a routine phenotyping method and the extent to which the data presented can be considered as a reference set for the field.

Pulsed wave Doppler tracings obtained from high frequency echocardiography are noted for their clarity and reproducibility. The authors took advantage of this, together with color Doppler, to identify abnormal blood flow jets in the alk5 mutant fish. These findings nicely show that echocardiography is a useful screening tool for evaluating mutants with unknown phenotypes or for those in which structural defects are anticipated.

Echocardiography is an established method for quantification of ventricular size and function in adult zebrafish when performed by experienced operators. As noted by the authors, echocardiographic images from a single fish can be collected within minutes and this technique can be used to evaluate large numbers of fish. The real question here is when to implement the complete pipeline and in which situations echocardiography (or one of the other techniques) might be adequate. The authors might consider making some recommendations about this. For example, echocardiography would be sufficient to evaluate adult fish that are expected to have cardiomyopathy phenotypes and completion of the extended imaging pipeline may not be necessary. Procedural tolerance, potential for serial assessment, throughput and cost also need to be considered, especially when substantial numbers of fish need to be evaluated. In order to better compare echocardiography and CMR for assessment of ventricular size and contractile function, echo data for these parameters needs to be included and a comparative analysis undertaken.

The wide range of heart rates in the echo data (58-143 bpm) is a concern and suggests that anesthetic and environmental factors are contributing to variability. The lower value of 58 bpm is notably unphysiological. These extremes of heart rate would confound cardiac assessment, particularly for ventricular size. The causes of these heart rate differences need to be identified, and at the very minimum, greater numbers of fish would need to be studied to be able to identify any biological differences between groups.

A major limitation is the relatively small numbers of fish that have been included in this study. Although looking at 10 WT fish and 12 mutants was sufficient to demonstrate the utility of these imaging methods, there was considerable variability for many of the cardiac parameters measured and the number of WT fish, in particular, is far too small to be robust as a reference data set. If this is an important goal of the paper, then more male and female WT fish of different ages need to be studied. Data also need to be provided for reproducibility, and inter- and intra-observer variability for measurement of cardiac parameters using the different methods.

Reviewer #2:

In this manuscript, the authors conducted phenotypic studies of a zebrafish adult alk5a/tgfr1 mutant by integrating different technologies, including echocardiography, MRI and microCT. They selected 10 WT and 12 alk5a mutants for their studies, and identified some mild phenotypes in OFT. They conducted correlation analysis among different parameters, and then selected fish with more severe phenotypes for further morphological characterization. The strength of the manuscript is optimization of novel technologies including MRI and microCT for cardiac studies, and their integration. However, there are some notable concerns as described below.

Major concerns:

1) There is excessively high variation in almost all parameters among different fish in the same group. For example, heart rate ranges from 58-143 bpm. It appears that adult zebrafish naturally exhibit high phenotypic variation in cardiac functions. However, the authors need to more carefully control their experimental conditions before reaching this conclusion. It has been reported that anesthesia and water temperature might affect cardiac functions in this animal model.

2) The experiments were not designed to deal with the excessively high variation. Fish from three different ages are phenotyped together as a single group, and the size of the group is small. This is a main weakness of the manuscript.

3) Fig. 3-figure supplement 1: contraction of the ventricle appears rather weak (difference between F' vs F" is small). Can you calculate ejection fraction? Is the EF significantly lower than EF in wild type fish that were obtained from high frequency echo or other technologies? Low EF might indicate that the fish is far from normal physiological condition, suggesting that the technology is premature for assessing cardiac function. Moreover, there is a huge difference in heart size between WT and mutant fish (F' vs G').

Reviewer #1:

This study by Benisimo-Brito and colleagues describes a comprehensive integration of functional imaging approaches for adult zebrafish cardiovascular phenotyping. The authors describe combined use of echocardiography, MRI and (ex vivo) micro-CT with light- and transmission electron microscopy to study alk5a-mutant zebrafish. They were able to identify multiple altered phenotypic parameters including abnormal hemodynamics (retrograde blood flow), compromised functional output, and morphological defects, including expanded outflow tract and altered atria and aortae. The authors were also able to nicely correlate the extent of morphological defects with function, across a highly variable range in severity of phenotypes.

This is an informative and elegant use of combined imaging platforms to study adult zebrafish; which has thus far been very challenging, given their opaque nature and the need for specialised adaptation of available clinical modalities. That said, use of some of these platforms has been applied previously for imaging adult zebrafish; for example, echocardiography and MRI (Gonzalez-Rosa et al., 2014; Koth et al., 2017) and micro-CT (most recently, Ding et al., 2019). The authors acknowledge this, but it remains the case that the technical novelty, as applied to functional cardiovascular imaging, is compromised. Instead, the strength here is in the combined, integrated use of multiple platforms. This study on the whole provides a very nice proof-of-principle, but it is unclear how this will be widely adopted by zebrafish laboratories elsewhere, given the need for significant high-end imaging facilities and appropriate in-house expertise. Moreover, the methodologies to adapt the platforms for zebrafish studies are not sufficiently well described herein to enable others to readily adopt.

Other specific comments:

1) The statement on page 8 needs qualifying. MRI has been used previously beyond generating static images in adult zebrafish: Koth et al., (2017) documented longitudinal imaging of live adult zebrafish during heart regeneration.

2) The monitoring of heart rate using self-gating (Figure 3, figure supplement 1C-C') is a nice addition - did the authors explore the use of telemetry probes to record the ECG, as this would be a novel addition to what has gone before?

3) Regarding the correlation analysis on page 10 the authors note 32 parameters. What are the prospects for applying machine learning/AI (eg. automated image analysis algorithms) here to enhance the number of parameters that can be recovered? This in turn would increase the depth of phenotyping and further inform the phenotypic-functional association.

4) The inherent variability of phenotypes between individuals is potentially a significant issue for basic studies, despite mapping to human variation in disease progression/outcome. Given the assumed relatively in-bred nature of the mutant background, why is there such variability and does this reflect on the sensitivity of the imaging? The authors note age and body size (page 11) as influencing variation; if they were to image fish of the same age (and sex) and within a narrow body size range is this variability reduced?

5) As under the general comment above, the methodology is insufficient in places for others to adopt the described imaging platform(s); for example, under echocardiography (page 19) the authors loosely describe a "bed made of modelling clay"- more details are required here and elsewhere to facilitate others utilising similar platforms.

6) Under the MRI procedure the authors decided to analyze specimens in a container without water flow, to reduce the imaging time to less than 20 minutes and consequently to maintain survival. This relatively short imaging time is reflected in the low resolution and somewhat suboptimal images shown in Figure 3C-D. Moreover, in the absence of water flow and gill perfusion it is unclear how any functional parameters obtained are physiologically meaningful? This approach renders the use of MRI more for 3D live imaging than for interrogating function. In the previous MRI study, by Koth and co-workers (2017), live adult zebrafish were placed under anaesthesia and physiological conditions, i.e. upright in water and with gills suitably perfused. This enabled imaging for several hours and with a 100% recovery rate and consequently, the resolution and image quality were higher and the functional parameters more physiologically relevant. The current MRI approach ought to be at least comparable in terms of quality of outputs as that which has gone before.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The reviews highlight the value of imaging adult zebrafish to evaluate cardiovascular structure and function. However, they point out that each of the three imaging technologies has been reported before, and suggest that the manuscript would be strengthened by a more critical comparison between the imaging modalities. The reviewers also raised concerns about the value of the data as a reference for cardiac function parameters, given the small numbers of WT fish, variability in WT fish, and the lack of data for reproducibility, and inter- and intra-observer variability for the various cardiac parameters. Lastly, they felt that the platforms are highly technical and require significant resource and specialist insight into adaptation for use on zebrafish, thus making it unclear how it will be applicable more broadly and within other laboratories in the field.

Reviewer #3:

The article by Youssef G et al, focused on developing a Machine Learning system to use immunofluorescence data to detect metastatic cells in tumor stroma, which might be responsible for metastasis in case of OSCC. To detect single cells in the transition of EMT to MET they focused on EMT-Stem cells rather than only EMT phenotypes. They have shown that retention of epithelial marker EpCAM and stem cell marker CD24 and upregulation mesenchymal marker Vimentin can identify disseminating EMT stem cells in the tumor stroma. It is very well presented, well written and has high implication.

Comments to improve:

1) Strongly recommended to add the distribution of tumor status vs. proposed marker expression pattern. That is to show the distribution of EpCAM, CD24, Vimentin +/- in metastatic vs. other tumor status as mentioned in Supplementary figure 2. This might help you to establish these markers combination to follow a pattern in disease progression.

2) In all cell and tissue images add the scale.

3) For figure 3f, show enlarged picture of the single cell staining on the inset or add a separate panel to show only single cell staining.

4) Figure 4, the panel name or the font is too small to read, enlarge the font size (a, b, c, d, f).

5) Same problem with figure 6a, font size too small. In addition, in the heat maps, is it possible to add cluster names horizontally? Also for figure 6c, the cluster names are too small.

6) The EMT sub-populations are not associated with a spectrum of epithelial/mesenchymal genes expression (supplementary figure 5). The explanation is not very clear.

Reviewer #2:

The authors tackle the important and intractable question of the mismatch between the primacy of EMT in cell culture studies versus the rarity with which EMT is morphologically apparent in resected tumour tissues.

The early part of the study is convincing and well conducted, with identification of subpopulations of EMT cells with the ability to undergo MET, and associated marker profiles in flow cytometry.

They then develop an impressive multiplex assay for the identification of cells with the same profile in resected tumour material- a really promising approach bringing molecular findings into the context of primary tumour tissue.

The major issue that I have is in the application of this assay to tissues, and the subsequent AI analysis. Only one example of the putative invading population is shown (Fig 4C) and the stromal 'infiltrative' subpopulation is adjacent to a very flat and 'pushing' tumour/stroma boundary, with no apparent budding into the stroma. This would need to be addressed with several more examples and high-magnification H&E images. Furthermore, this is a major claim- namely that occult infiltrating EMT cells are commonly encountered in peritumoural stroma but can only be differentiated from somatic stroma by multiplex immunofluorescence- and it needs major evidence to back it up. What do these cells look like on H&E? Are they mesenchymal in their appearances on H&E? Can they be conclusively differentiated from other stromal constituents (eg myofibroblasts, plasma cells) immunohistochemically and/or morphologically? It could be that the power to predict metastatic status power is related to somatic stromal factors rather than EMT.

The AI prediction of metastatic status is compelling, but this fundamental point would need to be persuasively addressed in order to support the author's major claims. I do not feel qualified to comment upon the AI strategies used later in the study.

Reviewer #1:

This manuscript follows previous studies describing the existence of a subpopulation of mesenchymal-like cells (expressing Vimentin) that also express EpCAM and/or CD24 concomitant with the ability to undergo MET. These subpopulations appear to exist within oral squamous cell carcinoma (OSCC) cell lines and within primary tissues. The paper demonstrates that CD24 expression is requisite for plasticity and suggests that the presence of CD24+/EpCAM+/VIM+ cells in the stroma of OSCC tumors may be indicative of metastasis. Some whole genome transcriptome analysis was also done to determine differences between bulk, EMT restricted and EMT stem populations. Overall, the notion that specific cells have the plasticity needed to move between epithelial and mesenchymal states is intriguing, and the presumption that these cells contribute to metastasis seems logical. However, the work is still rather preliminary. Accordingly, it is difficult to make solid conclusions regarding the prognostic utility of this state or of what may regulate it.

Major comments:

The study uses a very small sample size (24 patients) for the test and validation cohorts. The study should be expanded to use a different set of patient samples for test and validation sets. Moreover, the utility of the stem-EMT signature should be tested using multivariate analyses.

In figure 4, it looks like CD24 is positive in the bulk of tumors (regardless of stage) and in skin. Is this specific? Also, there appear to be VIMENTIN/EPCAM/CD24 positive cells in the bulk of non-metastatic tumours. Can this be seen using sequencing? Overall, the images as presented are not overly convincing.

EMT stem versus restricted signatures should be validated using additional models. Also, greater evidence is required to determine how these cell fractions may differ. Are they sitting in different epigenetic states? Can trajectories be detected in human cancers, using single cell sequencing, for example? Finally, do they have different metastatic potentials?

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

This manuscript was reviewed by experts in the areas of cancer stem like cells, EMT events and pathology. Overall, all of the reviewers were intrigued by the concepts underlying this paper. However, it seems that the work is validating the existence of an EMT-stem like population, whilst also attempting to formulate a clinical prognostic application for the existence of these cells. The function of these cells as metastatic drivers requires further exploration. Moreover, the pathological assessments must be improved upon. We hope that these comments are helpful.

Reviewer #3:

General assessment:

Futai and colleagues present an extremely elegant study in hippocampal CA1 slice cultures which combines cell type-specific expression of inhibitory synapse markers and conditional deletion of neurexins (Nrxn), knockdown of neuroligin3 (Nlgn3) and rescue experiments with defined splice variants of Nrxn by biolistic transfection with paired patch-clamp recordings. They find that synaptic transmission between inhibitory cholecystokinin(&VGT3)-positive interneurons (VGT3+) and CA1 pyramidal neurons depends specifically on the combination of presynaptic Nrxn1α with insert in splice site #4 and postsynaptic Nlgn3 without A1&A2 splice inserts.

Major concerns:

1.) The role of neurexins for transmission at the VGT3+ interneuron-to-CA1-pyramidal cell synapse remains unclear: The authors claim that Nrxn are important for the transmission at the VGT3+ synapse. However, I do not see the necessary experiment to substantiate such a general claim, for example, by comparing VGT3+synapses of control/undeleted to deleted NrxnTKO slices. Figure 5 rather shows that Nrxn is required to mediate the effect of overexpression of transfected Nlgn3Δ in CA1 neurons but this might be due to the overexpression itself. Thus, this effect would be more convincing if lack of Nrxn at VGT3+ synapses caused the opposite result on uIPSCs.

2.) The idea of "A Specific Neuroligin3-αNeurexin1 Code ..." implies to most readers that a direct interaction between these two molecules is involved because numerous biochemical papers in the field have used the term splice code to refer to a hierarchy of binding affinities between Nrxn and Nlgn variants. However, such preferential binding of αNrxn1+AS4 to Nlgn3Δ is neither shown in the manuscript, nor is it likely: The authors report that „αNrxn1+AS4 and βNrxn3-AS4 are the unique Nrxn genes expressed in VGT3+ neurons compared with PV+ and Sst+ neurons" (Figure 6 & 7) but demonstrate that of these two isoforms, only αNrxn1+AS4 transfected into VGT3+ interneurons mediated the effect of Nlgn3Δ overexpressed in pyramidal neurons (Figure 8). If binding or direct physical interaction was involved in the mechanism, βNrxn3-AS4 should have performed better than αNrxn1+AS4 because both the LNS5-EFG-LNS6 cassette and the insert in AS4 reduced the affinity. The surprise is shared by the authors themselves in the last paragraph of the Results section (p.12). At least to me, it appears that additional pre- or postsynaptic molecules, or a different mechanism altogether, are involved in mediating the effect of αNrxn1+AS4&Nlgn3Δ on VGT3+ synapses.

3.) To actually prove the specificity of the impact of Nlgn3Δ splice variant on inhibitory transmission from VGT3+ interneurons (Figure 2), an important control is missing: Another Nlgn3 variant, in which the A inserts are present, should be tested in the overexpression experiment. I do acknowledge that the authors compared different Nlgn3 variants in a recent paper (Uchigashima et al., 2020, JBC) in a related setting but no data exist for the proposed specificity of the Nlgn3Δ splice variant at VGT3+ synapses as far as I can see.

Reviewer #2:

Motokazu et. al., identified a specific Nlgn-Nrxn pair that regulates GABAergic synapse function in a subset of interneurons. This is a really interesting study, in which they use complicated techniques to dissect NLGN3 and NRXN function. The authors performed elaborate experiments from a single cell level to a tissue level that support their conclusions. Overall the data appear of high quality and reliable, but the study would benefit from some clarification of text and figures.

1) They are doing overexpression experiments on a WT background, so it's impossible to know if this effect is from homodimers of NLGN3 or heterodimers of NLGN3 with either NLGN1 or NLGN2. Perhaps the authors could discuss this caveat in the manuscript.

2) The authors see an increase in IPSCs when o/e NLGN3 in pyramidal neurons when Sst+ neurons were stimulated using optogenetics, whereas Horn and Nicoll did not see any changes. Horn and Nicoll used NLGN3A2 (including A2 insert) and in this study the construct doesn't have A1 or A2 insert. Perhaps they can discuss if the A2 insert can potentially be the culprit for the discrepancy if this is a potential confounding factor.

Additional comments:

1) In Fig. 1, please indicate Fig. 1C in the legends and make a box for the enlarged region in the lower magnificent image. It would be better to take out the busy alphabetic labels (E1, E2, E3, etc.).

2) Please increase text font size for the sample traces in all figures.

3) Authors showed quantitative graphs showing connectivity but definition of the connectivity is not well explained. More detailed explanation for how they quantified the connectivity should be addressed in methods.

4) In Fig. 5A, it would be more accurate to normalize KO Nrxns to WT Nrxns (set WT Nrnx as 100 %). The current Fig. 5A graph looks like Nrxn3 is not dominant in WT mice (~ 0.1 %) but the Fig. 7B graph shows Nrxn3 is dominant. Is there a discrepancy or perhaps add an explanation?

5) In Fig. 6J, the graphs for βNrxn1, αNrxn2, and βNrxn2 can go together with the image data in Figure S3.

6) Authors should explain and provide more information about the parameters of the Fig. 7A plot in the main text and legends. Correct the missed indication of Fig. 2B in the results text.

7) What if presynaptic αNrxn1+AS4 couples with Nlgn3 KD or NlgnTKO condition? What would be the expectation?

Reviewer #1:

Gaining insights into synapse-type specific regulatory mechanisms is of significant general interest. Yet, substantial concerns need to be addressed to improve this study.

Major points:

1) The authors state that Nlgn3 is particularly enriched at VGT3+ synapses. This is based on the colocalization of immunolabeling for Nlgn3 and each of the markers for three interneurons types as well as with the general inhibitory synapse marker VIAAT in Figure 1. If the intensity of marker labeling is not similar across interneuron types and if imaged fields are not comparable, the use of Nlgn3 co-labeling to assess a preferential localization is compromised. This concern is apparent e.g. in the example image for SST+ synapses with its weak labeling (Fig 1J) and needs to be addressed.

2) The data in Figure 5 support that the lack of presynaptic Nrxns 1/2/3 abolishes the potentiation effect of VGT3+ inhibitory synaptic transmission by Nlgn3Δ. To interpret these data, the authors also need to show whether the Nrxn triple KO in VGT3+ cells affects the amplitude of uIPSCs in postsynaptic control neurons expressing Nlgns at endogenous level.

3) The physiological findings are based on paired recordings where genetically labeled VGT3+ interneurons are stimulated. These cells are sparse and heterogeneously distributed in CA1 (Pelkey et al., Physiological Reviews 2017). Given the issues with Cre driver lines, a more thorough analysis is needed to establish that bona fide VGT3+ interneurons contribute to the reported findings. The scattered distribution of the individual RFP+ cells in single-cell RNAseq data (Fig 7a) adds to this concern about cell identity. The only relevant evidence presented is the IHC analysis in Fig S1A-C but it does not include probes for other interneuron types in the CA1 that shows the specificity of the VGT3+ label.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary

This study by Uchigashima et al. investigates to what extent Neurexin-Neuroligin interactions define synapse functions in an inhibitory microcircuit in the hippocampal CA1. The authors propose that Neuroligin-3 and Neurexin-1α regulate inhibitory synaptic transmission at synapses formed by vGluT3-positive (VGT3+) interneurons on CA1 hippocampal pyramidal neurons. This is based on (1) immunohistochemical data that localize Nlgn3 to synapses of VGT3+ interneurons, (2) the regulation of unitary inhibitory postsynaptic currents by Nlgn3 overexpression or knockdown in postsynaptic pyramidal neurons in organotypic slices from VGT3+ reporter mice, and (3) the finding that Nrxn deletion in VGT3+ interneurons prevents the effect of Nlgn3 overexpression in postsynaptic neurons. Single-cell RNA sequencing and in situ hybridization are presented to show that Nrxn1α and Nrxn3beta mRNAs are prominent Nrxn isoforms in VGT3+ interneurons, and Nrxn1α SS4 rescued Nrxn deletion effects. With some additional critical controls and a more careful interpretation of the presumed mechanism, the manuscript would make a highly interesting contribution to the field of synapse specification by synaptic cell adhesion molecules.

Author Response

Reviewer #1:

The manuscript by Mitchell et al. finds that the NAIP-NLRC4 inflammasome in mice is a critical host factor that controls intestinal infection with the human specific bacterial pathogen Shigella flexneri. The work suggests that Shigella is actively suppressing the human NAIP-NLRC4 inflammasome possibly using an T3SS effector protein, which does not recognize its substrate in mouse cells. The authors use this information to determine that B6 mice lacking the NAIP or NLRC4 inflammasome components are susceptible to Shigella infection and observe disease symptoms similar to Shigellosis in humans. In addition, 129 mice exhibit additional disease symptoms, and the authors suggest that loss of Caspase-11 in 129 mice is responsible for this phenotype.

The strengths of this manuscript include the introduction of a new mouse model that mimics Shigellosis, the demonstration that NAIP/NLRC4 activation is important for epithelial cell defense, and the potential of these findings to clarify aspects of human infectious disease caused by this pathogen. The manuscript is well presented, and the experiments are conducted with a high degree of rigor. Overall, this is an important contribution to the Shigella field and also has significant implications on our understanding of inflammasomes in host defense against pathogens.

Response: We thank the Reviewer for recognizing the impact and rigor of our work.

There are some weaknesses that should be addressed. Experimentally, it has not been directly demonstrated that IECs from NLRC4-/- mice undergo cell death (using biochemical markers). This is a critical aspect of the model.

Response: Prior work in the field (e.g., Sellin et al, 2014; Rauch et al, 2017) has already established that inflammasome activation in IECs results in their death and expulsion from the intestinal epithelium. We are currently working on showing this also occurs with Shigella but we have no reason to doubt that it does; our preliminary data indicate that Shigella-infected propidium iodide (PI)-positive cells are expelled from IEC monolayer cultures in an NLRC4-dependent manner. We intend to provide these data in a revised version of the manuscript.

In addition, it would be useful for the authors to evaluate bacterial burden over the time course in Figure 6. Although this is not absolutely necessary to support the manuscript conclusions, this information would greatly benefit the community that intends to use these mice in the future.

Response: This is indeed an experiment we plan to complete in the future. At present we are constrained by the numbers of available mice. We agree with the reviewer that the timecourse is not essential to establish the main conclusions of the present manuscript, and have thus prioritized other experiments.

There are also some discussion points about the mouse model that would enhance the overall impact of the work. For example, a more in depth discussion about the differences between human Shigella infection and the new model would be helpful. It is important to emphasize that the mouse model requires a much greater inoculum of the pathogen to induce disease and requires microbiota-deficiency to be effective. What are the implications of this finding on our understanding of human disease?

Response: Although it is often (correctly) stated that as few as 10-100 bacteria can infect humans with Shigella, there is actually considerable heterogeneity in the infectious dose. DuPont et al 1989 summarizes several human challenge studies in their Table 1, which shows that while 25-39% of humans exhibit symptoms after low dose infection (<200 CFU), 36-44% of humans are resistant to high doses (10^4-10^8 CFU). Therefore we do not consider the infectious dose in our mouse model to be out of the range of what is ‘normal’ in humans. Indeed, our new model may help us understand some of the factors that confer resistance to certain humans. We used a dose of 5x10^7 in our manuscript to ensure reproducible infection of all mice. However, in limited studies, we have observed disease in oral route infected, antibiotic pre-treated NAIP–NLRC4-deficient mice with 10^6 CFU (4/4 mice) and 10^5 CFU (2/3 mice). We are currently repeating these experiments, which we intend to include in a revised manuscript. We also agree with the reviewer that the infectious dose in humans vs. mice merits more discussion in a revised manuscript.

In lines 274-285 the authors present an either/or scenario in which either macrophage pyroptosis is required for IEC infection or inhibition of NAIP/NRLC4 pyroptosis in IECs is required for IEC infection. However, these scenarios are not mutually exclusive. For example, it is plausible that the extremely low burdens of Shigella required to infect humans (<100 CFUs) is due to the pathogen initially crossing the epithelial barrier (e.g. through M-cells) to infect macrophage, and then re-infection of IECs after macrophage pyroptosis. In this scenario, the NAIP/NLRC4 inflammasome could prevent further expansion of bacterial in IECs by eliminating the cell-to-cell spread that have been described by others. Importantly, the macrophage lifecycle stage may not be necessary in mice in which the microbiota has been removed and Shigella is delivered at a very high inoculum. While, additional ideas could be, and should be, put forth since the mouse model provides new insights or challenges an existing dogma in the field.

Response: We do clearly state in our manuscript (line 277) that our results do not directly address the question of whether Shigella might benefit from inflammasome activation in macrophages. In a revised version of the manuscript we will further expand on the discussion of the role of inflammasomes in macrophages and IECs to acknowledge multiple, non-mutually exclusive scenarios.

Reviewer #2:

Mitchell et al explore the role of NLRC4 in defending against Shigella infection by demonstrating that NLRC4 contributes to resistance to shigellosis in mice. Using in vitro assays, they first show that mouse but not human macrophages undergo NLRC4-mediated pyroptosis in response to Shigella infection despite an ability for both species to successfully detect Shigella NLRC4 agonists. They then demonstrate that C57BL/6 background mice, which normally resist shigellosis, become susceptible to infection when deficient in NAIPs or NLRC4. In parallel, 129 background mice develop more significant infection including intestinal bleeding. Furthermore, using a mouse line in which NLRC4 expression is restricted to intestinal epithelial cells (IECs), they show that IEC expression of NLRC4 is sufficient to resist shigellosis. Finally, using a known attenuated Shigella mutant, they demonstrate that their shigellosis model can mimic kinetics seen in humans.

Mitchell et al convincingly demonstrate both the importance of NLRC4 in protecting mice against Shigella and the utility of their mouse model for studying Shigella infections, both of which are significant and will push the Shigella field forward. There are mechanistic questions to be addressed in future studies beyond the current manuscript, attesting to the importance of the paper in opening up new areas in the field of research. In some places, the authors draw conclusions that reach beyond what is proven in the data, which should be addressed in text edits to the manuscript. In summary, this article presents an important new model for Shigella infection. The impact of the manuscript is the development of a mouse model with which to study Shigella infection in vivo.

Response: We thank the Reviewer for emphasizing the importance of our new shigellosis model for the field. We have addressed their comments below.

Major comments:

Many questions remain concerning why NLRC4-deficient THP1 cells still undergo pyroptosis. The authors provide evidence that Shigella activates PYRIN and/or AIM2 inflammasomes in humans, and that somehow mouse macrophages would fail to have this same detection. At face value, the data would suggest that humans are able to detect Shigella by Pyrin and AIM2, but for some reason these two inflammasomes are insufficient, and instead NLRC4 is required for in vivo defense. Then in mice, it would imply that everything is flipped - for some reason detection by Pyrin and AIM2 is not important, but now the bacteria can be detected by NLRC4 and this is important. The NLRC4 focused conclusions are consistent with the in vivo data, that NLRC4 in humans fails to detect, but NLRC4 in mice succeeds in detecting Shigella. However, the data that Pyrin and AIM2 in human cells successfully detect Shigella are inconsistent with the overall conclusions of the paper. I suspect that this is an artifact of THP1 cells, and that the in vivo situation in humans is that these two inflammasomes will fail to detect Shigella. There is published precedent from other infections where in vitro detection belies in vivo lack of detection (e.g. Listeria is detected by AIM2 in vitro, but probably not in vivo). It may be difficult to make direct comparisons between how inflammasomes act in THP1 cells as compared to BMMs, due to artifacts arising from the different origins and passage levels of the two cell types. It may be that the inflammasomes response is most important in IECs, as proposed by the authors, and that IECs may not express Pyrin or AIM2. There is evidence from publicly available IEC transcriptional profiles that IECs do not express Pyrin (Mefv) (Reikvam, doi: 10.1371/journal.pone.0017996), although this profile does show Aim2 expression in IEC. It is my understanding that BMMs do not express Pyrin unless they are strongly stimulated with some TLR agonist. As it stands, the in vitro data appear to contradict one of the main conclusions of the paper, because it would seem that human Pyrin and AIM2 inflammasomes can detect Shigella, and so these should compensate for NLRC4. The explanation as to why Pyrin and AIM2 are insufficient to compensate for NLRC4 evasion in human infection should be addressed at least in discussions of the data to explain the apparent discrepancy.

Response: The reviewer states that our claim that human PYRIN and AIM2 inflammasomes can detect Shigella in THP1 cells is “inconsistent” with the overall conclusion of our paper, which is that the NLRC4 inflammasome provides necessary defense of mouse intestinal epithelial cells. We do not agree that there is an inconsistency and indeed many of the points the reviewer makes in their comments fit with our view, so perhaps there is less disagreement than it might seem.

As the reviewer discusses, differences in inflammsome expression in humans vs. mice, and in IECs vs. macrophages vs. THP1 cells, and the kinetics of inflammasome responses, as well as several other factors, can easily account for the results we obtain. It appears that PYRIN is not well expressed in mouse IECs (Price et al. 2016), at least not uniformly at levels in all cells that are sufficient to confer protection. AIM2 is expressed in colonic IECs (Price et al. 2016), but it is not clear that it would be engaged in every infected IEC. For example, AIM2 detects bacterial DNA, which might only be released if the Shigella bacteria lysed in the cytosol. As noted by the reviewer, this may be a relatively rare event, as previously documented for AIM2 activation by Listeria-infected macrophages (Sauer JD et al, 2010). AIM2 activation may also be kinetically delayed in IECs. It appears instead that NLRC4 is the main inflammasome that can respond to Shigella in mouse IECs; thus loss of NLRC4 is sufficient to lead to susceptibility of mice. It remains possible that there is some functional AIM2 or PYRIN (or CASP11 or NLRP1B) in mouse IECs; thus, the further removal of these inflammasomes might lead to even greater susceptibility. Alternatively, a low level of activation mediated by these additional inflammasomes (perhaps in macrophages instead of in IECs) might even be necessary to produce the inflammation that causes disease symptoms.

In humans, consistent with our data in Fig. 1, we propose that the NLRC4 inflammasome is antagonized or otherwise evaded by Shigella. The reviewer wonders why PYRIN or AIM2 cannot compensate for NLRC4, and is suspicious that the activation of PYRIN/AIM2 we observe in THP1 cells is not representative of what would occur in vivo. Certainly we agree that THP1 cells are non-physiological and we do not attempt to make claims in the manuscript that our observation of AIM2/PYRIN activity in these cells means anything for human shigellosis.

The reviewer states: “the in vitro data [in THP1 cells] appear to contradict one of the main conclusions of the paper, because it would seem that human Pyrin and AIM2 inflammasomes can detect Shigella, and so these should compensate for NLRC4.” For all the reasons discussed above, we do not agree there is a contradiction. There are many reasons why PYRIN and AIM2 might function in THP1 cells (and possibly even human macrophages) but would not compensate for NLRC4 in IECs.

In sum, we agree that there is more to learn about which inflammasomes, if any, are activated by Shigella in human IECs, but given the many uncertainties, we do not feel it is fair to say that our results are internally contradictory. We will endeavor to discuss some of these points in a revised manuscript.

Reviewer #3:

Mitchell et al describe the development of a mouse model for shigella gastroenteritis, the lack of which has been a serious impediment to Shigella research. They identified a difference in recognition of shigella between human and mouse Naip/NLRC4 which contributes to the resistance of mice to Shigella gastroenteritis. They suggest that Shigella specifically inhibits human Naip/NLRC4 activation and that the difference between mice and human susceptibility to infection is due to differential inhibition. This was confirmed by the ability of NLRC4-/- mice can recapitulate human infection. Furthermore they show that it is inhibition of NAIP-NLRC4 in IEC that is required for infection to occur. This manuscript therefore describes a number of important findings and uses these to develop a very useful animal model of shigellosis.

We are grateful for the Reviewer’s comments and suggestions, and provide point-by-point responses below:

I have three suggestions that I believe would improve the manuscript:

1) Determine the inflammasome that causes cell death in Shigella-infected THP1's. WT Shigella infection did not induce pyroptosis of colchicine-treated (PYRIN inhibitor) AIM2-/- THP1 cells, indicating one or both of these inflammasomes is responsible for the cell death observed in shigella infected THP1 cells. Why not test these separately to determine which?

Response: We have now made AIM2/MEFV–/– THP-1 cells. Our preliminary finding is that cell death and IL-1B levels in these cells are impaired in response to Shigella infection. We intend to include these data in a revised manuscript.

2) Markers of inflammation during disease. Clinical features of the disease (diarrhoea, weight, CFU/organ, fecal blood) are described well. But since Shigellosis is an inflammatory disease, it would have been nice to have seen some inflammatory molecules/cytokine levels measured, in addition to clinical features. The authors did measure levels of MPO, but that was as a marker for neutrophil recruitment.

Response: We agree that additional readouts of inflammatory disease are warranted. We are planning to repeat our experiments and measure cytokines in the blood. We intend to provide these data in a revised manuscript.

3) Further refinement of the mouse model. The authors present the inhibition of human NAIP/NLRC4 as the main factor that affects the difference in infection between humans and mice but a high innolcum (5 x 10(7) cfu/mouse compared to approx. 100 cfu for humans) is still required in addition to streptomycin treatment. It is not discussed whether any refinement of these procedures was attempted or why such a high inoculum and streptomycin treatment is still required. Presumably microbiota differences in addition to naip-/nlrc4 is an important species specific determinant of infection, hence the streptomycin treatment. Why is such a high innoculum required?

Response: this comment is similar to one of the comments of Reviewer 1. As we state above, it is actually not entirely clear that the infectious dose for humans is consistently ~100 CFU. Indeed, there appears to be great variation, with some humans exhibiting resistance to doses more than 10^5 CFU. Although we used high inoculums in our experiments, this was just to ensure consistent infection of all mice. Preliminary experiments in which we reduce the dose suggests that, like some humans, some mice are also susceptible to lower doses (e.g., 10^5 CFU). Thus our model exhibits an infectious dose within the range of what is observed in humans and we do not feel there is a large discrepancy here, though it appears that we do not recapitulate the extreme susceptibility seen in some humans. We don’t find this particularly surprising as Shigella is a human-specific pathogen and it is likely that at least some of its virulence factors may not work well in mice. Instead, we think what is most surprising is that loss of one host defense component (NLRC4) is sufficient to produce disease symptoms that are strikingly similar to what is seen in humans. We acknowledge that one difference is the need for streptomycin in our model. Clearly this suggests, as the reviewer states, that the microbiota can influence susceptibility. This is a well-described phenomenon with many enteric pathogens and it will be of interest in future studies to determine what components of the microbiota afford protection in our model.

Reviewer #3:

Mitchell et al describe the development of a mouse model for shigella gastroenteritis, the lack of which has been a serious impediment to Shigella research. They identified a difference in recognition of shigella between human and mouse Naip/NLRC4 which contributes to the resistance of mice to Shigella gastroenteritis. They suggest that Shigella specifically inhibits human Naip/NLRC4 activation and that the difference between mice and human susceptibility to infection is due to differential inhibition. This was confirmed by the ability of NLRC4-/- mice can recapitulate human infection. Furthermore they show that it is inhibition of NAIP-NLRC4 in IEC that is required for infection to occur. This manuscript therefore describes a number of important findings and uses these to develop a very useful animal model of shigellosis.

I have three suggestions that I believe would improve the manuscript:

1) Determine the inflammasome that causes cell death in Shigella-infected THP1's. WT Shigella infection did not induce pyroptosis of colchicine-treated (PYRIN inhibitor) AIM2-/- THP1 cells, indicating one or both of these inflammasomes is responsible for the cell death observed in shigella infected THP1 cells. Why not test these separately to determine which?

2) Markers of inflammation during disease. Clinical features of the disease (diarrhoea, weight, CFU/organ, fecal blood) are described well. But since Shigellosis is an inflammatory disease, it would have been nice to have seen some inflammatory molecules/cytokine levels measured, in addition to clinical features. The authors did measure levels of MPO, but that was as a marker for neutrophil recruitment.

3) Further refinement of the mouse model. The authors present the inhibition of human NAIP/NLRC4 as the main factor that affects the difference in infection between humans and mice but a high innolcum (5 x 10(7) cfu/mouse compared to approx. 100 cfu for humans) is still required in addition to streptomycin treatment. It is not discussed whether any refinement of these procedures was attempted or why such a high inoculum and streptomycin treatment is still required. Presumably microbiota differences in addition to naip-/nlrc4 is an important species specific determinant of infection, hence the streptomycin treatment. Why is such a high innoculum required?

Reviewer #2:

Mitchell et al explore the role of NLRC4 in defending against Shigella infection by demonstrating that NLRC4 contributes to resistance to shigellosis in mice. Using in vitro assays, they first show that mouse but not human macrophages undergo NLRC4-mediated pyroptosis in response to Shigella infection despite an ability for both species to successfully detect Shigella NLRC4 agonists. They then demonstrate that C57BL/6 background mice, which normally resist shigellosis, become susceptible to infection when deficient in NAIPs or NLRC4. In parallel, 129 background mice develop more significant infection including intestinal bleeding. Furthermore, using a mouse line in which NLRC4 expression is restricted to intestinal epithelial cells (IECs), they show that IEC expression of NLRC4 is sufficient to resist shigellosis. Finally, using a known attenuated Shigella mutant, they demonstrate that their shigellosis model can mimic kinetics seen in humans.

Mitchell et al convincingly demonstrate both the importance of NLRC4 in protecting mice against Shigella and the utility of their mouse model for studying Shigella infections, both of which are significant and will push the Shigella field forward. There are mechanistic questions to be addressed in future studies beyond the current manuscript, attesting to the importance of the paper in opening up new areas in the field of research. In some places, the authors draw conclusions that reach beyond what is proven in the data, which should be addressed in text edits to the manuscript. In summary, this article presents an important new model for Shigella infection. The impact of the manuscript is the development of a mouse model with which to study Shigella infection in vivo.

Major comments:

Many questions remain concerning why NLRC4-deficient THP1 cells still undergo pyroptosis. The authors provide evidence that Shigella activates PYRIN and/or AIM2 inflammasomes in humans, and that somehow mouse macrophages would fail to have this same detection. At face value, the data would suggest that humans are able to detect Shigella by Pyrin and AIM2, but for some reason these two inflammasomes are insufficient, and instead NLRC4 is required for in vivo defense. Then in mice, it would imply that everything is flipped - for some reason detection by Pyrin and AIM2 is not important, but now the bacteria can be detected by NLRC4 and this is important. The NLRC4 focused conclusions are consistent with the in vivo data, that NLRC4 in humans fails to detect, but NLRC4 in mice succeeds in detecting Shigella. However, the data that Pyrin and AIM2 in human cells successfully detect Shigella are inconsistent with the overall conclusions of the paper. I suspect that this is an artifact of THP1 cells, and that the in vivo situation in humans is that these two inflammasomes will fail to detect Shigella. There is published precedent from other infections where in vitro detection belies in vivo lack of detection (e.g. Listeria is detected by AIM2 in vitro, but probably not in vivo). It may be difficult to make direct comparisons between how inflammasomes act in THP1 cells as compared to BMMs, due to artifacts arising from the different origins and passage levels of the two cell types. It may be that the inflammasomes response is most important in IECs, as proposed by the authors, and that IECs may not express Pyrin or AIM2. There is evidence from publicly available IEC transcriptional profiles that IECs do not express Pyrin (Mefv) (Reikvam, doi: 10.1371/journal.pone.0017996), although this profile does show Aim2 expression in IEC. It is my understanding that BMMs do not express Pyrin unless they are strongly stimulated with some TLR agonist. As it stands, the in vitro data appear to contradict one of the main conclusions of the paper, because it would seem that human Pyrin and AIM2 inflammasomes can detect Shigella, and so these should compensate for NLRC4. The explanation as to why Pyrin and AIM2 are insufficient to compensate for NLRC4 evasion in human infection should be addressed at least in discussions of the data to explain the apparent discrepancy.

Reviewer #1:

The manuscript by Mitchell et al. finds that the NAIP-NLRC4 inflammasome in mice is a critical host factor that controls intestinal infection with the human specific bacterial pathogen Shigella flexneri. The work suggests that Shigella is actively suppressing the human NAIP-NLRC4 inflammasome possibly using an T3SS effector protein, which does not recognize its substrate in mouse cells. The authors use this information to determine that B6 mice lacking the NAIP or NLRC4 inflammasome components are susceptible to Shigella infection and observe disease symptoms similar to Shigellosis in humans. In addition, 129 mice exhibit additional disease symptoms, and the authors suggest that loss of Caspase-11 in 129 mice is responsible for this phenotype.

The strengths of this manuscript include the introduction of a new mouse model that mimics Shigellosis, the demonstration that NAIP/NLRC4 activation is important for epithelial cell defense, and the potential of these findings to clarify aspects of human infectious disease caused by this pathogen. The manuscript is well presented, and the experiments are conducted with a high degree of rigor. Overall, this is an important contribution to the Shigella field and also has significant implications on our understanding of inflammasomes in host defense against pathogens.

There are some weaknesses that should be addressed. Experimentally, it has not been directly demonstrated that IECs from NLRC4-/- mice undergo cell death (using biochemical markers). This is a critical aspect of the model. In addition, it would be useful for the authors to evaluate bacterial burden over the time course in Figure 6. Although this is not absolutely necessary to support the manuscript conclusions, this information would greatly benefit the community that intends to use these mice in the future.

There are also some discussion points about the mouse model that would enhance the overall impact of the work. For example, a more in depth discussion about the differences between human Shigella infection and the new model would be helpful. It is important to emphasize that the mouse model requires a much greater inoculum of the pathogen to induce disease and requires microbiota-deficiency to be effective. What are the implications of this finding on our understanding of human disease? In lines 274-285 the authors present an either/or scenario in which either macrophage pyroptosis is required for IEC infection or inhibition of NAIP/NRLC4 pyroptosis in IECs is required for IEC infection. However, these scenarios are not mutually exclusive. For example, it is plausible that the extremely low burdens of Shigella required to infect humans (<100 CFUs) is due to the pathogen initially crossing the epithelial barrier (e.g. through M-cells) to infect macrophage, and then re-infection of IECs after macrophage pyroptosis. In this scenario, the NAIP/NLRC4 inflammasome could prevent further expansion of bacterial in IECs by eliminating the cell-to-cell spread that have been described by others. Importantly, the macrophage lifecycle stage may not be necessary in mice in which the microbiota has been removed and Shigella is delivered at a very high inoculum. While, additional ideas could be, and should be, put forth since the mouse model provides new insights or challenges an existing dogma in the field.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary

In this manuscript, the authors introduce a new mouse model of Shigellosis, provide evidence for NAIP/NLRC4 activation as being important for epithelial cell defense, and apply these findings to observations made in humans infected by this pathogen. These are important findings and provide an opportunity to further advance the field in ways not previously possible. However, there are areas where the in vitro and in vivo data presented contradict each other, and there are inconsistencies with previously published work by the authors. In addition, with the development of the new mouse model being a major highlight of this manuscript, significantly more detail and discussion must be added to explain this mouse model.

Reviewer #3:

Luo and colleagues use a combination of viral tracing and targeted neuronal manipulation tools to dissect the role of GABAergic retinal ganglion cells (RGC) in mediating aversive responses to looming visual stimuli. This paper reports the existence of a population of GABAergic RGCs projecting to the superior colliculus (SC). These conclusions were based on a set of retrograde and anterograde tracing experiments in two mouse lines that putatively label GABAergic neurons (vGAT-Cre and GAD2-Cre). Targeted ablation of the GABAergic RGCs compromised looming-triggered escape behavior, which suggests a possible involvement of the superior colliculus projecting GABAergic RGCs in mediating the looming-evoked flight response. Although these findings could provide important insights into the neural circuitry that mediates aversive behaviors, tracking the origin of these circuits back to the retina, we have major concerns with the paper in its current format.

The current data set raises three major concerns that need to be addressed.

-First, the specificity of the labelling strategies is insufficient to make the current claims. The viral tools used to kill or manipulate RGCs are not specific for either RGCs (shRNA experiment), or SC-projecting RGCs (DTA experiments), and hence do not support the pathway specific claims in the manuscript. Also, the presented data raises questions as to whether all labeled neurons in these mouse lines are functionally inhibitory in the adult retinal.

-Second, the behavioral tests performed do not check for effects of killing GABAergic RTGCs on thalamic dependent visual processing.

-Third, the presentation of the data makes it very difficult for the reader to ascertain the claims made by the authors. In addition, the writing needs major revision.

Major concerns:

1) Lack of specificity of the labelling strategy. The authors claim that GABAergic RGCs mediate escape responses via GABA release in the SC. The current data does not support this claim since none of the used tools is specific enough. To maintain these claims, the authors need to either test if the SC-projecting GABAergic RGCs have no (or minimal) collateral projections to other targets or if the ganglion cells that collaterally project to other brain areas are not involved in the aversive behavior being tested. Further, it is necessary to narrow down the cell populations affected by their manipulations and to show that GABA-release by RGCs is involved in the tested escape behavior.

a. We are concerned that the mouse lines used, in particular the vGAT line, do not label cells that are functionally GABAergic in an adult animal. The gene coding for vGAT, Slc32al, is found in amacrine cells, but not in RGCs (Siegert et al. 2011). In Figure 1, the GABAergic positive cell bodies are not confirmed as being RGCs, i.e. having an axon. In Figure S2 the authors do not differentiate between GAD2 and vGAT.

b. The viral tools used for ablating SC-projecting GABAergic neurons are not specific for the SC, but will also label very common collaterals to brain targets other than the SC including the thalamus (e.g. Ellis et al., 2016).

c. The shRNA approach to knock down vGAT expression removes vGAT from all types of vGAT-expressing retinal neurons, not only RGCs. It is very likely that vGAT-expressing amacrine cells are affected by this manipulation.

d. Please remove the claims that the behavior is mediated through the PBGN pathway. The transsynaptic HSV approach to label multisynaptic targets of GABAergic RGCs does not support this claim. It is unknown whether the axon terminals in the PBGN labelled in these experiments stem from the SC. Also, other SC-targets that are known to mediate escape, such as the PAG (Evans et al. 2018), are also labelled in these experiments.

2) Inadequate test of visual circuitry function. The approaches used by the authors to test for different aspects of visual processing focus on a few known reflex pathways, but do not directly test for thalamic/cortical dependent visual behaviors, i.e. image formation. This needs to be changed in the description of the tests and the interpretation of the results. The description in the figure itself is good, but the conclusions drawn are misleading. The authors use four different approaches to test for visual function and draw the following conclusions:

a. Looming-evoked escape is decreased in two experimental conditions where vGAT-expressing neurons are impaired. The authors conclude that GABAergic RGCs projecting to the SC mediate escape. As described in point 1, these experiments are not specific enough to make those claims.

b. Electroretinograms (ERG) have unchanged a- and b- waves, which leads to the claim that GABAergic RGCs are not necessary for normal retina function. This is misleading as the largest contributors to an ERG signal are the photoreceptors and bipolar cells (e.g. Smith, Wang ... and Trembley, 2014).

c. Optokinetic reflex is unchanged after vGAT ablation. The authors conclude from these experiments that image formation is independent of GABAergic RGCs. This approach only tests for very specific retinal projections, probably to the AOS, but does not test for the function of the LGN-cortex projections, which form the major image formation pathway.

3) Insufficient data presentation. The currently presented histological sections are not sufficient to draw the same conclusions as the authors. In addition, several of the experiments lack clear quantifications to back up the claims in the text. The authors need to provide complete and readable pictures, and add quantifications to support their claims.

a. The role of PV+ SC neurons in the present study is unclear. The authors do not provide adequate evidence that GABAergic RGC-recipient neurons in the colliculus are PV+ (line 196). The referenced figure (Fig. 4B) shows only a single example of a staining. Quantification of the % of labeled neurons that are PV positive is required to strengthen this claim.

b. Please provide complete images of the histology at a readable size for all figures and add outlines of brain areas where necessary. Importantly, in Fig. 1G it looks as if the RGC axon terminals are only present in the intermediate layers of the medial SC. Since it is claimed that the GABAergic RGCs include many different types, one would expect axon terminals across all depths of the superficial SC.

c. The re-analysis of the published scRNA results from Rheaume et al 2018 should be made clear in the manuscript. Currently there is no information in the main text about the underlying data set or analysis.

d. It is not clear in the text what the differences/similarities are between vGAT- and GAD2-Cre mouselines. Please make clear in the narrative and conclusion how each mousseline was used.

Reviewer #2:

In this study, Luo et al. report that GABAergic retinal ganglion cells projecting to the superior colliculus (spgRGCs) drive defensive responses to looming. Previous studies demonstrated that neurons in the superior colliculus (SC) mediate behavioral responses to looming. Most of the >40 ganglion cell types in mice project to SC. Which of these convey the relevant looming signals from the retina is unclear. Most ganglion cells express VGLUT2 and release glutamate from their axon terminals, but anatomical evidence suggested that a subset of ganglion cells may contain GABA. Furthermore, a recent study (Sonoda et al., 2020) showed that some intrinsically photosensitive retinal ganglion cells are labeled in Gad2-Cre mice and reduce the light sensitivity of photoentrainment and pupillary light responses.

Here, Luo et al. find that intravitreal injections of Cre-dependent adeno-associated virus (AAVs) reporters in Vgat-Cre and Gad2-Cre transgenic mice label ganglion cell axons in many retinorecipient brain areas, including SC. The authors reanalyze a published single-cell RNA sequencing dataset (Rheaume et al., 2018), which suggest that subsets of ganglion cells of most types express Gad2. Using optogenetics, the authors confirm that activation of Gad2-Cre- and Vgat-Cre-positive ganglion cells elicit inhibitory postsynaptic currents (IPSCs) in SC neurons. Based on retrograde tracing, the authors suggest that these ganglion cells belong to a variety of types. Next, Luo et al. demonstrate that the deletion of spgRGCs abolishes defensive responses to looming stimuli and looming-evoked cFos expression in SC. The authors illustrate the selectivity of these effects by showing that electroretinograms, optomotor responses, and pupillary light responses are unaffected by spgRGC deletion. Finally, the authors use an AAV-based shRNA strategy to knock down Vgat in the retina and show that this abolishes looming responses.

Overall, this study reports a surprising and potentially transformative finding (i.e., that a small subset of many RGC types uses GABA to drive looming responses in SC and behavior). The authors leverage a wide range of techniques to study spgRGCs, but some results and interpretations are confusing, and some conclusions are insufficiently supported evidence.

Specific comments:

1) The Vgat knockdown experiments are critical to show that GABAergic transmission matters. The current strategy targets all Vgat-expressing neurons in the retina. The vast majority of these are amacrine cells. Silencing amacrine cells will likely have widespread effects among ganglion cells. The authors should use a dual AAV strategy similar to the one they employed for DTA to restrict Vgat-shRNA expression to spgRGCs and show that ganglion cells' responses to looming are unchanged.

2) Previous studies show that activation of SC neurons (particularly PV+cells) promotes defensive responses to looming, and the cFos labeling in this study suggest that spgRGCs activate SC neurons. Yet, optogenetics experiments indicate that spgRGCs elicit IPSCs in SC neurons. These findings seem at odds. Although the authors show that some spgRGCs elicit a mixture of EPSCs and IPSCs, the Vgat knockdown experiments suggest that the GABAergic transmission mediates looming signals and elicits behavioral responses. The authors should characterize looming responses in SC by electrophysiology or optical recordings (as they have done in previous studies) to clarify the contributions of spgRGCs.

3) Details of the cFos experiments were missing. The authors should compare cFos labeling and changes in cFos labeling after spgRGC ablation between looming and other visual stimuli, to discern the specificity of these effects.

4) The characterization of spgRGC types is superficial. The authors should show patch-clamp recordings from a small number of RGCs, which seem to encompass a variety of types. The authors should record light responses characterization (incl. responses to looming stimuli) and reconstruct the morphology of a larger number of ganglion cells to classify types in line with other studies (e.g., Bae et al., 2018, Reinhard et al., 2019).

Reviewer #1:

The goal of this study is to identify the retinal ganglion cells that mediate the flight response of mice to a looming stimulus. The candidate they focus on are a subset of RGCs that release GABA at synapses with a particular subtype of neuron in the SC that was previously implicated in this behavior.

The impact of the paper is limited for two main reasons. First, there was a paper using a similar mouse line that was just published (Sonoda et al, Science 2020) that revealed that GABAergic intrinsically photosensitive RGCs shape several of the non-vision forming behaviors in mice (such as photoentrainment of circadian rhythms and the pupillary light reflex). The authors may not have been aware of this work when they submitted this paper but now that it is published, the authors need to more rigorously compare their results to that study.

Second, it is not at all clear that the authors have identified a subtype of RGCs that mediate the looming responses. Rather their data (particularly Figure 3) seems to argue that a lot of different RGC subtypes have GABA. So the model is that the 13% of multiple RGC subtypes project to PV cells in the SC and together they mediate the looming response?

Finally, there is a lack of quantitative description of many of the experiments that undermines many of the conclusions the authors want to make. These are described explicitly below.

1) The authors make use of both a GAD2-Cre and vGAT-Cre to label cells in the retina, apparently the results from the two lines are combined throughout the paper. The authors need to verify that the same cells are labeled for each line.

2) In Figure 1, the authors show beautiful images of their labeling but the quantification of RGCs that express GABA is not described. In the mouse retina 50% of the cells in the ganglion cell layer are amacrine cells. They do show some labeling in the optic nerve so clearly some RGCs are labeled but there is no way to know how many. Rather the authors rely on a re-analysis of an RNA-seq data set to estimate that 13% of RGCs across all subtypes! Of course, protein levels and not transcripts are what matter for this sty so at least a co-stain for a RGC marker would strengthen the finding. This would also resolve the issue brought up in point 1 above.

3) Figure 2. The authors use optogenetics to characterize the synaptic connections with target neurons in the SC. Again, there is a surprising lack of quantification. In Figure 2C they show light activation ChR induces an inward current but they don't say how many times they do that experiment. Most experiments are done in TTX + glutamate receptor blockers to isolate GABAergic currents but there is a subset in which the igluR blockers are absent and excitatory currents were detected. The authors need to clarify in what percent of neurons did they see GABAergic currents and in what percentage excitatory currents and in what percentage did they see both? Basically, the authors need to clarify if these RGCs are releasing both GABA and glutamate. This is critical for interpreting the experiments in which they kill this population of neurons and inhibit the behavior.

4) Figure 3. The authors use retrograde labeling to begin to identify the GABAergic RGC subtypes that project to SC. Again, the quantification is lacking - what percent of SC projecting cells were positive for GABA? It is really a confusing result because they find an array of RGC subtypes that seem to express GABA. Hence it does not appear that one type of RGC projects to SC but rather all types - but just the subset that release GABA along with glutamate. 5) Figure 4AB appears quite impressive but the logic is not clear. Does Herpes simplex virus work as an anterograde transsynaptic virus? More explanation is required. Again, there is no quantification of the results - just examples of single neurons found in several retinorecipient brain regions.

(Note: Figures 4C-G are impressive - killing this subpopulation of cells seems to eliminate the response to looming stimuli while other visually guided behaviors are retained.)

6) Figure 5H - this is a difference with the Sonoda paper - they find an effect on PLR when they reduce GABA release from ipRGCs.

7) Figure 6 - the authors use RNAi to reduce vGAT expression in spgRGCs and this also impacts behaviors. There are many controls that need to be done here primarily showing the glutamate release is normal. Otherwise this could just be a synaptic transmission deficit.

Preprint Review

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Summary:

This study reports that a small subset of different RGC neuron types that release GABA at synapses with a particular class of neurons on the super colliculus mediate the looming responses in mice. This result is potentially highly significant and as noted by one reviewer, potentially transformative in our thinking of how RGC cell types mediate behaviors. However, all three reviewers agree that many of the conclusions are insufficiently supported by the evidence. The reviewers offer many details for necessary experiments and clarifications that need to be made in order for the authors to be able to reach their conclusion.

Reviewer #3:

The bHLH transcription factor Atoh7 has been studied as a critical regulator of retinal ganglion cell (RGC) generation in several species but, as the authors detail in the Introduction, it is not clear how or at what stage it acts. For example, some (most) data suggest it is required to specify the RGC fate in precursors, while other data suggest it may be required for RGC differentiation and/or survival following their generation. Here, Brodie-Kommit et al. use a well-established method to distinguish these possibilities, deleting Atoh7 in the absence of Bax, a powerful proapoptotic gene. Both naturally occurring and genetically-provoked apoptosis of many neuronal types, including RGCs, have been shown to be prevented in Bax mutants, which are viable and generally healthy.

The authors show that RGCs survive and are functionally normal in the absence of both Atoh7 and Bax, but few axons leave the retina, so of course light-induced behaviors are greatly decreased. Single cell RNAseq demonstrates a delay in RGC differentiation in the absence of Atoh7 (with or without Bax) and a variety of gene expression changes.

As expected for a paper from two superb laboratories, the work is done to the highest standard and uses the best available methods. The result that blocking apoptosis rescues RGCs in the absence of Atoh7 is important and should help resolve controversies about its role, providing a strong argument against what is likely still the best-accepted model.

On the other hand, the paper does not go far beyond that simple result: it shows what Atoh7 does not do, but not what it does do, either to the RGCs that express it or to the RGCs that do not express it but nonetheless require it for survival. The physiological and histological data largely back up the survival result; the behavioral defects are sort of trivial once one knows that RGC axons fail to reach the brain; and the RNAseq data do not lead to substantial novel insights that shed light on either the presumably cell-autonomous or the clearly cell-nonautonomous mechanisms.

Reviewer #2:

In the present manuscript the authors reveal that RGC differentiation is largely rescued in the absence of Atoh7 when the pro apoptotic gene Bax is also removed in the developing retina. These rescued RGCs show some proper physiological responses but fail to develop proper connections to the brain. Retina vasculature is also affected by the absence of Atoh7 even when RGCs are "rescued". Finally by single cell analysis they reveal that Atho7 is required for proper timing of RGC differentiation but the expression of major markers for RGC can be independent from Aoh7 transcriptional activity. The paper is based on a series of very elegant genetic experiments and the single cell analysis is particularly illuminating in this context.

Major Points:

Cell death is only one of the RPC possible fates in the absence of Atoh7. Indeed the author and a vast amount of literature showed that in the absence of Atoh7 more adopt photoreceptor precursor fate among others. Is the block of apoptosis by Bax inactivation reducing this "ectopic differentiation phenotype" in addition to RGC fate restoration?

Linked to the previous point, does the single cell data reveal why some progenitors die in the absence of Atho7 while others change fate?

The authors should discuss this point in more detail.

Reviewer #1:

This manuscript challenges the notion that the transcription factor Atoh7 is required to confer neurogenic retinal progenitors the competence of generating retinal ganglion cells (RGCs), the first-born neurons of the retina. This idea is based on the evidence that Atoh7 inactivation in mice causes the loss of the majority of RGCs. Here the authors have generated a Atoh7Cre/Cre;Bax-/- mouse line to ask what happens if apoptotic cell death is prevented in Atoh7 null mice. Using a number of RGC markers, they show that in the adult retina a large number of RGCs are no longer lost and are functionally connected with other retinal cell types as the retinas generate light driven photic responses. However, the RGCs of the Atoh7Cre/Cre;Bax-/- mice cannot connect with brain targets as the axons (when present) do not exit the optic disk but grow in a disorganized manner within the fibre layer. As an additional feature, the hyoloid artery does not regress. In Atoh7Cre/Cre;Bax-/- embryos, RGC generation is delayed as determined by analysis of single cell RNA-seq. The authors conclude that Atoh7 is required for RGC survival but dispensable for their specification.

This is an interesting study that adds up to the existing literature related to the role of Atoh7 in RGC generation/differentiation. However, the conclusion seems rather stretched: do the cells generated in the absence of Atoh7 and Bax really have a (full) RGC identity as claimed in the title? Is the specification of ALL RGC really independent of Atoh7? Conclusions should be toned down and alternative interpretations should be offered. Indeed, preventing apoptosis does rescue the full number of RGCs (see for example melanopsin positive cells). The lack of Isl1 in Fig. 4 and the low number of Brn3a+ cells in Fig. S6 is rather striking and suggests more than a delay. Thus, at least a subset of RGCs seems to require Atoh7, likely early born RGCs. There are several studies indicating that RGCs secrete factors that regulate their own number (GDF11, Kim et al., 2005, Science, as an example). Lack of this feed-back at early stages may favour the generation of RGCs that are not full Atoh7-dependent, creating an imbalance between Atoh7-dependent (early) and Atoh7-independent (late) RGCs.

The second problem that remains unanswered is related to the "identity" of the RGCs present in Atoh7Cre/Cre;Bax-/- embryos. Are they really bona fide RGCs? These cells cannot connect properly with their brain target nor secrete the putative factors needed to induce hyaloid artery regression. These defects could perhaps be explained by asynchrony (cells are generated late to read the axon guidance cues, for examples) but they may also be interpreted as lack of full identity.

The authors need to consider these possibilities and further address the related points below:

1) The difference in cell number detected with RBPMS and Isl1 is puzzling (Fig. 1). Isl1 recognises RGCs but also amacrine cells, which should be increased in absence of Atoh7. How do the authors explain that Isl1+ cells are less than the RBPMS+ ones in Atoh7Cre/Cre;Bax-/- mice.

2) The sentence "Brn3b-positive ipRGCs differentiate normally in the absence of Atoh7" is an overstatement. Only 35% of them do, the others are presumably lost. Furthermore, the presence of a cell specific marker does not ensure that the cells are fully differentiated.

3) Line 435. Presumably a sentence describing the response of RGC in Atoh7Cre/Cre;Bax-/- is missing.

4) Lines 506-509. Failed vasculature regression: the authors state "...implies that Brn3b and Isl1 may activate expression of secreted factors that drive vascular regression". If this is the case why in Atoh7Cre/Cre;Bax-/- retinas the hyaloid artery is still present? The retinas do express levels of Isl1 and Brn3b so that these factors should be present.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

The three reviewers agree that the study is very elegant and well performed. However, they also find that the conclusions are rather stretched and there is no clear demonstration of what Atoh7 is needed for. Major concerns relate to the real identity of the rescued cells and the claimed independence of RGC specification from Atoh7. Unfortunately, the RNAseq data do not illuminate this issue or solve the cell-autonomous and non cell-non-autonomous mechanisms that are at the basis of the present observations.

Reviewer #2:

The focus of this paper is the zinc metalloprotease ADAMTS-5. This protein has received attention as a therapeutic target for the treatment of degenerative joint diseases such as osteoarthritis. The primary effort is devoted to the development of non-zinc chelating exosite type inhibitors. The authors have previously identified exosites in hypervariable loops that are required for or proteolysis of both aggrecan and versican. Targeting these sites with the hope of selectivity is certainly a good approach. The authors used the glycosaminoglycan (GAG) feature of substrates to build in exosite affinity. To this end the authors probed ADAMTS-5 with a small library of GAG-mimetic glycoconjugated arylsulfonamides.

With some minimal SAR, the authors were able to achieve some selectivity of ADAMTS-5 over ADAMTS-4 and some increase in potency over other inhibitors they have developed. They report IC50 values with the most potent (molecule 4b) at 9.4±2.8 µM. Some further SAR to more fully understand exosite binding (4b did not inhibit a peptide cleavage assay) did not lead to a more potent inhibitor. Further characterization of 4b inhibitory activity was carried out looking at synergism with a known zinc chelating inhibitor and some molecular docking studies. The docking studies led to experiments mutating residues that were thought to involve inhibitor binding. The results largely supported the in silico predictions.

Overall the reported results advance the idea that selective inhibitors of ADAMTS enzyme that are not dependent on zinc coordination are possible; however, in the absence of more detailed studies of inhibition in cells and potentially in animals it is not possible to say how important and influential molecules such as those described here will be on sorting out complicated in vivo physiology. The potency reported for 4b suggests significant optimization would be needed before in vivo significance could be assessed.

Reviewer #1:

This study pursues the development of ADAMTS-5 protease inhibitors by screening compounds linking a glycan (GlcNAc) with an arylsulfonamide, using click chemistry as the tether contains a triazene. ADAMTS-5 is a metalloprotease that has been implicated as a drug target for osteoarthritis. In prior work, this lab has identified exosites in ADAMTS-5 that can contribute to substrate recognition and processing. Here they identify a hybrid compound, 4b, that can block the protease activity of ADAMTS-5 with 9 µM potency. Using docking, they implicate several Lys residues that might confer interaction and show that potency of 4b is reduced with ADAMTS-5 mutants. Overall, compound 4b may bind as predicted although no additional experimental structural studies are performed to validate binding mode. While the study is a solid but limited medicinal chemistry effort, it is not felt that this manuscript will be of broad interest.

-The compound 4b potency is still rather weak relative to other previously published agents which show sub-µM potency. 1) Biochem J paper (2016) from this lab and BBRC (2016) from a Japanese lab reported antibodies that blocked ADAMTS-5 in the low nM range and worked in human chondrocytes. 2) Thiazolidine-diones (sub µM) were reported as cell active ADAMTS-5 inhibitors (Eur J Med Chem 2014). 3) Acylthio-semicarbazides are sub-µM ADAMTS-5 inhibitors (Eur J Med Chem 2013) although also target ADAMTS-4 more weakly, and showed selectivity against other metallohydrolases.

-Compound 4b was not used in a cell-based let alone animal model to analyze its pharmacological effects or promise. It is thus not clear how compound 4b stacks up to earlier agents. Compound 4b is a rather large compound for advancing clinically.

-No new insight into ADAMTS-5 biological function was gained here.

Preprint Review

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Author Response

Reviewer #1:

In this manuscript, Cobb and colleagues report on the biochemical and functional characterization of redox active ER proteins in the malaria parasite Plasmodium falciparum. They studied a protein called PfJ2, which contains HSP40 J and Trx domains and is homologous to human ERdj5. Using the TetR-PfDOZI aptamer system to tag PfJ2 and conditionally regulate its expression, they show that PfJ2 is localized in the parasite ER and is essential for parasite growth during the asexual blood stages. Using co-immunoprecipitation combined with mass spectrometry, they identify partner proteins of PfJ2 including other ER proteins such as PDI and BIP. Using a chemical biology approach based on DVSF crosslinker, they document the redox activity of PfJ2 and identify redox substrates of PfJ2, which include PDI8 and PDI11 protein disulfide isomerases. They further functionally characterized PDI8 and PDI11 using the glmS ribozyme for conditional knockdown. These experiments confirm that PDI8 and PDI11 are partners of PfJ2 and show that knockdown of PDI8 impairs parasite blood stage growth. Finally, the authors show that inhibitors of human PDI inhibit parasite growth (at best in the micromolar range) and block the redox activity of PfJ2 and parasite PDI.

This is an interesting study combining genetic and chemical biology approaches to investigate an understudied compartment of the malaria parasite. The manuscript is clearly written and the work technically sound. In summary, this study illustrates that ER redox proteins in the malaria parasite perform similar functions as in other organisms. The main limitation of this study is that evidence showing that redox ER parasite proteins are druggable is rather weak. PfJ2 is very similar to human ERdj5 in terms of active redox site and function, and the authors used inhibitors that are active on human PDI. It thus remains uncertain whether an antimalarial strategy targeting such conserved pathways is achievable.

RESPONSE: We thank the reviewer for their appreciation of our work. While PfJ2 shares some similarity to human ERdJ5, we disagree that they are functionally similar. Our data show that, unlike ERdJ5, PfJ2 substrates are primarily other redox chaperones. In terms of the redox active site, our data clearly identifies a pathway that is targeted by a small molecule inhibitor. There is a lot of precedence for targeting conserved pathways as an antimalarial strategy. For example, anti-translational and anti-proteasomal inhibitors are being widely studied for their potency as antimalarials (Baragana et al 2015 Nature; Li et al 2016 Nature; Wong et al 2017 Nat. Microbiol.; Kirkman et al 2018 PNAS; Stokes et al 2019 PLoS Path.), several proteases (with conserved active sites) are well known antimalarial targets (Sleebs et al 2014 PLoS Biol.; Nasamu et al 2017 Science; Pino et al 2017 Science; Favuzza et al 2020 Cell Host Microbe), and effective inhibitors targeting a parasite chaperone has been repurposed for antimalarial drug development (Lu et al 2020 PNAS). We thank the reviewer for recognizing that there is a long road ahead of us to develop a more specific inhibitor for PfJ2, however, that is beyond the scope of this study.

In addition, a number of specific points should be addressed to improve the quality of the manuscript:

Although PDI8 and PDI11 gene edition were performed in the PfJ2apt line, the authors did not attempt to knockdown both PfJ2 and PDI8/11 simultaneously (because PfJ2 is essential). Therefore, referring to "double conditional mutants" is misleading.

RESPONSE: We are open to alternative ways to refer to these mutants. Since we have orthogonal systems for knockdown of two proteins, we refer to these as double conditional mutants.

The authors should provide details on the parasite lysis conditions used for the co-IP experiments to identify interacting proteins (Table 1) and redox partners (figure 3). In their proteomic analysis, the authors considered proteins with a 5-fold increase in the specific versus control conditions. A more stringent analysis would retain only proteins identified exclusively in the modified J2apt line.

RESPONSE: We will include this in a new version. We agree that a more stringent analysis would lead to fewer proteins being identified, however, it also runs the risk of missing real interactors. We chose to use a 5-fold cutoff based on previously published work (Boucher et al 2018 PLoS Biol; Florentin et al 2020 PNAS).

In figure 6, the authors should probe the blots for a control protein that is not co-immunoprecipitated with PfJ2 or PDI8. In Supplementary fig 4, control untreated parasites should be analyzed in parallel to GlcN-treated parasites.

RESPONSE: We will do this once our labs reopen after the pandemic.

The partial reduction of protein levels (Fig S4) shows that the glmS system is not very efficient here, which might explain why there is no phenotype in the PDI11 mutant (Fig5B). This questions the conclusion that PDI11 is dispensable.

RESPONSE: We agree and we state that “These results...suggest that PfPDI11 may be dispensable... conclusions are supported by a genome-wide essentiality screen performed in P. falciparum” (Lines 319-322). We will add more discussion to explain this result.

Reviewer #2:

The claim here is of having discovered a druggable cellular process in P. falciparum, one that opens the door to therapeutic intervention in the most deadly form of malaria.

The study commences with a focus on what appears to be the Pf homologue of a eukaryotic protein disulphide isomerase, known to many as ERdJ5 and referred to here as PfJ2. Its cellular contingents were identified by cross-linking and pull down, it’s (predicted) thiol reactivity explored with agents that react with reduced thiols and it’s functional importance to parasite fitness (in the lab) explored by gene knockout. These experiments provide evidence that PfJ2 and it’s associated Pf PDIs engage in thiol redox chemistry in the ER of the parasite and that integrity of this biochemical process is important to viability of the parasite.

Lacking all expertise in molecular parasitology, this reader is unable to judge the specific significance of these findings to the field nor indeed the extent to which these are hard-won discoveries.

RESPONSE: We are gratified to note that the reviewer is cognizant of their limitations and their ability to judge the significance of this work.

However, from the perspective of the fundamentals of ER redox chemistry the findings represent a modest advance, showing that what is true of yeast and mammals is also true of Apicomplexa. The important mystery related to the juxtaposition of a J-domain and thioredoxin domains in PfJ2, remains.

The most important claim however is the one with translational potential, namely that one might be able to discover (electrophilic) compounds that, despite the monotony of shared chemical features of thiol chemistry, will nonetheless possess sufficient specificity towards this or that malarial protein to be converted one day to a useful drug. However, in regards to this important point the authors offer very little in the way of evidence how and if this might be achieved.

RESPONSE: We disagree. The work does not reconfirm the ‘fundamentals of ER redox’ chemistry. There is no work, in any system, that has shown that PfJ2-like proteins act as reductases for PDIs. In fact, as we state in the paper, in other model systems, there is a lot of redundancy built in the ER redox systems and PfJ2-like proteins work with specific clients like SERCA pumps or LDL receptor. Thioredoxin domain proteins in the ER of other eukaryotes have not been shown to work with each other or other chaperones. Furthermore, our data actually does suggest a reason why the J-domain is juxtaposed to thioredoxin domains. It recruits BiP to the mixed disulfides formed by PDIs. This insight would not have been possible in other systems because of the redundant redox mechanisms. In terms of the translational aspect, this work identifies an essential, pathway and a starting point for developing better inhibitors. As the reviewer may be aware, once a starting drug-like molecule has been identified, one has to embark on a medicinal chemistry program to develop more potent inhibitor. However, this is beyond the scope of this manuscript.

Therefore, the main conclusions to draw from this paper are that ER-localised thiol chemistry is also important in malaria parasites and that, assuming one were able to explore localised context-specific features of thiol reactivity in malarial proteins, it may one day be possible to develop anti-malarial drugs that exploit this as a mechanism of action. The generic nature of these considerations limits the significance of the conclusions one might draw from this paper.

RESPONSE: We are disappointed that we were unable to satisfy the reviewer’s need for ‘a giant leap for mankind’ insights.

Reviewer #3:

This paper describes redox-active proteins in the ER of malaria parasites. The authors start out with PfJ2, a J- and Trx-domain containing protein. They find that it is an essential ER protein that interacts with other chaperone and Trx domain proteins. Using a crosslinker with specificity for redox-active cysteines they identify PfPDI8 and PfPDI11 as redox-partners that together may aid folding of other proteins in the secretory pathway. Finally the authors use inhibitors that act on human PDIs and show that they inhibit parasite growth, albeit at rather high concentrations. This may be fortunate as this suggests different specificities for host and parasite PDIs. However, it also means that from this work it is difficult to judge if the parasite PDIs can be specifically targeted.

RESPONSE: We thank the reviewer for recognizing the important insights gained from this work. We agree that the specific inhibitor identified is not an ideal antimalarial. There is a lot of precedence in the field for antimalarial inhibitors that target conserved mechanisms such as protein translation (Baragana et al 2015 Nature; Wong et al 2017 Nat. Microbiol.), aspartic proteases (Sleebs et al 2014 PLoS Biol.; Nasamu et al 2017 Science; Pino et al 2017 Science; Favuzza et al 2020 Cell Host Microbe), the proteasome (Li et al 2016 Nature; Kirkman et al 2018 PNAS; Stokes et al 2019 PLoS Path.), the TRiC chaperone complex (Lu et al 2020 PNAS) etc. We are starting a medicinal chemistry program to identify more potent inhibitors of these redox chaperones. However, that is beyond the scope of this paper.

This is an interesting paper and rightly emphasises that it addresses a much understudied process and organelle in the parasite. The DVSF-crosslinking and the knockdown cell lines are highlights (although the knockdown cell lines were not fully exploited). The paper covers a lot of ground. However, this comes at the cost of depth. The actual function of the studied proteins on folding of other proteins and on the state of the ER was not evaluated and it is also not clear if the human PDI inhibitors indeed target the parasite enzymes. The high concentrations of inhibitors needed to show an effect on DVSF-crosslinking might indicate a secondary effect due to loss of parasite viability. As a result it is not fully clear if the studied proteins are indeed critical for folding of relevant substrates and if this process is druggable. More work is needed to support the main conclusions of the paper.

RESPONSE: We thank the reviewer for appreciating the diverse toolsets used here to gain important insights into the ER of malaria-causing parasites. Due to the short time-frame of the DVSF-crosslinking experiment (30 mins vs 48h life cycle), we are able to conclude that the effect of the drug is not secondary. A new version will clarify this.

Major points:

1) The authors describe conditional knockdown lines and find that PfJ2 and PfPDI8 are essential but these lines are not further exploited for functional studies. Did the knock downs have any effect on proteins they mention as potential substrates (Table 1)? Did it affect the state/morphology of the ER? Did knock down of PfPDI8 remove/shift one of the PfJ2 bands after DVSF-crosslinking, as would be expected? Is there an effect on BiP? A general folding problem in the ER with such a lethal phenotype might have profound effects on the morphology of the organelles receiving protein from the ER. What happens to other cellular markers after knock down of these proteins? Were the knock down cells analysed by EM? Was there an effect on protein export? As it stands the knock down data does not show a role of the complex in the folding of any type of substrate and the function in oxidative folding, as indicated in the title, remains tentative.

RESPONSE: The morphology of the ER is difficult to address due the fact that in these lifecycle stages the ER is quite condensed. Further, the ER is not clearly identifiable via EM. The knockdown of PDI8 is not complete, therefore, it is not possible to perform the suggested experiment as we will always see the residual PDI8 crosslinked with PfJ2. We are not sure what or if there’s any effect on BiP upon knockdown of PfJ2. BiP does not crosslink with PfJ2 and its expression levels do not change. We are not sure what other effect the reviewer expects on BiP. The co-IP data show that BiP is part of a complex with PfJ2 and PDI8, this complex has not been previously observed in the ER of any organism. Since the parasites die during the trophozoite/early schizont stages, several of these organelles such as Rhoptries, micronemes etc probably do not form. Once the lab reopens after the pandemic, we will test for the presence of these organelles via immunofluorescence microscopy as well as EM. Similar experiments could show an effect on protein export. However, since we didn’t identify any exported proteins to be putative substrates of PfJ2 (despite the expectation that chaperones are sticky and bind everything), and therefore, any effect we observe is likely to be indirect. Given the published data establishing the function of PDIs as oxidative folding chaperones, their high degree of conservation, and in vitro characterization, we conclude that they function in oxidative folding. Furthermore, we show that PfJ2 regulates the function of Plasmodium PDIs as well as recruits BiP to the mixed disulfide complex. BiP is a highly conserved chaperone that has clear function in protein folding. Based on this and the data presented here, we conclude that PfJ2 functions as a regulator of oxidative folding in P. falciparum.

2) While I like the idea to use established commercial drugs as novel potential antimalarials, those used here are specific for non-infectious human diseases and target the host which is not a desirable property. Considering this, their rather low activity against the parasite can be taken as a positive result. However, the low activity is less convincing to establish the folding pathway in the parasite ER as a drug target. Beside the issue that it is unclear if indeed oxidative folding is the essential function of the PfJ2 complex (see previous point), the data in Fig. 7 does not clearly establish that this function is targeted by the inhibitors used. The effect is only seen at concentrations of 5xIC50. It is possible that this severely reduced viability which could be a non-specific reason for the lack of DVSF-crosslinked products. This needs to be examined in more depth. For instance, is the crosslink still seen after equivalent treatment of cultures with 5xIC50 of other unrelated drugs? Were other, unrelated processes unaffected? What was the effect of exposure to the drug on the ER and parasite morphology? Was the appropriate parasite stage affected? Can it be tested how fast exposure to 5xIC50 of the drug kills the parasites (at least morphologically, but preferably also by more specific means)?

RESPONSE: We agree that the drugs identified here are not ideal antimalarials but rather they are starting molecules for a larger medicinal chemistry program, that is beyond the scope of this manuscript. While we see significant loss of DVSF crosslinking (for PfJ2) even at the IC50, the relationship between protein activity inhibition and parasite death isn’t always linear. We are testing analogs of 16F16 to identify more potent inhibitors of these proteins. We thank the reviewer for the suggested experiments, and when the pandemic is no long limiting access to the lab, we will perform some of these.

3) While generally sound, a few experiments would have benefitted from more controls. A reducing sample from the same parasites for Fig. S7 (loaded a couple of lanes away to avoid interference of the reducing agent) would have been nice for comparison to show specificity of the higher molecular weight adducts. Detection of a control protein not expected to co-purify (for instance a cytosolic protein or a membrane-bound protein to control for residual parasite material) would have been appropriate for the co-immunoprecipitations (e.g. Fig. 6A,D, Fig. S9).

RESPONSE: We show that there are no non-specific bands for PDI11, because when we mutate the cysteines, we do not observe any cross-linking. We will include the control proteins for the co-IPs, they were not included for the sake of clarity.

Reviewer #3:

This paper describes redox-active proteins in the ER of malaria parasites. The authors start out with PfJ2, a J- and Trx-domain containing protein. They find that it is an essential ER protein that interacts with other chaperone and Trx domain proteins. Using a crosslinker with specificity for redox-active cysteines they identify PfPDI8 and PfPDI11 as redox-partners that together may aid folding of other proteins in the secretory pathway. Finally the authors use inhibitors that act on human PDIs and show that they inhibit parasite growth, albeit at rather high concentrations. This may be fortunate as this suggests different specificities for host and parasite PDIs. However, it also means that from this work it is difficult to judge if the parasite PDIs can be specifically targeted.

This is an interesting paper and rightly emphasises that it addresses a much understudied process and organelle in the parasite. The DVSF-crosslinking and the knockdown cell lines are highlights (although the knockdown cell lines were not fully exploited). The paper covers a lot of ground. However, this comes at the cost of depth. The actual function of the studied proteins on folding of other proteins and on the state of the ER was not evaluated and it is also not clear if the human PDI inhibitors indeed target the parasite enzymes. The high concentrations of inhibitors needed to show an effect on DVSF-crosslinking might indicate a secondary effect due to loss of parasite viability. As a result it is not fully clear if the studied proteins are indeed critical for folding of relevant substrates and if this process is druggable. More work is needed to support the main conclusions of the paper.

Major points:

1) The authors describe conditional knockdown lines and find that PfJ2 and PfPDI8 are essential but these lines are not further exploited for functional studies. Did the knock downs have any effect on proteins they mention as potential substrates (Table 1)? Did it affect the state/morphology of the ER? Did knock down of PfPDI8 remove/shift one of the PfJ2 bands after DVSF-crosslinking, as would be expected? Is there an effect on BiP? A general folding problem in the ER with such a lethal phenotype might have profound effects on the morphology of the organelles receiving protein from the ER. What happens to other cellular markers after knock down of these proteins? Were the knock down cells analysed by EM? Was there an effect on protein export? As it stands the knock down data does not show a role of the complex in the folding of any type of substrate and the function in oxidative folding, as indicated in the title, remains tentative.

2) While I like the idea to use established commercial drugs as novel potential antimalarials, those used here are specific for non-infectious human diseases and target the host which is not a desirable property. Considering this, their rather low activity against the parasite can be taken as a positive result. However, the low activity is less convincing to establish the folding pathway in the parasite ER as a drug target. Beside the issue that it is unclear if indeed oxidative folding is the essential function of the PfJ2 complex (see previous point), the data in Fig. 7 does not clearly establish that this function is targeted by the inhibitors used. The effect is only seen at concentrations of 5xIC50. It is possible that this severely reduced viability which could be a non-specific reason for the lack of DVSF-crosslinked products. This needs to be examined in more depth. For instance, is the crosslink still seen after equivalent treatment of cultures with 5xIC50 of other unrelated drugs? Were other, unrelated processes unaffected? What was the effect of exposure to the drug on the ER and parasite morphology? Was the appropriate parasite stage affected? Can it be tested how fast exposure to 5xIC50 of the drug kills the parasites (at least morphologically, but preferably also by more specific means)?

3) While generally sound, a few experiments would have benefitted from more controls. A reducing sample from the same parasites for Fig. S7 (loaded a couple of lanes away to avoid interference of the reducing agent) would have been nice for comparison to show specificity of the higher molecular weight adducts. Detection of a control protein not expected to co-purify (for instance a cytosolic protein or a membrane-bound protein to control for residual parasite material) would have been appropriate for the co-immunoprecipitations (e.g. Fig. 6A,D, Fig. S9).

Reviewer #2:

The claim here is of having discovered a druggable cellular process in P. falciparum, one that opens the door to therapeutic intervention in the most deadly form of malaria.

The study commences with a focus on what appears to be the Pf homologue of a eukaryotic protein disulphide isomerase, known to many as ERdJ5 and referred to here as PfJ2. Its cellular contingents were identified by cross-linking and pull down, it’s (predicted) thiol reactivity explored with agents that react with reduced thiols and it’s functional importance to parasite fitness (in the lab) explored by gene knockout. These experiments provide evidence that PfJ2 and it’s associated Pf PDIs engage in thiol redox chemistry in the ER of the parasite and that integrity of this biochemical process is important to viability of the parasite.

Lacking all expertise in molecular parasitology, this reader is unable to judge the specific significance of these findings to the field nor indeed the extent to which these are hard-won discoveries. However, from the perspective of the fundamentals of ER redox chemistry the findings represent a modest advance, showing that what is true of yeast and mammals is also true of Apicomplexa. The important mystery related to the juxtaposition of a J-domain and thioredoxin domains in PfJ2, remains.

The most important claim however is the one with translational potential, namely that one might be able to discover (electrophilic) compounds that, despite the monotony of shared chemical features of thiol chemistry, will nonetheless possess sufficient specificity towards this or that malarial protein to be converted one day to a useful drug. However, in regards to this important point the authors offer very little in the way of evidence how and if this might be achieved.

Therefore, the main conclusions to draw from this paper are that ER-localised thiol chemistry is also important in malaria parasites and that, assuming one were able to explore localised context-specific features of thiol reactivity in malarial proteins, it may one day be possible to develop anti-malarial drugs that exploit this as a mechanism of action. The generic nature of these considerations limits the significance of the conclusions one might draw from this paper.

Reviewer #1:

In this manuscript, Cobb and colleagues report on the biochemical and functional characterization of redox active ER proteins in the malaria parasite Plasmodium falciparum. They studied a protein called PfJ2, which contains HSP40 J and Trx domains and is homologous to human ERdj5. Using the TetR-PfDOZI aptamer system to tag PfJ2 and conditionally regulate its expression, they show that PfJ2 is localized in the parasite ER and is essential for parasite growth during the asexual blood stages. Using co-immunoprecipitation combined with mass spectrometry, they identify partner proteins of PfJ2 including other ER proteins such as PDI and BIP. Using a chemical biology approach based on DVSF crosslinker, they document the redox activity of PfJ2 and identify redox substrates of PfJ2, which include PDI8 and PDI11 protein disulfide isomerases. They further functionally characterized PDI8 and PDI11 using the glmS ribozyme for conditional knockdown. These experiments confirm that PDI8 and PDI11 are partners of PfJ2 and show that knockdown of PDI8 impairs parasite blood stage growth. Finally, the authors show that inhibitors of human PDI inhibit parasite growth (at best in the micromolar range) and block the redox activity of PfJ2 and parasite PDI.

This is an interesting study combining genetic and chemical biology approaches to investigate an understudied compartment of the malaria parasite. The manuscript is clearly written and the work technically sound. In summary, this study illustrates that ER redox proteins in the malaria parasite perform similar functions as in other organisms. The main limitation of this study is that evidence showing that redox ER parasite proteins are druggable is rather weak. PfJ2 is very similar to human ERdj5 in terms of active redox site and function, and the authors used inhibitors that are active on human PDI. It thus remains uncertain whether an antimalarial strategy targeting such conserved pathways is achievable.

In addition, a number of specific points should be addressed to improve the quality of the manuscript:

Although PDI8 and PDI11 gene edition were performed in the PfJ2apt line, the authors did not attempt to knockdown both PfJ2 and PDI8/11 simultaneously (because PfJ2 is essential). Therefore, referring to "double conditional mutants" is misleading.

The authors should provide details on the parasite lysis conditions used for the co-IP experiments to identify interacting proteins (Table 1) and redox partners (figure 3). In their proteomic analysis, the authors considered proteins with a 5-fold increase in the specific versus control conditions. A more stringent analysis would retain only proteins identified exclusively in the modified J2apt line.

In figure 6, the authors should probe the blots for a control protein that is not co-immunoprecipitated with PfJ2 or PDI8.

In Supplementary fig 4, control untreated parasites should be analyzed in parallel to GlcN-treated parasites.

The partial reduction of protein levels (Fig S4) shows that the glmS system is not very efficient here, which might explain why there is no phenotype in the PDI11 mutant (Fig5B). This questions the conclusion that PDI11 is dispensable.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Reviewer #3:

In this manuscript, Bohr et al examine how the pluripotent stem cell system of planarians responds to organ-specific damage. If and how the differentiation of specific cell types is dynamically regulated is a conceptually fascinating problem in planarians and in general stem cell research. The authors address this problem by comparing the stem cell response between a single-organ amputation (the pharynx) versus broad tissue loss (decapitation). Their findings indicate that only the removal of the pharynx triggers the increased differentiation of pharyngeal cell types, while the loss of non-pharyngeal tissues upregulates the differentiation of progenitors of multiple organs, but not the pharynx. Further, the authors implicate temporally restricted ERK signaling as a regulatory component in the differentiation of pharyngeal cell types. These observations are also important because they contrast with the previously proposed "target blind" model (LoCascio et al., 2017) that posits the differentiation of different cell types at constant relative proportions, with the rate of stem cell divisions as global production rate regulator. In contrast, the observations by Bohr et al provide further evidence for more flexibility and specificity within the planarian stem cell system ("target consciousness") in the sense of lineage-specific adjustments in the production rates of specific cell types.

That said, the manuscript generally suffers from an overly narrow focus. Important questions remain regarding the specificity of the stem cell response to pharynx amputation and multiple experiments lack important controls (see below). Moreover, the authors have overlooked that a "target conscious" progenitor response has already been demonstrated by the selective proliferation of protonephridial markers expressing neoblasts in response to protonephridial damage by RNAi (Vu et al., 2015).

Major points:

1) Specificity of the stem cell response:

The central premise of the paper is the selective amplification of pharyngeal progenitors in response to pharynx amputation. The authors conclude this based on i) an increase in the absolute number of foxA+/piwi-1+ cells in a specific area, while ii) de-capitation has no effect on the absolute number of foxA+/piwi-1+ cells in the same area. This approach is an insufficient demonstration of specificity, as the known phenomenon of wound-induced stem cell activation might also change the absolute number of specific neoblast subclasses and might do so in an injury-dependent manner.

To account for this important caveat, the authors need to i) quantify RELATIVE proportions of foxA+/piwi-1+ cells out of total piwi cells (or of total H3P+ cells) and ii) they need to include other organ progenitors in the initial analysis. The latter is also critical because the pharynx is a complex organ comprising descendants of multiple lineages (e.g., muscle, neurons, epidermis) and it is not clear whether the foxA+/piwi-1+ cells indeed serve as a singular origin of all constituting lineages (as assumed by the authors), or if they only provide a subset of pharyngeal cells with a rate-limiting role in pharynx assembly (e.g., pharyngeal muscle). In the face of such uncertainty, iii) the quantification of new cell incorporation into the pharynx versus other tissues via BrdU labeling would be necessary to address this caveat and to provide a global perspective on the specificity of the response independent of incompletely characterized marker genes.

In addition, the following experimental design problems need to be addressed or better documented, including:

• The authors provide insufficient methodological detail on progenitor quantifications, even though the entire manuscript rests on this assay. What are their criteria for scoring a piwi-1+ cell as double-positive for the often weak and noisy lineage labels? If done "by eye", was double-blind scoring used? Were all cells in a given Z-stack counted or only specific planes? If the latter, by which criteria were image planes selected for quantification? How were the specific specimens out of an experimental cohort selected for imaging/quantification? Though not necessarily a unique shortcoming of this particular study, these points simply need to be adequately addressed in order to rigorously support quantitative differences between experimental conditions (e.g., specificity).

• The authors appear not to distinguish at all between technical replicates (e.g., multiple specimens within an experimental cohort) versus biological replicates (independent experimental cohorts). This is significant, because i), the use of the standard error of the mean (SEM) that the authors employ throughout is not really an appropriate measure for a single biological replicate with 3 animals - the standard deviation (SD) would seem a more appropriate measure in this context (SD). ii), the number of worms quantified for each experiment is generally low (n=3 animals in Fig. 1, 3, 5, 6; n=5 animals in the rest of the figures) given the observed variability in the data (e.g., ~25-30 foxA+/piwi-1+ cells 3d after pharynx amputation in Fig. 1E versus 50 cells in figure 1H). Similarly, for kinetic experiments as in Fig. 1H or 2C, it is simply crucial to ensure that the error bars include the variation in response dynamics between multiple replicates due to the drift in the baseline fraction of H3P+ cells or varying staining efficiencies (e.g., different batches of animals on different days), rather than the technical variation in a single experimental cohort only. Please address these concerns by adding more specimens and a thorough description of the experimental design.

2) Timeline of pharynx regeneration: The pharynx regeneration timeline and associated events that the authors present are insufficiently supported by experimental data. The conclusion in line 215 "that proliferation in a critical window of 1 to 2 days after pharynx amputation produces a population of progenitors that are likely essential for pharynx regeneration" rests i) on the diagnosis of a "proliferative peak of FoxA+ stem cells that occurs after pharynx amputation (Figure 2C)" (line 202). However, rather than a "proliferative peak", Fig. 2C shows a broad "proliferative plateau" of FoxA+ stem cells between 6h and 3 days after amputation. Similarly, the foxA+/H3P+ quantification after pharynx amputation in Fig. 4G also displays a lack of a peak of foxA+/H3P+ from 1d to 2d after amputation. ii), the associated nocodazole experiments suffer from the fact that the authors did not quantify the impact of the drug on the abundance of foxA+/piwi-1+ cells during treatment intervals from 0-1d and 2-3d after pharynx amputation. Therefore, the authors cannot rule out that nocodazole treatment might have similar effects on the abundance of foxA+/piwi-1+ cells throughout the 1-3 d post-amputation time interval, with the more severe organ-level phenotype of the 1-2d treatment window being caused by some other effect of the drug (e.g., on the differentiation of another rate-limiting cell type for pharynx regeneration or, conceivably, inhibition of priming neuronal activity ). Similar concerns apply regarding the statement in line 242, "... a window 1-2 days after amputation in which activation of ERK signaling is important for pharynx regeneration." Here, i) the quantification of the end-stage phenotype of drug treatment during the 1-2d time interval (regain of feeding ability) is missing. ii) Similarly, the examination of the consequences of PD treatment on foxA+ expression in piwi-1+ cells in panel 4D-H employs drug soaking for 3 days, yet the corresponding end-stage phenotype of 3-day drug treatment is not shown. iii) the implications of ERK in pharynx regeneration are tentative. Even though the PD compound is initially correctly introduced as "MEK inhibitor", the authors subsequently switch to the factually wrong "ERK inhibitor" designation (e.g., line 358). Further, additional experimental evidence for the assumed Erk inhibition as the cause of the observed phenotypes would be desirable to rigorously support the conclusion.

These caveats need to be addressed if a cell biological timeline is to remain part of this manuscript.

3) Integration with the existing literature:

The authors need to better integrate their findings with the literature. First, they need to cite the findings of Vu et al, which explicitly demonstrated a specific increase in the fractional abundance of piwi-1+/protonephridial marker+ cells in response to RNAi-mediated damage to protonephridia (Vu et al., 2015). As such, this study already demonstrates the main point of Bohr et al., namely that the planarian stem cell system is capable of "target conscious" progenitor provision. At the very least, the authors should credit these results as additional evidence for their model. A further finding that they should discuss is the demonstration by LoCascio et al (LoCascio et al., 2017) that flank region cut-outs cause a significant increase in pharynx cell incorporation over baseline, despite the absence of injury to the pharynx. How do the authors reconcile the discrepancy between these data and their own? In general, the discussion would benefit greatly from a more explicit comparison between the "target blind" model versus their data, as well as a broader perspective on the regulation of stem cell homeostasis.

Reviewer #2:

Bohr, Shiroor, and Adler investigate how stem cells respond to the loss of specific tissues in planarians. The planarian stem cell population (neoblasts) are distributed throughout the planarian body and include pluripotent stem cells and a wide range of lineage-committed progenitor cells. How this heterogenous pool of cells behave post-injury or amputation is incompletely understood. The discovery of markers to label stem cell progeny have opened the door to investigate how stem cells respond to tissue loss. However, the anatomy of planarians makes it difficult to surgically remove or damage specific organs. The PI of this study developed an assay to remove the pharynx by "chemical amputation" to study the mechanisms underlying regeneration of this organ without drastically perturbing or injuring other tissues. Using this approach, this paper investigates how a well-defined population of FoxA+ progenitors respond to pharynx removal at early time-points during the regeneration. Their data suggest that stem cells are able to detect loss of the pharynx and respond by generating significantly more cells fated to become pharynx, whereas amputation of non-pharyngeal tissues does not have an obvious effect on pharynx progenitor specification dynamics. In addition, using pharmacological treatments, the authors show that cell proliferation and ERK signaling are required for the expansion of pharynx progenitors and cell differentiation. In contrast, other cell types in the planarian eye do not appear to require proliferation or ERK signaling, suggesting that stem cell responses "target blind" as suggested in a previous study, but are rather tuned to specific missing tissues.

This work has the potential to make a significant contribution to the field by advancing our understanding of how the planarian heterogenous stem cell population responds to the loss of a specific organ. However, the report is preliminary as presented. It appears that the authors performed many experiments a single time. In addition, description of the methods is insufficient. The authors need to chiefly demonstrate the reproducibility of the data and robustness of the observations.

Concerns:

1) The authors need to replicate experiments to increase the sample size for most experiments.

2) Details for imaging and quantification should be explicitly stated in the methods, and the reported cell count numbers should be normalized as appropriate for each set of experiments.

3) Although the authors mention "lineage-tracing" experiments (see minor comments), they do not perform DNA analog pulse-chase experiments to analyze a temporal progression and spatial localization of stem cells to FoxA+ progenitors after pharynx removal. The authors rely on PH3-staining in conjunction with FoxA, and supplementary experiments using the pluripotent stem cell marker tgs-1 (which was only examined at 1 dpa). Could the authors clarify what they think FoxA+ stem cells represent? Are these self-renewing pluripotent stem cells or lineage-committed progenitors? Can the authors get some insight by scanning their images of PH3+ cells expressing FoxA visibly undergoing metaphase? Are daughter cells uniformly FoxA+ as reflected in the model? At least in one of the cells shown in the nocodazole treated controls it appears that both daughter cells express FoxA (Figure 3). I suggest showing some higher magnification images to support the interpretations/conclusions. Others have posited (e.g., Rink, Chapter 2 of Planarian Regeneration: Methods and Protocols), that not every dividing cell may be a long-term self-renewing stem cell and whether transient amplifying cells exist or contribute to regeneration in planarians is unknown. Adler and Sánchez Alvarado (2015) discuss the role of transient states and how the transcriptional profiles change in response to regeneration. It wasn't clear to me how the authors think about these cells based on the limited number of experiments and analysis, and there are a few places where the terminology is inconsistent, especially in reference to proliferating ovo+ progenitors (P. 14). The authors need to be clear, and it might be helpful to illustrate their model in one of the early figures or to include it in the final model, which omits tgs-1 due to the limited number of experiments performed with this marker gene (Figure 7).

4) The pharynx is complex and there is no data to assess what the contribution of other progenitor populations might be. I don't think or think it is unlikely that FoxA+ progenitors are solely responsible for reconstructing the pharynx. The authors should examine how other progenitor populations behave during the process of pharynx regeneration by extending the timeline of progenitor cell analysis. This would reveal if there is fluctuation in progenitor dynamics as animals regenerate the pharynx or re-scale proportions after pharynx regeneration. For example, can the authors test if they are able to detect a contribution of neural progenitors to regeneration of the pharyngeal nervous system? And if so, when during the regeneration process does it take place in the context of their study?

Reviewer #1:

This manuscript explores how planarian stem cells respond to the loss of a specific organ: the pharynx. The previously proposed "target-blind" model of planarian regeneration (LoCascio et al. 2017) posited that stem cells do not respond directly to missing tissues, but rather replace missing cell types based on their normal rates of homeostatic turnover. In contrast, the authors of this manuscript suggest that planarian stem cells can sense and respond to the loss of specific missing tissues, using the pharynx as a case study. The authors conclude that planarians may use more than one mode of regeneration, depending upon the target being regenerated (eye vs. pharynx).

The question explored in this paper is of fundamental importance, and providing an alternative model by which planarian stem cells regenerate missing tissues should be of interest to a broad readership. Unfortunately, in its current form, the manuscript presents enticing preliminary findings, rather than robust experimental observations. Because the authors are attempting to refute a previously published model, it is critical that the data are clear and convincing. If not, these findings could be summarily dismissed without appropriate debate. If the authors can demonstrate that their results are robust across larger samples sizes and experimental replication, and address the major issues listed below, this manuscript would represent a significant contribution to our understanding of planarian regeneration.

Major Issues:

1) Throughout the manuscript, experiments were either not repeated, or the number of biological replicates was not reported. In most cases, it appears that experiments were done only once (with the exception of the drug treatments). Numbers of biological replicates and sample sizes should be explicitly stated and the data from different replicates reported for Figs. 1D-G, 2B-D, 3C, 3E-F, 4B, 4D-H, 5C-D, and 6A-E.

2) The authors do not sufficiently describe their methods for imaging and quantifying cells (Figs. 1E, 1G, 2C-D, 3F, 4E-H, 5D, 6B). The size of the area covered to collect these data is unclear. High-magnification images are shown: are these the areas that were imaged? If so, their results could be biased by choosing small regions of interest. Ideally, the authors should quantify more than one region per animal. Also, they do not describe the depth of the z-stacks collected or how these stacks were normalized/standardized across conditions. All their conclusions hinge on the quantification of progenitor populations in response to different amputation paradigms or chemical treatments, so the standards for imaging and quantification must be clearly reported.

3) Inappropriate statistical tests were used throughout. The use of multiple t-tests amplifies the chance of a Type I error and is especially problematic when up to 7 comparisons were made! The authors should use one-way ANOVA with multiple comparison corrections for all experiments with more than two groups.

4) Figs. 1D-E show that upon pharynx amputation but not head amputation, FoxA+ piwi+ pharynx progenitors increase. These data suffer from the quantification issues highlighted above: how the data were quantified is not sufficiently described, only 3 data points were taken (one per animal), the experiment appears to have been performed only one time, and the wrong statistical test was used. Rather than reporting the number of FoxA+ piwi-1+ cells counted, the authors should quantify the total number of doubly positive cells as a percentage of piwi-1+ cells, as was previously published (Adler et al. 2014). The authors also fail to specify whether the change observed between "3 dpa phx" and "3 dpa head" is significant, which is a material point.

5) Fig. 2D also suffers from the inadequate quantification practices described above. Ideally, FoxA+ cells should be quantified as a percentage of the H3P+ cells observed.

6) The authors use "stem cell", "progenitor", "stem cell progenitor", and "progenitor stem cells" in a mixed and confusing way throughout the paper. For example, in lines 174-175 the authors state that "proliferation of FoxA+ stem cells precedes the increase in pharynx progenitors." This refers to FoxA+ H3P+ cells vs. FoxA+ piwi-1+ cells, but the only difference is that the former are stem cells in the act of mitosis. Is a distinction being made? Elsewhere in the paper, FoxA+ piwi+ cells are referred to as stem cells. The terminology used needs more clarity and consistency.

Along these lines, what is a FoxA+ PSC (Line 168)? Are the authors suggesting that FoxA is a pluripotency marker? Or are the authors saying that tgs-1 has a more expansive expression pattern and is co-expressed with progenitor markers? If double FISH was performed with the progenitor markers reported (ovo, myoD, gata-4/5/6, six-1/2, and pax6), would they all overlap with tgs-1? These experiments need to be performed to make any claims about FoxA expression in the context of pluripotency.

7) In Fig. 3C, how does pharynx regeneration occur over such a long period of time after nocodazole treatment in the 1-2 day window? Does target-blind regeneration occur once this window is missed? The authors should repeat analysis of FoxA+ progenitors at later time points in this condition, and/or show rates of BrdU incorporation into the pharynx with and without nocodazole treatment in this window.

8) The use of the inhibitor PD in Fig. 4 is problematic. No data are shown to verify that phosphorylation of ERK was inhibited in these experiments. A citation of previous use is not sufficient. The effect of PD on WT uncut animals with regards to FoxA+ cells is not shown and is a necessary control. To address questions of drug specificity, the authors should corroborate their findings with a second inhibitor of ERK signaling like U0126, which has already been shown to work in planarians (Owlarn et al. 2017).

9) The conclusion that ERK signaling functions in regulating differentiation but not proliferation is premature (line 249-264). Figs. 4E-H should be quantified as percentages of piwi-1+ and H3P+ cells, especially since there is decreased proliferation overall with PD treatment.

10) The use of head fragments to compare eye regeneration vs. pharynx regeneration is inappropriate. Previous studies have already shown that the absence of eyes is not required to induce ovo+ progenitor amplification (LoCascio et al. 2017). Thus, this is not a surprising result (line 343-345) and the authors are mis-citing previous observations (in the earlier work, head fragments were never described). The region where ovo+ cells was quantified in Fig. 6A is not justified or explained. The yellow box is placed in a medial region where ovo+ cells do not normally reside. The authors should image within the laterally positioned ovo+ streams that have been previously described (Lapan & Reddien 2012; LoCascio et al. 2017).

11) Rather than using head fragments, the authors should repeat the flank resection experiments shown previously (LoCascio et al. 2017). This previous study showed that increased BrdU incorporation into the pharynx occurred following flank resection even though the pharynx was present. That result may have been 1) an artifact of increased BrdU staining due to stimulation of proliferation upon injury, 2) caused by unintentional damage to cells associated with the pharynx, or 3) a response to the loss of FoxA+ progenitor populations that surround the pharynx rather than the loss of the differentiated organ. The authors have the opportunity to revisit this published observation by quantifying the FoxA+ progenitor response during flank resection +/- pharynx. Without these data, this story is incomplete and therefore the conclusion of a targeted regeneration response is not yet convincing.

12) The negative results that proliferation and ERK signaling are dispensable for eye regeneration in Fig. 6 are weak and unconvincing. The regenerated eyes appear smaller; this should be quantified (number of PRNs per eye). If the small pharynges that form in Figs. 3D and 4C are considered a deleterious phenotype, why is the same standard not applied to the eye? Also, existing eye progenitors could have been sufficient for eye regeneration in these drug treatments. Furthermore, eyes did not regenerate after nocodazole treatment 50% of the time. Is it not more likely that the observations reported are dosage and timing artifacts? How has proliferation been affected? These observations do not live up to the claims made.

13) The authors claim that ovo+ cells are not proliferative (H3P+) even in cases where there is eye progenitor amplification (head amputation), but the data are not shown (line 321). They should be. Indeed, previous publications have never shown that ovo+ cells proliferate. This might mean that there are proliferating eye progenitors that precede expression of ovo. The authors should discuss this alternative.

14) The authors claim that eye regeneration does not require proliferation or ERK signaling but pharynx regeneration does. This conclusion hinges on the gross observation that eyes can regenerate in the presence of nocodazole and PD (see point 12 above). These data are coarse and the interpretations are unconvincing. Instead, their model can be directly tested using BrdU pulse-chase experiments. According to the authors' model, one would predict that following pharynx amputation, the rate of incorporation of BrdU+ cells into the regenerating pharynx should be higher than in uninjured controls. Conversely, the rate of BrdU incorporation into the regenerating eye should remain unchanged between injured (i.e. eye-resected) and control animals (LoCascio et al. 2017). Once the authors have established the prediction above, they have the opportunity to show the effects of nocodazole, PD, and U0126 on BrdU incorporation in the regenerating eye vs pharynx following eye resection and pharynx amputation in the same animal. This way, the authors can directly test the requirement for proliferation and/or ERK signaling in both tissues.

Preprint Review

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Summary

All three reviewers recognized the potential significance of this work, but shared concerns about sample sizes, lack of biological replicates, and insufficient details about cell quantification.

Reviewer #3:

Kim et al. studied the roles of GATA1 binding and H3K27ac on chromatin interactions associated with binding of the architectural factor CTCF. The authors focused on a TAD and sub-TAD surrounding the human beta-globin locus. The sub-TAD that is flanked by tissue-invariant CTCF sites that form contacts with each other only in erythroid cells. Loss of GATA1 binding at the beta-globin enhancer (LCR) and perturbation of H3K27ac affects some CTCF associated contacts, both involving the sub-TAD as well as the (tissue-invariant) TAD boundaries.

The mechanisms by which tissue specific contacts are established are of great interest in the field. However, while this report provides some correlative data to support a link between H3K27ac and CTCF contacts, the study in its current form is too preliminary and failed to address alternative explanations.

1) A major concern for this study: the MEL/chr11 cell line might not be a suitable model system. The CTCF/Rad21 binding profiles in the MEL/chr11 seem quite different from normal human erythroid cells. Specifically, the signals of CTCF binding at C4, C5 and C6 are almost at the baseline (Fig2A/B and Fig3D/E) in MEL/chr11. However, those sites should have comparable CTCF binding strength with C3 and C7, (e.g. Fig2E). The diminished CTCF binding at the C4-C6 sites might affect the sub-TAD structures in MEL/chr11 cells.

2) Loss of GATA1 binding at HS2 or HS3 affects GATA1 binding at other sites as well. It is also possible that loss of GATA1 binding impairs binding by other nuclear factors that might be involved in sub-TAD formation. The same holds for histone modifications other than H3K27ac. This should be discussed.

3) Fig.2: the correlation between H3K27ac and CTCF contacts does not hold at all examined sites. For example, H3K27ac is reduced also at C7 and C3 that maintain contacts. Same in Fig.3 where increases in H3K27ac is also increased near CTCF sites whose contacts don't increase.

4) Fig.2: total H3 is reduced at C5 to the same extent as asH3. How was H3K27ac normalized?

5) Why were p300 inhibition experiments done in K562 cells? In Fig2E and Fig4D it seems that the H3K27ac signals are not concordant between MEL/chr11 and K562 cells. For example, in Fig2E, the H3K27ac at C3 site is very strong in the MEL/chr11; However, in Fig4D, the H3k27ac signal at C3 site is near baseline. The H3K27ac signals also suggest that the MEL/chr11 cell line is different from normal human erythroid cells and also the leukemia cell line K562. The different H3K27ac profiles at CTCF binding sites confound the interpretation.

6) Fig1E, the interactions between HS5-3'HS1 (C4-C5) were not significantly changed in the HS3/HS2 mutated MEL/chr11 cells. Actually this well known interaction between HS5-3'HS1 was not even detected by 3C in the WT control MEL/chr11 cells, contrary to previous studies. Again, this suggests that the MEL/chr11 cell line is not an ideal system for this study. The reduced interactions between beta-globin and C5/HS5 could be the result of loss of GATA1 binding but not CTCF. For clarity it would be better to plot the 3C data scale to the actual genomic distance.

7) The authors should make clearer distinctions throughout whether they are considering supposedly tissue-invariant CTCF contacts near the TAD boundaries or the tissue-specific sub-TAD. It appears that both can change upon their perturbations.

8) Data mining: "acetylation level was decreased remarkably in the boundaries of longer interactions (over than 100 Kb)" why is this remarkable? How does contact distance inform the role of H3K27ac? What is the correlation genome wide between H3K27ac and CTCF ChIA PET? This could be done using data sets from a variety of cell types.

9) Fig.6A: GATA1 knock down seems to affect H3K27 broadly and not any more extensively (or even less) at CTCF sites.

Reviewer #2:

The authors analyzed long and short range chromatin interactions in erythroid cell lines after perturbation of globin associated enhancers, histone acetylation, GATA1 expression, or CBP/p300 expression. The data show that CTCF binding sites are associated with high levels of H3K27 acetylation in the context of short range interactions. Deletion of GATA1 binding sites in the human LCR in hypersensitive sites 2 or 3 caused a reduction in H3K27ac at nearby CTCF sites and impaired the interaction of those sites, without interfering with the binding of CTCF or the cohesin subunit Rad21. Treatment of cells with TSA or inhibition of CBP/p300 or GATA1 expression had a similar effect.

The manuscript provides interesting and novel observations with respect to GATA1 binding and H3K27ac at nearby CTCF sites. However, the mechanism(s) by which GATA1 modulates H3K27ac levels at CTCF sites remain(s) unknown.

Specific comments.

1) One possible interpretation of the results, which has not been addressed by the authors, is that the reduction in histone acetylation levels may modulate the stiffness of chromatin, which may particularly affect short-range interactions.

2) Figure 3: TSA treatment also affects other histone acetylation events. This should be mentioned. Furthermore, the data in Figure 3D are not consistent with data in Figure 1E with respect to the control cells. In Figure 1E it is shown that the anchor C5 interacts with beta and C6, Figure 3C shows no interactions between these elements.

3) Figure 4: There is no description of how the CBP/p300 depleted cells were generated. Was this a single shRNA? If so, it would be important to repeat the experiment using a second shRNA targeting a different region of the RNA to avoid off-target effects. Furthermore, it would be important to show the CBP/p300 binding pattern across the globin locus and the CTCF sites. Does H3K27ac at the CTCF sites correlate with CBP/p300 binding? These data should be available from K562 cells.

4) Figure 6: there is no description of how the GATA1 depleted cells were generated. Again, was this a single shRNA?

Reviewer #1:

In this study, Kim et al described the GATA1-dependent histone H3K27ac on a subset of CTCF binding sites and CTCF-mediated chromatin interactions in erythroid cells. The authors generated a GATA1 binding site deletion in MEL cells and observed impaired CTCF-mediated interactions around the beta-globin gene cluster. They further modulated H3K27ac by TSA treatment of CBP/p300 knockdown, and noted that altered H3K27ac affected interactions between a subset of CTCF sites. The authors further performed global correlation analysis between public ChIA-PET and H3K27ac in K562 cells with or without GATA1 depletion, and presented evidence supporting a modest effect of H3K27ac at some CTCF sites upon depletion of GATA1 in K562 cells. Based on these findings, the authors concluded that GATA1-dependent H3K27ac mediates erythroid-specific chromatin interactions between CTCF sites.

Overall, this manuscript provides molecular details of the role of GATA1-mediated transcriptional programs in regulating chromatin interactions between CTCF sites. The experiments related to GATA1 binding site mutations were well designed and executed. The authors also make use of existing public datasets to extend the analysis to global scales. However, the current study falls short in providing strong evidence to support several conclusions due to a combination of insufficient data and suboptimal data quality. The overall conclusions that GATA1 regulates chromatin interactions through H3K27ac-mediated effects do not significantly extend our current understanding based on previous studies in the authors' group (Kang et al., 2017 BBA 1860:416) and others (Hsu et al., 2017 Mol Cell 66:102). The lack of replicate experiments for several ChIP-seq studies limited the robustness of relevant conclusions.

In summary, although the current study provides additional insights into the role of GATA1-dependent transcriptional programs in regulating CTCF-mediated chromatin interactions, the overall findings were not developed in sufficient depth in light of previous studies and some conclusions were not sufficiently supported by the evidence.

Major points:

1) The authors previously showed that interactions between CTCF sites associated with sub-TADs are dependent on the binding of GATA1 to LCR enhancers (Kang et al., 2017 BBA 1860:416). In this study, the authors provided further details of the relationship between GATA1 binding, H3K27ac, and CTCF-mediated interactions. These data provide additional insights into the molecular mechanisms of GATA1-mediated effect on chromatin interactions, although they do not add significantly to previous studies from these authors and others (e.g. Hsu et al., 2017 Mol Cell 66:102).

2) To determine the effect of GATA1 binding site KO on CTCF-mediated interactions, the authors performed 3C-qPCR analysis (Fig. 1E). Given the higher resolution and ability to quantitatively contextualize the data obtained from next-gen sequencing based 3C methods, I recommend these be done in the future. Similar for the studies in Figs. 3B-E and 4E.

3) Page 5, line 115-117. It is stated that 'when it is compared to the results from knocking down GATA-1...'; however, no results from GATA-1 knockdown were included for the comparison. These studies would be helpful to determine whether the effect is directly caused by loss of GATA1 binding at the LCR enhancers.

4) It is unclear whether GATA1 site KO also affected H3K27ac signals at other CTCF-bound chromatin regions besides the b-globin gene cluster (C3 to C7). For example, in Fig. 2E, it would be helpful to include C2 and C8 regions in the ChIP-seq track as controls. Additional analyses of global changes of H3K27ac and CTCF binding also will be helpful to determine whether the effect is limited to the b-globin gene cluster.

5) In Fig. 3, to determine the effect of H3K27ac on chromatin interactions, the authors treated the cells with the HDAC inhibitor TSA. A major caveat of these studies is related to the pleiotropic effects of TSA on global H3K27ac and gene expression, thus the indirect effects on chromatin interactions due to altered gene regulation and/or erythroid maturation. This limitation should be discussed.

6) In Fig. 5, it would be important to include analyses by separating CTCF binding sites depending on whether or not they are associated with TAD boundaries. Is there correlation between the range of CTCF-mediated interactions and TAD boundary? These studies will provide a global assessment of the findings based on the beta-globin gene cluster in Figs. 1-4.

7) The effects of GATA1 knockdown on H3K27ac signals at CTCF binding sites at the global or selected regions are marginal (Fig. 6A, C,D, noting the scales of y-axis not started with 0 in Fig. 6C,D). It is unclear whether this is due to suboptimal data quality (see below) or limited effects at a global scale. These results raise questions about the extent to which the GATA1-mediated effect on H3K27ac at CTCF sites and CTCF-mediated interactions in erythroid cells.

8) There are concerns about the quality of several genomic datasets including H3K27ac ChIP-seq that may limit the robustness of relevant analyses. Specifically, the quality of H3K27ac ChIP-seq in K562 cells is suboptimal and no apparent H3K27ac enrichment is noted at the CTCF-binding sites (C3, C4, C6 and C7). Comparing Fig. 2E with Figs. 4D and 6A, the signal-to-noise ratio is highly variable in different experiments. No replicate experiment or quality control analysis was provided.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary

This study investigates the relationship between the binding of the transcription factor GATA-1 and histone acetylation on CTCF sites in the same genomic region. Although the reviewers find this work interesting, they raise concerns about the strength of the novel conclusions that can be drawn at this stage. Specifically, the reviewers are concerned about the strength of the data supporting a specific role of GATA1 binding in regulating CTCF-associated sub-TAD interactions (Reviewer #1 and #3), the lack of technical details on several key experiments (Reviewer #1, #2 and #3), the lack of consideration of alternative interpretations on GATA1- and/or H3K27ac-mediated chromatin regulation (Reviewer #2 and #3), and the use of MEL/chr11 cell line as the experimental model system (Reviewer #1 and #3).

Reviewer #3:

The manuscript by Sahm et al. describes the transcriptomic comparison of breeders and non-breeders in two species of mole rats from genus Fukomys. The remarkable aspect of Fukomys mole rats is that the breeders live significantly longer than workers. The authors produced new breeder couples by pairing animals from different family groups and then compared their transcriptomes to non-breeders of the same age from the original colonies.

There were very few differences identified between breeders and non-breeders. Most transcriptomic changes were confined to gonads and endocrine glands. This is somewhat unsurprising and these organs become active for breeding. The pathways that became activated were related to ribosome biogenesis, protein translation, and MYC signaling, which all reflect physiological activation of these tissues in breeders.

Interestingly, some activation of these signaling pathways was also observed in non-gonadal tissues, which contradicts the common dogma that downregulation of these pathways is associated with lifespan extension. This is a remarkable result that suggests that short-lived model organisms may not correctly reflect signaling effects required for longevity in long-lived species. The authors also point out to higher glucocorticoid levels in workers and speculate that that may be showing Cushing's like syndrome.

Overall, this is an important study of high interest.

Items to address:

1) It is not clear how long were the animals maintained in a breeder status prior to analysis.

2) Figure 3A, the rationale for the comparison of changes in young breeder versus non breeder animals to changes that occur with age over time is unclear.

3) Figure 4, were the changes driven by gonads mainly? How many were non-gonadal? For example, in Figure 2, muscle showed 0 DEGs by status, but in pathway analysis we see upregulation of pathways. Please explain.

4) Table 2: TOR is downregulated in breeders while ribosome processes are upregulated, please explain.

5)The finding of Cushing's syndrome needs more support. Please consider comparing Cushing's related transcriptome changes as a whole to the changes observed in mole rats, otherwise this conclusion may need to be toned down.

Reviewer #2:

Sahm et al. have analyzed gene expression of 22 samples across 15 tissues of Fukomys mole rat, and with these resources, they try to explain why breeders and non-breeders have different lifespans in those species. Below I highlight key aspects of the approach (and related conclusions, or lack thereof) that I believe represent serious issues. One positive note, again, the questions and data of this paper that I believe are highly interesting and important if the author can pursue it in a more focused and solid way.

1) First, in my opinion, the discussion of the paper is not well synthesized, and the content does not help the reader for the aim of study and of what is discussed in the title (e.g., HPA) and abstract. While the entire discussion fails to build logics between HPA stress and aging in mole rats, it tells the story of intervention and hypothesis testing instead, with the last of the results immediately jumping into comparisons of positive selection genes and DEG (It is unclear why it is relevant even one gene is found under positive selection).

2) Given hundreds of samples have been sequenced in the paper, there is no extensive examination of batch effect, which could ultimately, in its present form, put all the results (e.g., DEG analysis, pathways enrichment, multifactors analysis) and conclusions at high risk. Particularly, the PCA analysis has indicated the species, tissue, and the combination of both variables accounted for 98.4 % of the total variance in the data set--it becomes more important to know how the authors have organized the sequencing strategy.

3) Unsophisticated use of enrichment analysis on pathways likely leads to misleading conclusions - a large portion of the analyses presented use an unreasonable approach to identify genes with expression shift across tissues and species to make conclusions that I believe are largely misleading about genes important for longevity. The authors identify pathways that have overall (gene-wide) changes in gene expression as p values looks like a potential indication of expression shift. While this approach MAY be lucky enough to catch a few of these 'true positives", the VAST majority of what it will identify will be pathways with global accumulated changes (which is what the point would be), but rather small pathways or pathways fully of with wired p values or undetectable expression (and thus perhaps some of the least important genes). Then, the extension of these approaches to pathways further muddies the waters of any discussions. The approaches for detecting affected global pathways have been the subject of a very large body of literature, and there are well developed hierarchical/empirical models for testing these hypotheses that the authors have not referred to. And, of course, it is strongly encouraged that the authors formulate a new model/index to reevaluate pathways analysis as the data and experimental design is unique compared to other studies.

4) Last but not the least, small KEGG set, i.e., KEGG, that with very few genes could also be confusing such whole categories analysis. The author should check this potential bias using random sampling 'pseudo-KEGG set' with the same gene number and/or identify a threshold to filter each true KEGG category considered.

Reviewer #1:

This is a primarily descriptive study reporting gene expression differences between breeding and non-breeding individuals of two long-lived Fukomys species. These mole rat species are interesting for this type of analysis because it has been previously shown that breeders live ~2-fold longer than non-breeders. Thus, it may be possible to learn about mechanisms that determine longevity by studying differences between breeders and non-breeders. Although the manuscript is primarily descriptive, there is value in observational data sets such as this, which can be hypothesis generating and can spur future, more mechanistic studies. A lot of analyses are presented - with many different comparisons of differentially expressed genes, GO terms, etc. - but they have not yet produced a lot in terms of true biological insight. As it was largely limited to gene expression, it is also a bit one-dimensional. The data will likely be of interest and value to scientists who study the comparative biology of aging and systems biology of aging, but without additional biological insights derived from the data, the manuscript will probably not capture the interest of a broad scientific audience or even the broader gerontology community.

My largest concerns with the content of this manuscript are related to interpretation of the data. While this type of comparative gene expression analysis can generate hypotheses, it cannot strongly support or refute causal relationships without additional experimentation. The authors repeatedly appear to interpret correlative observations with causation and make claims that overreach the data. The title itself is a good example of this where the authors claim "the HPA stress axis shapes aging rates". There is no direct evidence to support this claim or others similar in nature throughout the manuscript.

Another area of overinterpretation is with respect to the relevance of these findings as a test of the validity of prior aging theories or mechanisms. It seems very likely that this is a somewhat unique evolutionary case where upon the switch from non-breeder to breeder there is a dramatic rewiring of physiology at many levels (transcriptional, translational, post-translational, metabolome, epigenome, etc.). Simply because this switch does not match patterns seen in longevity interventions such as caloric restriction, reduced GH/IGF-1 signaling, or mTOR inhibition does not refute or call into question literature describing potential mechanisms for how those interventions act. It likely simply reflects that this is a different path to achieve longevity.

Specific comments:

• The title is problematic as described above.
• The first sentence in the abstract is problematic as it implies causality between sexual activity/reproduction and longevity. Sexual activity/reproduction are associated with life expectancy. It is interesting to consider whether these two things could perhaps be uncoupled in this animal, as has been shown for reduced fecundity and longevity in invertebrate models.
• The phrase "oppose crucial findings" in the abstract is also problematic. First, the word "crucial" does not seem to make sense in this context. What makes them crucial? Second, it is intuitive and expected, indeed perhaps required, that reproduction would be associated with anabolic processes, and this study does not show causality between the observed changes in these processes and longevity, so it does not actually "oppose" the prior findings in genetic models with reduced IGF-1/GH signaling where lifespan is extended.
• I have a problem with the premise that it is possible to "confirm or falsify" results from cross-species or intra-species studies through the type of approach taken here as implied in line 47. Confirming or falsifying results implies something about the quality of the prior data itself. I assume what the authors mean is confirming or falsifying the underlying hypotheses or assumptions. Even that is questionable, however, since the mechanisms by which longevity are determined could simply be different within species versus across species versus cases like this where you have dramatically different life expectancies in breeders versus non-breeders.
• I thought the discussion of the GH/IGF-1 results was fairly balanced, but I would encourage the authors to consider more deeply the within species versus across species observations in the literature. The evidence for reduced GH/IGF-1 increasing lifespan comes from within species studies and appears to hold true from worms to dogs and likely in humans as well, although the correlation between body size and lifespan is a bit more complicated in humans for obvious reasons. Within species, smaller individuals who have reduced GH/IGF-1 tend to live longer - that's a correlation. In worms, flies, and mice a reduction in growth signaling has been shown to be sufficient - and very likely causal - for enhanced longevity through genetic and pharmacological studies. The comment that these interventions are all performed during development is not exactly true - in mice rapamycin at least works in adulthood and even when only given transiently or intermittently in adulthood. Across species, larger species tend to live longer. Perhaps the mechanisms going from non-breeders to breeders more resemble the evolutionary longevity strategies that have been taken at the species level rather than the mechanism that appear to determine longevity within species. Personally, I don't see this as a contradiction or a controversy within the field.
• I find the "short-lived" versus "long-lived" species argument to be overly speculative and arbitrary. Interventions such as CR, mTOR inhibition, reduced IGF-1, etc. extend lifespan at least from worms to mice, which is a >50-fold difference in lifespan. Mice to people is ~30-fold. Compared to mice, worms are shorter-lived (by a fold difference metric) than mice are compared to humans.
• The authors state that breeders and non-breeders have "massively diverging aging rates", but I think it is important to keep in mind that differences in lifespan do not necessarily imply differences in aging rate. Especially going from the long-lived state to the short-lived state. Perhaps there is good evidence that functional and molecular declines and diseases/pathologies of aging are accelerated in the non-breeders and delayed in the breeders, which would support this assertion, but this is unclear from the manuscript.
• The phrase "unilaterally described as harmful" in the conclusion is simply not true. GH/IGF-1 signaling limits lifespan in worms, flies, and mice but none of the papers cited unilaterally claim that it is harmful. In fact, some of those same papers note that high GH/IGF-1 signaling often confers a selective advantage in terms of faster maturation and reproduction. So, at the species level, this is beneficial. Even at the individual level, high GH/IGF-1 may be associated with better outcomes in the wild where predation is a factor. High GF/IGF-1 in these species is detrimental (only?) in the context of aging/longevity in a relatively safe laboratory environment at the individual level.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 2 of the manuscript.

Summary

Mole-rats live in social colonies that contain two breeders and many non-breeding workers. This study looks at gene expression between breeding and non-breeding individuals of two long-lived mole-rat species in the genus Fukomys. The large lifespan difference between breeders and non-breeders has made these animals an important model system for the study of aging, and the data collection reported in this manuscript is very impressive. The paper is descriptive data, with limited data analyses and experimental support for the conclusions. However, given the scale and rarity of the dataset, it will be a valuable resource for the aging research community once the quality and physiological relevance of the data are demonstrated by additional bioinformatic analyses and experimental validations.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 2 of the manuscript.

Summary:

VolcaNoseR is a plotting tool to make volcano plots from transcriptomics and proteomics datasets. It is easy to use, intuitive, interactive and reactive. However, VolcaNoseR does not provide any statistical analysis of the data, and it is therefore of limited applicability as it is likely that a user that is able to handle and analyse this type of data, is likely to be able to produce a scatter plot. The bigger hurdles with this type of analysis that could lead to new biological results are centered around the correct statistical analysis of the data, problems that the software does not address.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to version 1 of the manuscript.

Summary:

This manuscript describes the mechanism by which the transcriptional repressor ZBTB18 regulates the expression of sterol regulatory-element binding proteins (SREBP), transcription factors that control the expression of enzymes involved in fatty acid and cholesterol biosynthesis,in glioblastomas. The connection between core transcriptional regulation and tumor metabolism is an area of current interest. This manuscript uses immunoprecipitation and mass spectrometry to identify the well-characterized transcriptional corepressor CTBP2 as a new ZBTB18 interacting protein, which the authors show overlap in binding at many gene promoters. They further show that CTBP2 activates, while ZBTB represses the expression of some SREBP genes. The reciprocal regulation of ZBTB18 and CTBP2 has potential value in understanding the functional regulation of lipid biology. However, reviewers raised substantial concerns with the studies, as described below.

Reviewer #3

The authors address an important open question in decision neuroscience: how do perceptual and metacognitive choices arise from the same sensory input? They perform an experiment that asks observers to report both their percept and associated confidence, and then investigate the role of history biases in both perceptual and metacognitive decisions. They find support for (well-established, e.g. https://elifesciences.org/articles/11946 ) second-order theories of metacognition, which state that metacognitive reports arise from more than just the information used to guide first-order perceptual decisions.

The methods and statistics are rigorous, and the authors have thoroughly reviewed the relevant literature on the topic. The mutual information analysis is a nice way to quantify the size of different biasing factors. However, the paper presents only limited mechanistic insight into history biases, decision processes or metacognition. It would help to clarify what the main insights are, and how they change our understanding of decision-making and its underlying computational nature.

Technical suggestions/comments:

-A recent study (https://elifesciences.org/articles/49834 ) shows the importance of correcting for slow fluctuations within a session, to accurately estimate history biases that are due to the previous trial itself. It would be great to see if the results hold after such a correction, to ensure that the effects are not due to slow fluctuations in choice and metacognitive reports within a session.

-The answer to whether perceptual and metacognitive decisions arise from the same or distinct processes may depend strongly on the nature of the confidence report. Would the same conclusions hold if choice and confidence were indicated with the same action (e.g. https://elifesciences.org/articles/12192 )?

-Half of participants base their confidence ratings mostly on confidence history, rather than on evidence. Does this just mean people were not very motivated to do well on the confidence report? Were they rewarded to perform well on both tasks?

-The authors test the population-level prevalence and effect sizes of perceptual and metacognitive history biases? However, with n = 37 their size does not seem large or diverse enough to infer properties of the general population.

Reviewer #2

In this paper, Benwell and colleagues present a perceptual decision-making task with confidence ratings in human subjects to investigate choice and metacognitive history biases. The statistical analyses are solid and thorough. The mutual information analysis is a valuable complement. The paper is comprehensive, clearly written and the figures are informative. It would help if the authors could emphasise their reasoning across the paper: why selecting this particular paradigm to study history biases, and what is the added value of their findings beyond previous work? Many similar data sets (perceptual decision & confidence) have been published and are open. Moreover, it seems important to better justify their hypotheses and motivate the analyses, particularly the final focus on repeat vs. alternation in a paradigm in which these were not manipulated explicitly by the experimenters.

The authors suggest that history biases are adaptive (building on the stability of real-life environments), whereas at other times, that they are maladaptive ("irrelevant factors such as previous confidence reports"). It would be helpful to explicit the arguments in favour of either interpretation, and to clarify what computational interpretation the present findings favour, if any. There is already a little bit about why it may be advantageous to assume stability. Are there other reasons to think of choice/metacognitive bias as helpful vs. maladaptive? In which contexts? If repeating were a more prevalent bias than alternating in the population, why would this be useful? Relatedly, it would be helpful to further clarify for readers why it is relevant to study choice and confidence history biases, i.e. explain why it is not a simple by-product of experimental designs where experimenters artificially present multiple times very similar decisions.

It is interesting that the authors comment on the prevalence of each result in their sample, instead of simply reporting statistics on group means, to get a better sense of the strength of the findings. However, it is a bit difficult to generalise about "population prevalence" unless larger samples than the current n=37 are used. Because the experimental design overlaps with previous work, most of these analyses could be re-done on other datasets to address discrepancies between the present findings and that of Urai et al. The confidence database (Rahnev et al., 2020) may provide a useful resource for future work (especially for drawing conclusions about population prevalence based on the current sample of 37 subjects).

Technical suggestions/comments:

Could the authors indicate the proportion of errors vs. correct trials on previous repeating vs. alternative trials? If there were more errors on alternating trials, could it be that due to a post error slowing mechanism whereby subjects became more accurate after an alternate, hence the increase in d'? Regarding Fig S1 and the comparison with previous studies, it would be worth discussing the results in relation to a related study in rats (Hermoso, Hyafil et al., 2020 ncomms), for instance examining if the choice bias was overall driven by correct trials and absent after errors (Fig 2A). Finally, in Fig S1 the authors show a choice bias present for both high and low confidence at t-1. Would it be more precise, for concluding about a lack of an influence of confidence, to perform an ordinal regression analysis using the 4 levels of confidence available?

In Fig 1F, 1G, 1H, could the authors perform psychometric and statistical analyses to actually demonstrate the findings that the authors describe, or rephrase that the confirmation of model predictions are qualitative only? (For instance, showing quantitatively that the slopes are different for high and low confidence in Fig. 1F)

In particular, when comparing Fig 1F and 1G, are the patterns for confidence and RTs identical with respect to absolute orientation? If so, is this an issue for interpreting confidence data (supposedly not only a strict reflection of RTs but also incorporating information about accuracy)?

Could the authors comment on (even briefly) the other psychometric parameters (stimulus independent lapse rate and slope)? Why do the stimulus-independent lapses fixed and not fitted with the two other psychometric parameters? Does it change the conclusions if they are fitted? It would be worth checking parameters of the sigmoid psychometric function in Fig S1 (right panel red curve), because the psychometric function looks unusual with an increase at highly positive orientations.

It is reassuring to see that the correlation results in Fig. S4 are reproduced using an alternative metric of metacognitive efficiency (meta-d'/d'). However, could the authors provide this measure for all other analyses based on meta-d'-d'? I am not asking for a detailed breakdown or new figures, but at least in the text specify whether findings are maintained using this alternative metric.

Could the authors argue that here we have a true metacognitive history bias, and not a bias due to low-level effects e.g. motor anchoring, use of scale? (See e.g. Foda, H., Barger, K., Navajas, J., & Bahrami, B. (2017). Domain-general idiosyncratic anchoring of metacognition.)

Reviewer #1

This preprint by Benwell and colleagues aims at studying 'history' biases during perceptual and metacognitive decision-making. The authors rely on a canonical, well-controlled two-alternative orientation discrimination task with confidence reports on a 4-point scale, tested in 37 human observers. Based on both model-free (mutual information) and model-based (type-2 signal detection theory) analyses, the authors report dissociations between perceptual history biases (related to previous perceptual decisions) and metacognitive history biases (related to previous confidence reports). They interpret these two forms of history biases as 'heuristics' informing type-1 (perceptual) and type-2 (confidence) decisions in the absence of sufficient evidence in the current trial.

History biases have generated a lot of interest over recent years, and the comparison of perceptual and metacognitive history biases in a single behavioral modeling study is interesting. The standard 2-AFC + 4-point confidence paradigm used by the authors is well suited to address the research question outlined by the authors in the introduction. However, I am not entirely satisfied by the definition of metacognitive history biases used by the authors throughout the manuscript – something which is likely to impact some of the dissociations reported by the authors.

Indeed, the authors report no effect of confidence at trial t-1 on perceptual bias at trial t (lines 147-149). However, this apparent dissociation appears unsurprising if the response at trial t-1 is not considered in the analysis (as shown in Figure 4). Indeed, a high confidence report in favor of a Left response at trial t-1 is likely to bias the perceptual response at trial t in the opposite direction to a high confidence report in favor of a Right response at trial t-1. In other words, when considering metacognitive history biases, the authors should consider four (not two) types of trials, based on the previous confidence report (high/low) but also the previous response (Left/Right). A true dissociation between previous confidence and the current response would imply that the perceptual history bias (i.e., the effect of the previous response on the current response) is of the same magnitude following low confidence reports and high confidence reports. It is very important that the authors re-compute the effect of metacognitive history biases in this response-dependent fashion. Indeed, Figure 4 will show no effect (i.e., an apparent dissociation) even if the perceptual history bias is strongly increased following high confidence reports than low confidence reports. The manuscript should always consider the direction of the previous response when assessing metacognitive history biases, and only claim dissociations if these previous response-dependent analyses reveal no interaction between the size of perceptual history biases and the previous confidence report (high vs. low).

Along the same lines, Figure 2C should be modified to plot confidence not as a function of the absolute orientation, but as a function of the orientation signed by the provided response (positive for a stimulus orientation consistent with the provided response, and negative for a stimulus orientation inconsistent with the provided response). It is highly likely that confidence does not scale with the absolute orientation as suggested by Figure 2C, but as a function of the consistency of the stimulus orientation with the provided response (highest confidence for an easy stimulus orientation consistent with the provided response, lowest confidence for an easy stimulus orientation inconsistent with the provided response).

Regarding the use of mutual information (MI) as a metric for comparing all kinds of effects, I wonder whether the authors could explain more extensively their reasoning. I was under the impression that MI is bounded differently for different kinds of variables (e.g., a binary effect is bounded at 1 bit). Comparing binary variables (Left/Right responses) with non-binary variables (1-4 confidence reports) may thus be problematic, unless I have missed something. To validate the use of MI for claiming "sub-optimal metacognitive performance" (lines 193-195) would require to perform sanity checks such as model simulations with optimal metacognitive performance. The goal of these simulations is to show the difference between the pattern of MI obtained for simulations with genuinely optimal metacognitive performance (and matched perceptual performance to the human subjects) and the pattern of MI obtained for human subjects.

In the type-2 SDT modeling, the authors now separate Left and Right responses when computing their abs(meta-c minus c) measure. As mentioned above, I believe that the authors should always split Left and Right responses when assessing metacognitive history biases and claiming dissociations between type-1 (perceptual) and type-2 (metacognitive) processes. As above, also, model simulations with optimal metacognitive performance but no history biases (neither perceptual nor metacognitive) may be useful to validate the analyses carried out by the authors on their behavioral data.

In Figure 4, as in Figure 2C, post high confidence and post low confidence should be further split between post high/low confidence in a Left response and post high/low confidence in a Right response. While a high confidence report in the previous trial may not potentiate perceptual sensitivity (d') on the current trial, it is possible that a high confidence report for a Left response in the previous trial would bias perception in favor of a Left response in the current trial more than a low confidence report for a Left response (and vice versa for a Right response).

Finally, the repeat vs. alternate effect shown in Figure 5 could be driven by at least two very different mechanisms that cannot be teased apart from presented analyses: 1) the reduced orientation sensitivity in repeat trials proposed by the authors, and 2) a non-zero 'repetition lapse' rate (i.e., a fraction of trials in which the subject blindly repeats his/her previous response). To distinguish between these two accounts, it would be very useful to re-plot Figure 5C. Instead of the absolute orientation, one would use as x-axis the orientation signed by the previous response (positive if the current orientation is in the same direction as the previous response, negative otherwise) and plot on the y-axis the fraction of repeat decisions in the current trial. Fitting a sigmoid function to this curve with a non-zero probability of a blind repetition should afford to tell whether the lower apparent sensitivity in repeat trials shown on Figure 5C is actually triggered by blind repetitions – instead of a lower sensitivity to orientation.

Preprint Review

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Summary

This preprint describes a behavioral study of 'history biases' during perceptual and metacognitive decisions. The preprint reports dissociations between history biases across successive perceptual decisions and history biases across successive confidence reports. The question of how perceptual decisions and confidence reports arise from the same sensory input is important, and the statistical analyses of the behavioral data are rigorous and thorough. In particular, the proposed mutual information analysis appears valuable to quantify and compare different biasing effects. However, despite these methodological strengths, the preprint does not reveal substantive new insights into the computational processes which may give rise to the observed effects. Also, the preprint reads at times more like a collection of findings than a coherent study of a targeted research question. In this respect, it would be useful to emphasize the added value of the findings beyond the extensive previous work on history biases and on the relation between type-1 (perceptual) and type-2 (metacognitive) decisions. An explicit motivation of the performed analyses, particularly the focus on the repetition vs. alternation contrast at the end of the results, would be very useful to clarify the reasoning followed by the authors throughout the study.

Preprint Review

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Summary

This paper analyzes the evolution of the KRAB-containing zinc finger protein (KZFP) family of proteins. While the reviewers were all interested in the topic, several major concerns came up during review. These include technical limitations of the methods chosen to analyze this challenging protein family (e.g., determination of orthology, selection analysis, and so on), and that new ideas, including claims about non-coding evolution and positive selection, are not convincingly supported by the analysis presented.

Reviewer #3

Vuorio and colleagues combine atomic resolution molecular dynamics simulations and NMR experiments to probe how glycosylation can bias binding of hyaluronan to one of several binding sites/modes on the CD44 hyaluronan binding domain. The results are of interest specifically to the field of CD44 biophysics and more generally to the broad field of glycosylation-dependent protein-ligand binding. The manuscript is clearly written, and the combination of data from computational and experimental methodologies is convincing. I especially commend the authors on the thorough molecular dynamics work, wherein they ran multiple simulations at microsecond timescale and tried different force fields to minimize the likelihood of their findings being an artifact of a particular force field.

Reviewer #2

This manuscript is focused on understanding how N-linked glycosylation regulates the binding of the (very large) polysaccharide hyaluronan (HA) to its major cell surface receptor CD44, a question relevant, for example to the role of CD44 in mediating leukocyte migration in inflammation. The paper concludes that multiple binding sites for HA exist and that their occupancy is determined by the nature of the glycosylation, a suggestion first made by Teriete et al. (2004). The work is based on atomistic simulations with different glycan compositions and NMR spectroscopy on a non-glycosylated CD44 HA-binding domain (HABD) expressed in E. coli. While the question being researched is interesting and of biological relevance, there are flaws in the work.

The paper describes how the well-established HA-binding site on CD44 (determined by a co-crystal structure; Banerji et al., 2007) is blocked by N-linked glycosylation (principally at N25 with a contribution from glycans at N100 and N110) and how certain glycans favour binding at a completely distinct binding site that lies perpendicular to the canonical 'crystallographic' binding site. This alternative 'upright' binding site, which has been proposed previously by the authors (Vuorio et al., 2017), needs further supporting experimental data.

Firstly, unlike the 'crystallographic' binding site that forms an open-ended shallow groove on the surface of the protein allowing polymeric HA to bind (and multivalent interactions to take place), the 'upright' binding site is closed at one end and can thus only accommodate the reducing end of the polysaccharide (as apparent from Appendix 1 Figure 1). Its configuration means that it would be impossible for this mode of binding to allow multivalent interactions with polymeric HA. This is a major problem since biologically relevant CD44-HA interactions are multivalent where a single HA polymer interacts with a large number of CD44 molecules (e.g. see Wolny et al., 2010 J. Biol. Chem. 285, 30170-30180). So even if this binding site existed, an interaction between a single CD44 molecule on the cell surface with the reducing terminus of an HA polymer would be exceptionally weak.

Secondly the NMR experiments performed in this study, purporting to provide evidence for multiple modes of binding, are problematic. Why weren't differentially glycosylated proteins used, i.e. where individual sites were mutated (e.g. +/- N25); this would have allowed comparisons of the glycosylation patterns hypothesised (based on the computer simulations) to favour the 'crystallographic' versus 'upright' modes. Furthermore, previous NMR studies have shown that the binding of HA to CD44 causes a considerable number of chemical shift changes due to the induction of a large conformational change in the protein (Teriete et al., 2004; Banerji et al., 2007), making it very difficult to identify amino acids directly involved in HA binding based on the NMR data. Moreover, this conformational change has been fully characterised for mouse CD44 with structures available in the absence and presence of HA (Banerji et al., 2007); this information should have been used to inform the interpretation of the shift mapping. In fact, the way in which the shift mapping data are interpreted is simplistic and doesn't fully take account of the reasons that NMR spectra can exhibit different exchange regimes.

Reviewer #1

The authors use MD simulations and NMR to study the cell surface adhesion receptor CD44 with the purpose of understanding the binding of carbohydrate polymer, hyaluronan (HA). In particular, this study focuses on the effects of N-glycosylation of the CD44 glycoprotein on potential HA binding. The authors previously proposed two lower affinity HA binding modes as alternatives to the primary mode seen in the crystal structure of the HA binding domain of CD44, driven by different arginine interactions, but overlapping with glycosylation sites that will affect HA binding. This study suggests that, because the canonical site appears blocked by glycans attached to the surface, HA would instead likely bind to an alternate parallel site with lower affinity, thus changing receptor affinity. The authors do not study HA binding to the glycosylated form directly, but undertake simulations of bound glycans to draw their conclusion. They do, however, place HA near the non-glycosylated CD44 in simulations, although it is not clear that MD sampling has been designed to provide unbiased observations of HA binding, or how the simulations help explain the NMR experiments.

The data rely on libraries of MD simulation, which are substantial, with several replicas of a microsecond each. But what have these simulations really proved with reliability? Figure 2a shows that, while glycans stay roughly where they started, they are dynamic and cover much of the canonical HA binding site, which may be the case. From this the authors imply that the crystallographic site is significantly obstructed, the lower-affinity upright mode remains most accessible, and that the level of occlusion of the main site depends on the degree of glycosylation and size of the oligosaccharides. However, a full simulation of HA binding to this glycosylated surface was not attempted. It would have been good to see the glycans actually block unbiased simulation of canonical binding to the crystallographic site on long timescales (not being dislodged), but allow alternative binding to the parallel site, without initial placement there.

HA was, however, added to the non-glycosylated CD44-HABD surface in simulations, but no clear data is shown to illustrate the extent of sampling, convergence and reproducibility, beyond some statistical analysis of contacts. It seems a total of 30 microseconds of the non-glycosylated protein with 2 or 3 nearby HA placed was run, leading to contacts. But how well did these 30 simulations sample HA movement and relative binding to sites, if at all? Figure 4 suggests that the HA stay where they have been put. As the MD is the dominant source of data for the paper, the extent of sampling and how the outcomes depend on the initial placement of molecules requires proof. Was any sampling of HA movement, such as between canonical and alternative parallel conformations seen in MD?

The NMR is suggested to show that a short HA hexamer can bind to non-glycosylated CD44-HABD simultaneously in several modes at distinct binding sites, and that MD "correlates" with this. But is this MD biased by initial choices of where and how many HAs are placed, given HA movement is likely not well sampled?

No MD seems to have been used to examine the blocking or lack thereof by antibody MEM-85 in glycosylated or non-glycosylated CD44.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to Version 1 of the preprint.

Summary

This manuscript examines how N-linked glycosylation regulates the binding of polysaccharide hyaluronan (HA) to cell surface receptor CD44, to conclude that multiple sites exist but are controlled by the nature of the glycosylation. The reviewers appreciated many aspects of the work, but they have raised serious concerns about the experimental and simulation design. The reviewers suggested that the proposed alternative binding site may not be biologically relevant, as the relevant CD44-HA interactions are multivalent and cannot be supported by that site. They also suggested that the findings are not well supported by the NMR experiments, which could have been extended to allow comparisons of the glycosylation patterns hypothesised. Moreover, the MD simulations, despite being considerable in size, were limited in sampling different possibilities without bias from the initial HA placement, and there is not enough data to convince the readers of thorough sampling and reproducibility.

Reviewer #3

This study addresses the role of the miR29 micro RNAs in the regulation of melanoma development. Expression of miR29 that is generated from pre-miRs from two clusters is regulated by oncogenic BRAF in human melanocytes. Levels of the mature miR29 are down-regulated in melanoma compared to untransformed melanocytes or nevi and inhibition of miR29 function increases melanoma growth in a murine in vivo model. From RNA-seq data and computational analyses, the authors identify the small MAF protein MAFG as a novel target of miR29 that is involved in melanoma growth. . This study is focused on the function of miR29 in melanoma. The necessity of having the first two figures relevant only for the role of oncogenic BRAF and NRAS in regulating miR29 expression in MEFs is not obvious. Perhaps only one of the two should be shown as a main figure while the other could be moved to the supplemental figures.

The authors state that TPA regulates the MAPK pathway, but this is misleading as the primary target for TPA is PKC. This should be corrected.

The comparison of miR29 expression in the collection of melanocyte and melanoma lines uses a poor logic. BRAFV600E expression in primary melanocytes leads to senescence, the HERMES lines are already immortalized by exogenous expression of various genes (CDK4 etc), but this is not mentioned. What would be the effect of BRAFV600E expression in primary melanocytes on Mir29 and MAFG expression? The comparison between these melanocyte lines and the melanoma lines is also misleading as while they all share the BRAFV600E mutation, the melanoma lines have very different transcriptional signatures some being of melanocytic phenotype and other de-differentiated phenotypes. This is not mentioned and how the differences in transcriptional phenotype and P53 status affect miR29 and MAFG expression is not mentioned (see also comment below).

The description and characterization of the mouse melanoma models is not acceptable as presented. There are no images of tumours, no measure of number and size of tumours or tumour progression only Kaplan-Meier plots of viability. It is impossible for the reader to assess the conclusions from the figure, the additional data should be added. Also, can the authors show that the mouse tumours (or the cells established in vitro) express Mafg and that its levels are altered in the different genetic backgrounds. If not then another mechanism is maybe operative in the mouse tumours.

The RNA-seq data following expression of the miR29 mimics is not fully described, how many genes were changed, what is fold change of the genes that were subsequently selected for further study, in particular MAFG?

The changes in MAFG protein expression in Figure 6A are minor. What is the evidence that such small changes can really impact cell growth (see below)? At face value, basal MAFG expression in H1B melanocytes appears higher than in WM164 cells and its levels in H1B cells can only be mildly affected by modulating miR29. Can the authors comment. More importantly, in Figure 6F some highly tumorigenic lines like 1205Lu or SK-Mel-28 have MAFG levels comparable to the HERMES lines. This does not support the authors’ hypothesis that MAFG levels are major regulators of tumorigenic capacity. There is no obvious correlation between the MAFG mRNA and protein levels comparing panels E and F. Also, what are the relative levels of miR29 in these different cell types, do they correlate with MAFG protein levels or are differences in MAFG levels explained by other regulatory mechanisms? Is there any correlation between MAFG protein levels and cell growth rates and clonogenic capacity amongst the different analyzed melanoma lines? Resolving these issues would strengthen the conclusions.

To fully demonstrate that the effects of miR29 in regulating tumour growth are principally mediated via MAFG, the authors must show they can rescue cell growth defects upon miR29 expression, by expressing MAFG from a cDNA that is insensitive to miR29 regulation. This experiment will help to exclude the implication of other potential miR29 targets in regulation of melanoma cell growth.

Reviewer #2

The manuscript by Vera and colleagues dissects the mechanism of miR-29 family expression in melanoma and provides a possible target to support its tumour-suppressive functions. Towards this the expression of miR-29 family upon MAPK and P53 signalling is carefully followed in transgenic mice and humans and classical target analysis is performed. However a few points remain to be addressed:

Subsection “The MAPK pathway regulates miR-29 expression in human melanocytes and melanoma cells”: "Our results indicate that BrafV600E-induced expression of miR-29 may form a tumour suppressive barrier that restricts the full transformation of melanocytes." This is an overstatement. While the authors clearly show a tumour suppressor role for miR-29 and clearly show that it is induced by MAPK signalling, they never prove that inhibition of miR-29 supports melanocyte transformation.

Discussion section: "Thus, our work has uncovered that miR-29 prevents melanoma progression downstream of MAPK signalling by repressing MAFG." Again overstatement. Although the authors prove that MAFG is important in melanoma and it is a target of miR-29, they never prove that the activity of miR-29 is mediated by MAFG. A rescue experiment is missing here. The sentence needs a rewording.

Additionally, the authors could add (expression) correlation analysis between miR-29 and MAFG in human melanoma samples from publicly available databases.

Reviewer #1

The goal of this manuscript is appealing. The authors wish to evaluate the importance of mir-29 and MAFG in melanoma progression that would be linked to the activation of the MAPK pathway. This article presents a huge amount of biochemical experiments; it has a potential. However, a significant number of issues must be clarified.

The MAPK pathway is induced in the very large majority of melanoma, the role of mir29 and MAFG should then be observed in the vast majority of melanomas. Is it the case? If not, what is(are) the main cause(s)? The authors used BRAF V600E, which is perfectly understandable in the case of melanoma, and they also used KRAS G12D. This last mutation is very rare in melanoma. Why not address a similar question with NRAS Q61K/R?

Choice of the cellular models:

1) The authors focus on mouse embryonic fibroblasts (MEF) in the two first figures. What is the significance of MEF for human melanoma? Why not using primary melanocytes from human (NHEM) and/or established mouse melanocyte cell lines?

2) In this study, as models the authors use mouse (MEF and transgenic) and human (melanoma and melanocyte) species. A crucial question is: are the targets for mir29 the same in humans and mice? The conservation of miR and targets is very poor between species. This needs to be addressed.

3) The authors have to better explain their conclusion of Figure 1. All the presented experiments were performed in MEF. What would happen if the authors used cells from the intestine to evaluate the consequence of BRAFV600E on miR-29? The choice of intestine is not random. What is the link with melanoma? The reason for using mouse embryonic fibroblasts is fine to study molecular issues for this type of cells. However, it is fully accepted that the responses of melanoma to various agents are highly variable.

Quality of the presented results and reproducibility:

I will not go through all of the experiments. I will make some remarks.

1) Figure 1A: The abundance of pERK is moderately induced after expression of KRAS G12D. The authors have to show quantifications on several independent experiments to be convincing.

2) Figure 3E: The culture media are different in melanocyte and melanoma cell lines. It is therefore difficult to compare the level of miRs. For nevi and melanoma, there is also a pitfall. What is the level of these miR in the stroma? What is the percentage of stromal cells in these biopsies?

3) Figure 4: There is a clear action of miR-29 sponge in melanoma initiation in mice. What are the targets in mice? According to their models, are they the same in humans? According to the claim of the authors on progression, we expect that the mice have more metastasis? Is it the case? The authors present an overall survival curve. Knowing the ethical rules associated with mouse studies, the authors do not show the survival since they have to sacrifice the mice. The authors have to show the associated raw data.

4) Figure 7: To further test the importance of MAFG as an oncogene, the authors have to evaluate the growth proliferation in a medium lacking major supplement allowing melanocytes to grow in culture, to reduce the amount of serum, and to test the ability of these cells to grow in 3D or/and in mice.

Terminologies are vague and/or not defined:

1) What do the authors refer to "melanoma progression"? In vivo, the authors address the question of melanoma initiation. There is no information on invasion or metastasis. This is crucial according to their title.

2) AOf course according to the title we wonder if this function is attributed to miR-29a? miR-29b? miR-29c? All? Proper introduction of these three miRs must be done including the known targets of these Mirs. Of course, it has to include the knowledge associated with the different species. In particular, they have to make the point for mouse and humans.

3) The authors refer to physiological conditions in vitro on plastic in the presence of calf serum. The authors must reformulate the text accordingly and tone down their conclusions.

4) The authors refer to "full transformation of melanocytes". What do they refer to? It is too vague. Molecular? Cellular?

Bypass of senescence in melanomagenesis:

Bypass of senescence is mainly due to the RB/INK4A during melanomagenesis. P53 may be involved but appears to occur later. The authors must address this issue, especially when they use Hermes cells.

TPA induces mainly PKC and not the MAPK pathway as the authors mention. The authors should clearly show that the MAPK pathway is indeed induced, not only using pERK. Here, in this context, the WB analyses are not sufficient. Moreover, what would be the action of dbcAMP and aMSH?

Additional comment:

The authors could present a clear and comprehensive scheme for humans (and mice?) representing the associated pathways.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to Version 2 of the preprint.

Summary

This study addresses the role of the miR29 microRNAs in the regulation of melanoma development. Expression of miR29 that is generated from pre-miRs from two clusters is regulated by oncogenic BRAF in human melanocytes. Levels of the mature miR29 are down-regulated in melanoma compared to untransformed melanocytes or nevi and inhibition of miR29 function increases melanoma growth in a murine in vivo model. From RNA-seq data and computational analyses, the authors identify the small MAF protein MAFG as a novel target of miR29 that is involved in melanoma growth.

We found this study interesting, but we are of the opinion that the central hypothesis that miR29 regulates MAFG levels to influence melanoma is not yet fully substantiated by the data. Critical experiments could be added, for example, the rescue of growth defects upon miR29 mimic expression with a miR-insensitive form of MAFG, or evidence that Mir29 regulation of Mafg is involved in the mouse melanoma. Furthermore, we do not feel that the immunoblots support the idea that MAFG promotes tumour growth as the 1205LU cells that are highly tumorigenic in nude mice have MAFG levels comparable to the melanocytes lines.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to Version 4 of the preprint.

Summary

While all three reviewers found this study to be conceptually of considerable interest, a number of major concerns were highlighted. Most notably, the reviewers do not feel that the central claim of the paper that phospho-eIF4E and S6K1 "interaction is sufficient to overcome rapamycin sensitivity and mTORC1 dependence of S6K1" is sufficiently supported by the evidence presented.

Reviewer #3

This is a straightforward study addressing the evolutionary divergence of the glucocorticoid receptor. Authors use the GR and MR receptors from elephant shark which represent distinct orthologs of human GR/MR which diverged from a common CR receptor in cartilaginous fishes. The authors address two functional questions regarding 1) agonist/antagonist specificity between ES GR/MR and 2) The functional role of the AB domain (N terminal domain) of the GR/MR which is known to play a specific role in GR transactivation. The study is technically well executed. However, the following should be addressed.

1) While the introduction is informative, it is difficult to follow as the authors describe ligand activities for two receptors, multiple ligands, multiple species and chimeras. While this information is summarized well in Table 1, it does not appear until well into the manuscript. It would help readers, I believe, to be more general in the introduction rather than provide a plethora of ligand specificities.

2) Given that a large component of the study focuses on the functionality of the GR A/B (AF1) activation domain here termed the "NTD" it would seem prudent to have some introduction and/or discussion on the role of this domain in NR's in general. Depending upon which of the NRs is being addressed the AB domain may serve multiple functionalities. For instance, the AB domain domain is a target site for receptor phosphorylation through differing kinase/phosphatase activities. Phosphorylation within the AF-1 domain can significantly affect transcriptional activity and impact ligand dependent and ligand independent activities. For example, Estrogen receptors are phosphorylated at both serine and threonine residues by mitogen activated kinase (MAPK) following growth factor stimulation and enhance transcriptional activity. PPAR and PPAR are additionally phosphorylated within the A/B domain yet exhibit reciprocal transcriptional activation (PPAR) and repression (PPAR). VDR and RXR also have putative phosphorylation sites. In this study, no mention is given to the role of Ab domain phosphorylation or how the functionality of the AB domain might be involved in allosteric interactions that facilitate ligand receptor binding.

3) As stated in comment 2 above, the study could also be greatly enhanced if the authors further conducted experiments to further refine the region of importance within the NTD that facilitates the activation of the GR. Alignment of the two sequences could help infer potential targets and functional mutation studies may provide greater mechanistic insight into the NR functionality and aid making evolutionary inferences in how MR and GR have diverged from human GR/MR. This aspect of the study could also be modeled using a three-dimensional molecular docking approach.

4) The experiments were conducted in HEK cells, which may or may not contain essential coregulators necessary for driving transactivation. It is also highly noticeable that MR activities are significantly attenuated compared to GR. Comment by the authors on both these points would be useful.

5) While the study recognizes the significant differences in EC50 across receptor types and their ligands, little attention is given to the Emax for each of the assays. It seems strange that ES-MR demonstrates a great potency for cortisol and corticosterone than GR however the Emax values for GR are magnitudes greater than MR.

Minor comments:

Why was the AF2 domain left out of Figure 2?

Reviewer #2

The authors report the first characterization of the elephant shark glucocorticoid receptor (GR). In my view, the experiments are a useful contribution to the literature, but the significance of the work as presented is limited.

They have two new findings:

1) The elephant shark GR does not activate in response to progesterone or 19norP, despite the steroids binding to the GR. This contrasts with their previously published characterization of the elephant shark MR (ref #36). GR from other organisms does not activate with progestins, but also does not bind them.

2) The GR N-terminal domain (NTD) dramatically increases the fold activation of the GR, but has no apparent effect on steroid specificity (Figure 4). This is a property of the NTD, as swapping the GR NTD onto the MR ligand-binding domain leads to elevated activity (Figure 6). This behavior matches what has been seen previously for bony-vertebrate GRs, but has not been demonstrated for cartilaginous fish GRs.

They have one finding that is somewhere between new and confirmatory:

3) The elephant shark GR behaves similarly to the previously characterized skate GR (refs #7, #37) in that it responds to both aldosterone and cortisol and has lower sensitivity to steroids than the MR.

Presentation:

I found this paper difficult to read. The introduction was long. It was difficult to tell from the introduction what was previously known and what was new in this paper. The results had little narrative structure, making it difficult to understand why the authors chose to do each experiment. And the discussion did not really explore the implications of their observations.

There are four data figures and a table. Of those, Figs 3, 4, and Table 1 are the same data shown in different ways. Of the data in these figures, the MR bits-about half of the data-have already been published for slightly different constructs of the same proteins (ref #36). The work was observational, with no mechanism – evolutionary, biochemical, physiological, or otherwise – presented.

Specific comments:

1) The authors never discuss the implications of their results for the physiology of elephant sharks. Why should it matter that the elephant shark GR does not respond to progesterone and 19norP? Is this surprising given what we know about GRs from other species?

2) The authors don't "close the loop" on their evolutionary questions regarding steroid specificity. How does their work contribute to our understanding of the evolution of the GR and its function across vertebrates? Can they propose when the progesterone response evolved (or was lost)? Was it gained on the MR lineage or lost on the GR lineage? (One of the papers the authors cite (Bridgham et al, #7) reports that the hagfish CR-which is co-orthologous to MR and GR from jawed vertebrates-responds to progesterone. It seems like this is worth bringing into their discussion). In general, a much more fleshed out discussion of what is known about GR and MR from other cartilaginous, ray-finned and jawless fishes is in order.

3) The authors argue that the importance of the NTD for GR activation, but not MR activation, indicates that the NTD activity evolved after the divergence of MR and GR. It is equally likely, however, that MR NTD lost its ancestral ability to activate. (This could be tested by, for example, characterizing full-length CR from hagfish or lamprey and asking if its NTD is more MR-like or GR-like in function.)

4) In the paragraph starting “Activation of elephant shark GR by aldosterone...”, the authors should probably note that the previously characterized skate GR responds to aldosterone and cortisol, as does the reconstructed ancestor of GR and MR (refs #7, #37). This adds heft to their claim that GR is transitional from MR in elephant shark.

5) The authors motivate their decision to characterize the full-length elephant shark GR by saying that because no full-length elasmobranch GR has been characterized, "the identity of the physiological glucocorticoids in cartilaginous fish is not known." This seems odd, given that, to a first approximation, most GR NTDs amplify the response to all steroids without dramatically altering specificity (see, Figure 4A and C, for example). Is there some reason the authors expect the NTD to alter specificity in this case? Further, all of the data in this manuscript are in vitro: this cannot show whether these steroids are physiological or not.

Minor comments:

In several places, the language the authors chose seems to imply that the elephant shark is ancestral. The sentences should be modified to indicate that the shark gives insight into an ancestral state, but is not itself ancestral.

Reviewer #1

This is a well carried out study of the ligand specificity and also the role of the NTD of elephant shark GR and MR. The study though, conflates two things – the role of the NTD in transactivation (it is well known that the NTD of steroid receptors contains a transcription activation function – TAF1) – and the role of the NTD in ligand binding (allosteric interactions between the NTD and the ligand binding domain; LBD). While it is possible that the NTD exerts an allosteric influence over the LBD, as suggested by the authors, I do not feel that this conclusion is justified by the data presented.

Major points:

1) The introduction conflates the two issues of allosteric interaction between NTD and LBD (e.g., as shown in ref 22) with the existence of a TAF in the NTD (demonstrated in ref 19 for example). The activation domain is autonomous, requiring tethering to DNA by the DNA binding domain of the receptor. This applies to the statement “It is not known when the strong dependence of vertebrate GR on the NTD for activation of gene transcription evolved”. However, it has also been demonstrated (though not in most of the references cited) that there is an allosteric interaction by which the GR NTD alters ligand binding (i.e., affinity) by the LBD, alluded to (albeit not explicitly) earlier on.

This is problematic when it comes to the way the data in Figure 3 are described. Activation of a reporter gene was measured, not activation of the receptor. If the reporter gene had not contained a GRE, there would have been no effect of steroid on the experimental readout, but the receptor would still have been activated by the steroid. What Figure 3 shows is that the GR NTD contains a strong transcriptional activation domain, required for induction of MMTV LTR-luciferase, consistent with previously published data. However, the MR does not have a TAF in the NTD (at least one active at this promoter); deletion of the NTD has no effect on transactivation of the reporter. The data in Figure 3 say nothing about the affinity of the receptors for the ligands. To infer anything about ligand-dependent activation of receptor, a ligand dose-response is required (as in Figure 4).

2) It is not clear if the EC50s reported in Table 1 are sufficiently (significantly) different to each other in order to infer anything about the influence of the NTD on ligand binding. No statistical analysis has been performed on the EC50s.

The similarities of the EC50s for all 4 corticosteroids for the truncated and full-length MR supports the EC50 being determined by the LBD and is consistent with no role for TAF1 at this promoter. For the GR, the EC50s reported in Table 1 derive from the data shown in Fig4. There are very minor differences in EC50 for corticosterone (the highest affinity ligand) between GR-FL, GR-truncated and the MR-GR chimera. This suggests the affinity of the receptor for this ligand is determined by the LBD. Likewise, the affinity of all 3 receptors for cortisol is within experimental error (with the additional caveat that the graphs in Figure 4 do not plateau for cortisol, so the estimate of EC50 is likely to be inaccurate; this caveat also applies to the statement “the EC50 for cortisol increased over 2-fold, and an EC50 for 11-deoxycorticosterone was too low to be calculated”). Aldo also doesn't reach plateau, so the same caveats apply there (and there is <3-fold difference between the EC50 for GR-FL and MR-GR). This I do not feel that the data support the conclusion drawn regarding allosteric signalling between NTD and LBD (“These results indicate that allosteric signaling between the NTD and DBD-LBD in elephant shark GR is critical for its response to corticosteroids, in contrast to elephant shark MR”).

3) The same issue arises in the description of the results of the chimera experiment (starting “Thus, in the GR NTD-MR DBD-LBD chimera...”). The reason that fusion of the GR NTD to MR LBD conferred greater activation of the reporter gene is because it fused a strong activation domain (TAF1) to the MR LBD. This also allowed the prog and 19norprog activation - the fusion of the GR TAF1 to the MR ligand specificity. This was to be expected. Similarly, the MR NTD does not contain a TAF (at least one active at this particular promoter). So it was only to be expected that a fusion of the MR NTD to GR LBD would lack the strong GR TAF.

Minor comments:

The authors might want to discuss RU486 (which binds to both GR and PR) with respect to the experiments shown in Figure 5.

Preprint Review

This preprint was reviewed using eLife’s Preprint Review service, which provides public peer reviews of manuscripts posted on bioRxiv for the benefit of the authors, readers, potential readers, and others interested in our assessment of the work. This review applies only to Version 1 of the preprint: https://www.biorxiv.org/content/10.1101/822718v1.full

Summary

This paper uses the sequences of and experiments involving the mineralocorticoid (MR) and glucocorticoid (GR) receptors from a cartilaginous fish (the elephant shark), a sister taxa to the ray-finned fish and terrestrial vertebrates, to investigate the early evolution of the specificity of these important steroid receptors.

The reviewers appreciate the value of studying the activity and specificity of steroid receptors (SR) from a taxon that diverged from its common ancestor with vertebrates close to 500 million years ago, but identified several important issues that they feel limit the impact of the manuscript. These are described in detail in the individual reviews.

1) In the interpretation of their experiments on the N-terminal domain (NTD), the authors conflate two things: the role of the NTD in transactivation and its role in ligand binding. This leads to a conclusion – that there is an allosteric interaction between the NTD and the ligand binding domain (LBD) – this is not demonstrated.

2) The in vitro characterization of the activity and steroid specificity of elephant shark SRs in an in vitro assay is a useful contribution. However, in the absence of a stronger relationship of these experimental observations to a biochemical mechanism of action, a specific evolutionary scenario, or to elephant shark physiology, the broader significance of these findings is unclear.

3) Some of the statistical analyses and evolutionary analyses need stronger support.