GDNF regenerates the missing enteric nervous system of Hirschsprung mice via non-canonical signaling in diverse subtypes of tissue-resident progenitors

Reviewer #1 (Public review):

Gary, Soret et al., present an interesting and ambitious study investigating the cellular and signaling mechanisms by which GDNF induces enteric neurogenesis in a disease model of HSCR. The manuscript combines scRNA-Seq, pharmacological inhibition, and several lineage-tracing strategies. The lineage tracing experiments in particular are technically impressive and clearly represent a substantial amount of work. The figures are generally beautiful and high quality, and the biological question is an important one.

However, while I found the study interesting, I also think that several of the major conclusions are substantially stronger than what the current data support. In particular, the scRNA-Seq dataset that the study is founded on is difficult to interpret because of the RFP-based enrichment strategy, the lack of WT reference controls, and the very non-stringent FACS gating. Several mechanistic claims are also based primarily on expression patterns or sequencing results.

Major concerns:

(1) The G4-RFP based enrichment strategy raises some concerns. The authors note that 88-90% of SOX10+ glial cells (where did this number come from, it doesn't seem to match the range in the bar graph?) and only 70% of GDNF-induced neurons. They then sort in "yield" mode using a non-stringent gating strategy, but do not provide the flow graphs in the supplements for interpretation. Consistent with this, the initial dataset contains multiple non-ENS populations, including lymphoid, myeloid cells etc, suggesting that their strategy, in addition to missing cell populations, additionally includes potential negative cells based on background fluorescence.

(2) It's not clear to me why the authors did not include a wild-type control for comparison. Due to the RFP-enrichment strategy, it is additionally difficult to compare to integrated with scRNA-seq datasets. The comparison seems important because the central question is not only whether GDNF induces neurons in the mutant colon, but whether the induced cells and associated populations resemble those found in a normal ENS.

(3) The proportional changes in Figure 2 are hard to interpret. The authors write that GDNF treatment leads to an enrichment in enteric neurons, "at the expense of" SCPs. This seems to be a strange conclusion or writing, unless the authors are suggesting that certain cell populations are additionally depleted by GDNF treatment. I think the authors should provide stronger support, or dial down on conclusions based on cluster proportions, given the sorting strategy.

(4) Some of the mechanistic conclusions are far too strong for the evidence. For instance, the claim that GDNF signals through GFRa1/2 based on only expression UMAPs is not justified. The authors should at least confirm some of the major findings via smFISH (HCR or RNA-Scope), and dial down the mechanistic claims. The pharmacological data is more supportive but still indirect. This section would be stronger if the authors validated NCAM1/FAK activation in the specific progenitor populations proposed to respond to GDNF.

(5) The inhibitors are administered during the same P4-8 window as GDNF. Given that the authors report cellular-level responses as early as 6 hours post GDNF treatment, it is important to know whether the inhibitors were already active at the time of GDNF administration. Why were the inhibitors not administered prior to the start time of GDNF treatment?

(6) The authors draw inferences and conclusions based on IHC images, but do not provide any details on the analysis procedures. For example, in Figure 3, the authors interpret changes in NCAM and FAK expression level. However, it does not appear that there are notable differences in intensity between the two timepoints. There are however, differences in signal coverage. Without knowing what was actually measured and quantified, it is not possible to interpret the results. Please provide the necessary information for all experiments in the methods section.

(7) The final results section introduces one of the more surprising claims in the paper, that a non-neural crest-derived progenitor contributes to regeneration, but the section ends quite quickly and abruptly after introducing the observation. The authors should provide additional validation or interpretations of the data.

Reviewer #2 (Public review):

Summary:

Previous work from this group demonstrated regeneration of the ENS following exogenous GDNF treatment within the aganglionic portion of the bowel in several Hirschsprung (HSCR) murine models as well as colon from HSCR patients (Soret, et. al., Gastro. 2020). Focusing on the Holstein (HolTg/Tg) HSCR mouse model, the authors build upon their prior work utilizing lineage tracing, immunohistochemistry, scRNA sequencing, and pharmacological methods to further delineate the mechanisms and cell types contributing to ENS regeneration in this context. This work adds to the knowledge base regarding natural ENS development as well as ENS generation outside of natural ENS development. Furthermore, this work provides important clinical implications for potential curatives treatments for HSCR disease.

The conclusions in the paper are overall well supported by the data with the majority of technical and model limitations openly acknowledged. Strengths include the use of scRNA sequencing, several genetic mouse models with ample, well-planned time points within experiments. However, additional analysis, clarity or more detail around experimental protocols, and broader discussion of prior studies would strengthen the manuscript by improving interpretation of the findings and placing them more clearly within the context of existing work in the field.

First, utilizing the G4-RFP transgene for ENS cell selection and subsequent scRNA sequencing of RFP+ cells, the authors nicely demonstrate the presence of known cell clusters (based on markers and analysis from prior sequencing studies) including Schwann cell precursors (SCPs), enteric glial cells (EGCs) and neuron subtypes in the aganglionic colon of HolTg/Tg GDNF-treated and untreated mice. Further use of this dataset led to the discovery of Ncam1 expression, a GDNF receptor, within all ENS cell clusters, suggesting importance of this protein in the GDNF-induced ENS regeneration phenotype. Interestingly, Ret was limited to some neuron types. On the protein level, temporal and GDNF-treatment changes in NCAM1 expression and downstream phospho-FAK(Y397) were nicely demonstrated via Western blot. Mechanistically, the importance of NCAM1 in ENS regeneration was demonstrated given pharmacologic blockade of downstream FAK signaling via PF-562271 resulted in significantly fewer GDNF-induced neurons. The paper would be strengthened here, however, if the following areas were addressed:

1) Although the GDNF-induced regeneration appears likely through an NCAM1 signaling mechanism, inhibition of FAK phosphorylation by PF-562271 could affect more than NCAM1 signaling. Blocking NCAM signaling through another method (such as through NCAM1 targeted monoclonal antibodies or small molecules) would support the authors' interpretations further.

2) A point of ambiguity is the exact cells included in the final scRNAseq analysis. The authors noted they flowed and gated broadly, including RFP negative cells, in the initial set of cells selected for sequencing (given RFP expression is not visualized within all neurons and glia in GDNF-treated HolTg/Tg mice.) Pan-neuronal (Elavl4, Tubb3) and pan-glial (Sox10) marker expression were utilized to select cells for final analysis (unsupervised analysis, pseudotime trajectories, etc.) Here, it is unclear if RFP expression was examined in these cells, either by looking at unmapped reads or if included in the initial alignment. If this is discernable within the authors' data set, this provides an opportunity for an interesting additional analysis to determine if progenitors or neuronal or glia populations differ in the RFP+ and RFP- groups.

3) The authors presumably sequenced both the submucosal and myenteric plexus ENS components within their scRNAseq analysis. Given the relatively sparse numbers of ENS cells in the submucosal plexus compared to myenteric plexus in the distal colon, this is unlikely to change their analysis or conclusions. However, given their tissue analysis focuses on the myenteric plexus, this difference should be acknowledged.

The authors go on to further to utilize their scRNA sequencing data set with pseudotime trajectory analysis to determine that SCPs appear to go through an EGC-like state prior to GDNF-induced neurogenesis. This was followed nicely by use of transgenic mice (Dhh-Cre) and immunohistochemistry within their HolTg/Tg model to capture the SCP population and demonstrate in vivo this progression. Additionally, they were able to demonstrate that temporally, SCPs generated neurons much sooner (within 6 hours of GDNF-treatment) compared to neural crest derived EGCs (labeled by Slc18a2-Cre and GFAP-CreERT2 lines).

Fascinating here as well is that the authors unearthed that most generated neurons following GDNF-treatment appeared to derive from direct cell transdifferentiation (suggested by EdU incorporation investigation at various time points) and that these neurons did not seem to originate from SCPs or EGCs (i.e. a non-neural crest origin.) Acknowledging that their mouse genetic tools and sequencing could have missed a NCC-derived population, the authors go on to label neural crest derivates utilizing the Wnt1-Cre2 transgene in their wildtype and HolTg/Tg mouse model and find that while Wnt1 labels the vast majority of neurons in wildtype mice, nearly 25% of neurons in P20 HolTg/Tg mice appear non-NCC derived. Finally, once again utilizing various genetic mouse lines for lineage tracing and immunohistochemistry, the authors demonstrate NCC-derived neural progenitors (SCPs, EGCs) appear to preferentially give rise to cholinergic neurons where non-NCC derived neurons tend to be more nitrergic.

4) The high magnification of the majority of images provides the reader with extremely compelling evidence in regard to visible overlap or lack thereof across various reporter lines, antibody markers, and EdU labeling. Unfortunately, this can somewhat create a trade off with the area or number of cells examined which appears somewhat less than the number of cells and/or area examined by many prior studies in the field. The near equal averages across the three mice in each group in many of their experiments makes this less of a concern, but the paper may be strengthened by noting exactly how the 3-11 images per mouse were selected. Were these randomly selected across the tissue, moving from mesenteric to anti-mesenteric? Or caudally to distally?

5) In line with this, the authors report a near 100% of Wnt1-Cre2 driven reporter expression in wildtype mice but a large portion (~25%) of neurons in HolTg/Tg model appear non-NCC derived (i.e. not Wnt1-Cre2 labeled.) The original Wnt1Cre line (Danielian, et.al., Curr Biol. 1998) has been reported to incompletely label all neural crest derivatives/ENS (Hari, et. al., Development. 2012.; Deal, et. al., Dev Bio. 2021). To my knowledge, the same type of analysis has not been carried out with the same rigor in the ENS with the Wnt1-Cre2 line. It could be -- depending on tissue sampling, area covered via imaging, and if there is any patchy or unique patterning to non-NCC derived neuro regeneration -- any incomplete labeling of neural crest by Wnt1-Cre2 could be missed. Of course, alternative interpretations are that the non-labeled cells are truly non-NCC derived. Utilizing other lineage tracing models for other non-NCC derived lineages may help address this issue, but would require many mouse crosses and additional experiments, and thus likely outside the scope of this manuscript. However, this caveat should be addressed.

6) A very important and fascinating find by the authors is that the NCC versus non-NCC derivatives appear to preferentially give rise to cholinergic or nitrergic neurons respectively. This will have important implications in treatment options for ENS regeneration not only within HSCR disease, but other ENS disorders as well. A point of discussion the authors missed out on is several previous reports regarding skewing of ENS neurons (typically toward higher nitrergic numbers) in ganglionic and/or hypoganglionic segments of HSCR bowel in murine models and patients (Zaitoun, et.al., Neurogastroenterol. Motil. 2013.; Musser, et.al, CMGH. 2015.; Cheng, et.al., J Pediatr Surg, 2017.; Sukhada, et. al., Front. Cell Dev. Biol. 2022.) Could ganglionic portions of the bowel in HSCR disease contain more of the non-Wnt1 labeled population? Why do proportions in the aganglionic region generate correct proportions following GDNF-induced treatment compared to ganglionic bowel? This does not need to be experimentally addressed in the manuscript, but including in the discussion impresses upon the audience the importance of the authors findings and that these factors need to be further experimentally delineated and considered with any therapeutic interventions.

Reviewer #3 (Public review):

Summary:

In this work, the authors aim to build on their previous work to further define the mechanism by which GDNF can induce enteric nervous system migration and differentiation in the Holstein mouse model (Hol Tg/Tg) of Hirschsprung's disease (HSCR). They show that GDNF can cause neuronal differentiation from either Schwann cell precursors (SCP) that migrate from the periphery and/or enteric glia (or neural crest precursors located in the intestine). Surprisingly, the rescue effect of GDNF is mediated through signaling with NCAM1 rather than the canonical receptor RET, with blockade of NCAM1 significantly reducing the number of GDNF-treatment induced neurons in the distal colon of Holstein mice. The authors then perform scRNA-seq data of the colonic ENS from Holstein mice +/- GDNF, and pseudotime analysis of this data indicates the SCP downregulate SCP genes and upregulate classical enteric glial genes on their transition to becoming enteric neurons. Following this, the authors employ Dhh-Cre mice (to label SCP), Slc18a2Cre and GFAPCreERT2 (to label enteric glia) and finally Wnt1Cre2 mice (to label neural crest derived cells) to assess the kinetics and end identity of enteric neurons driven by GDNF treatment. Using these animal models, the authors propose a model by which transdifferentiation of SCP gives rise to enteric neurons first, followed by transdifferentiation of enteric glia; the resulting enteric neurons labelled by Dhh, Slc18a2 or GFAP Cres are all biased to a cholinergic lineage, raising a questions about the source of nitrergic neurons. Finally, the authors postulate that at least some nitrergic neurons come from a non-neural crest lineage in GDNF treated Hol Tg/Tg mice as they are not labelled by a Wnt1Cre2 model, while all ENS cells are labelled in three wildtype Wnt1Cre2Tg/+;R26YFP/+ mice.

Strengths and Weaknesses:

This work convincingly shows that NCAM1 is required for GDNF-induced rescue of the Holstein mouse model of HSCR and, along with the NCAM1 staining in human HSCR tissue, highlights the potential of this treatment even in HSCR patients with loss of function RET mutations. The major weakness of this study is in the interpretation of the mouse models; many of these models are not fully penetrant/show mosaicism in other studies (like the DhhCre and Wnt1Cre) or may not only label the specific subpopulation they present (in this case, the GfapCreERT2 and Slc18a2Cre; these genes have been shown in Schwann cells/SCP in other studies, and the expression pattern of these two genes outside of the gut at the relevant developmental timepoints are not shown). While these are unavoidable limitations with our current mouse models, the authors need to clearly acknowledge these limitations in the interpretation of their data (with the DhhCre and Wnt1Cre) or more definitively show the models are only labelling enteric glia (in the case of the Gfap and Slc18a2Cre). In addition, in some figures the authors should add untreated Hol Tg/Tg and ideally WT mice so readers can contextualise the effect of GDNF on Hol Tg/Tg mice. Finally, it appears the statistics throughout the paper are performed on using each ROI taken from n=3-5 animals - this is inappropriate, as images from the same animal are not independent samples. The statistical unit in question for every analysis performed should be 1 animal, thus the statistics should be done on the n=3-5 animals, not the n=3-11 images from 3-5 animals (which leads to an n of 6-55).

Specific comments:

In general I find the author's conclusions are relatively well supported, albeit a little overstated for the evidence presented in the later figures and with the need to correct the statistical analysis. For Figures 1-5, I have only minor comments, as follows.

In Figure 1-2, the Gata4-RFP reporter is used to sort cells for scRNA-seq, and the authors get a large number of non-ENS cells so utilise Elavl4 and Sox10 expression to pull out neurons and glia to analyse. Do other putative neuronal/glial genes pull out the same cells, and can the authors find evidence of non-neural crest derived glia/neurons in this dataset? This would ensure there isn't a bias in this first analysis and strengthen the later claims respectively.

In Figure 3, the interpretation of increased NCAM1 and pFAK would be aided by adding the MFI for the untreated Hol Tg/Tg and ideally WT mice at p10 to assess if this is a normal developmental increase or induced by GDNF treatment - I would ask the authors add at least untreated Hol Tg/Tg at p10 as authors already present this data as images in figure 3D. Similarly, it would be nice to have neuronal counts of untreated Hol Tg/Tg and WT mice presented in Figure 4c to assess if NCAM1 inhibition completely or only partially prevents the effect of GDNF.

In the text accompanying Figure 2 and 5, the authors use a variety of markers of assign SCP or enteric glia identity to the clusters, but some of the enteric glia genes can be expressed by Schwann cells/SCP in other contexts - it is worth adding references to the genes chosen to define SCP and enteric glia so readers can understand why those were chosen and the strength of evidence for each marker. For me, with the exception of Dhh I do not find any of these genes definitive as, at least on the SCP/Schwann cell side, they have been shown to express Gfap, Slc18a2, Sox2 and single cell analysis indicates they also express Cpe. The ability for SCP/Schwann cells to express both Gfap and Slc18a2 is important for the interpretation of the upcoming experiments.

In Figure 6, the authors state in line 213 that "quantitative analysis as a function of time revealed that GFAP+ cells in the distal colon are not all derived from Dhh-expressing SCPs on the first day of treatment"; however, the DhhCre is restricted to specific SCP subsets (Xie, Meng, et al. "Schwann cell precursors contribute to skeletal formation during embryonic development in mice and zebrafish." Proceedings of the National Academy of Sciences 116.30 (2019): 15068-15073) and thus may not be labelling all SCP coming into the intestine. As far as I know there are no models that would allow labelling of all SCP without labelling enteric glia so would require the generation of a new models or techniques that is out of scope for this work - however, the authors should acknowledge the possibility of Dhh negative SCP contributing to the ENS.

Figure 7 and 8 focuses on the contribution of Dhh+ cells, Slc18a2+ cells and cells expressing GFAP between p3-p8 to the ENS of GDNF treated Hol Tg/Tg mice. The authors first show that by p20 the number of neurons per mm2 is equivalent to those at p60, indicating p20 as an appropriate timepoint to assess the relative contribution of each pool of glia to the resulting neurons. The authors show that neurons derived from a DhhCre are detectable first, then Slc18a2, followed finally by GFAP. This data supports the authors claims that neurons first arise from Dhh+ SCP, but as I raised earlier, both Slc18a2 and GFAP can be expressed by schwann cells later in development - the authors in fact show that GFAP is in fact expressed by Dhh+ cells in figure 6, and showed with pseudotime analysis that SCP undergo a transition to Gfap+ Slc18a2+ glial cells before becoming neurons. The data presented here negates that analysis, or at least suggests some Dhh+ cells skip this step, otherwise the kinetics of neuronal differentiation would align across the 3 lines used. Could the authors address this discrepancy? For example, one addition could be to show that SCP/schwann cells on extrinsic gut innervating nerve fibres do not express Gfap or Slc18a2 at the timepoints used. In addition, their scRNA-seq analysis suggests that Gfap & Slc18a2 are expressed in the same cells, so one would expect similar kinetics in both populations - what is the overlap of GFAP staining with Slc18a2-YFP expression at the earlier stages (say p6 and p10?). Alternatively, the inducible nature of the GFAPCreERT2 means some bona fide GFAP expressing cells may be missed if the tamoxifen dose is not saturating, thus underestimating the contribution of this population to the total neuron count. As such, could the authors please show co-staining with GFAP in some induced GFAPCreERT2 samples to assess the effectiveness of this Cre. As with other figures, it would also be nice to add Holstein negative reporters at p20 as a control to assess the level of contribution each one of these cell lineages has in a normally developing animal compared to GDNF treated Hol Tg/Tg mice.

In Figure 9, the authors show that neurons derived from labelled cells in the DhhCre-YFP or Slc18a2Cre-YFP skew strongly cholinergic (81%) compared to nitrergic (13%), but only 52% of the total neurons in GDNF treated Hol Tg/Tg mice are cholinergic, while 42% are NOS1+. The authors say that a similar trend is seen in Slc18a2Cre-YFP mice with a 'slightly higher percentage' reflecting Slc18a2 expression in neurons. However, this 'slightly higher' percentage looks to be about 40%, which is the amount expected in GDNF treated Hol Tg/Tg. I think the authors underplay the level of nitrergic neurons that are labelled in the Slc18a2Cre mice and should consider the possibility that Slc18a2+ glia can give rise to the nitrergic neurons seen in GDNF treated Holstein mice. This data also contrasts with prior reports that indicate SCP tend to become NOS1 expressing in a Ret or Ednrb loss of function HSCR model (Uesaka, Toshihiro, et al. "Enhanced enteric neurogenesis by Schwann cell precursors in mouse models of Hirschsprung disease." Glia 69.11 (2021): 2575-2590), a discrepancy worth discussing.

In Figure 10, the authors assess the contribution of neural crest to the ENS of WT and Hol Tg/Tg mice using a Wnt1Cre2 line, and conclude there is non-neural crest contribution to the ENS of GDNF treated Hol Tg/Tg mice. This is an interesting idea and supported by a few studies the authors mention in the discussion; however, the labelling of neural crest derived cells in Wnt1Cre2 may not be fully penetrant. While this line has a well established leaky phenotype, others have reported it can have patchy recombination in the neural crest too (potentially in a background dependent manner, according to the line information on Jackson laboratories). For example, recent works shows significant mosaicism in the embryonic phase (Gandhi, S., Du, E. J., Pangilinan, E. S., & Harland, R. M. (2024). The Wnt1-Cre2 transgene causes aberrant recombination in non-neural crest cell types. bioRxiv, 2024-11.) This may not be the case in the authors home institution in a FVB background, as they show all HuCD+ and Sox+ cells overlap with the Wnt1Cre2 reporter, but the Hol Tg/Tg mice have aberrant neural crest development - this could interfere Wnt1 expression thus the effectiveness of the Wnt1Cre2, thus leading to non-labelled, but actually neural crest derived cells. It is also possible that those neurons are truly from a non-neural crest background, and the neural crest labelling tools are all flawed in one way or another - as such, I think the authors just need to discuss this alternative possibility in the discussion.

Finally, Figure 11 shows NCAM1 expression in human tissue resections from HSCR patients. This data bolsters the idea that GDNF treatment could be an effective treatment for HSCR. The methods indicate that 3 tissue samples from HSCR patients were obtained, but staining is only shown for one - could all 3 be included, along with secondary only controls? This is important as human tissue resections are often processed many hours after removal, so are prone to higher background. It would also be interesting to include tissue from non-HSCR patients (the controls used most often in other studies are resections from anorectal malformations which are performed at approximately the same age as HSCR resections) to see if NCAM1 expression is influenced by the absence of an ENS in human patients, but I understand these samples are not always possible to obtain. If not possible, the authors could consider analysing publicly available RNA sequencing datasets to assess if RET is solely expressed in mature neuronal populations while NCAM1 is expressed by glial and neuronal populations like in their mice data.

Overall, the authors clearly show that GDNF can drive differentiation of neurons from different glial populations through NCAM1 not RET, and supports continued effort to translate this work to the clinic as a potential therapy for HSCR patients. I am not convinced that the relative contributions of each glial subpopulation can be extrapolated from the mouse models used - this is a problem across the field, and will only be rectified with the development of new models, which is out of scope for this work. This work complements recent work showing NCAM1-GDNF signaling promotes neurogenesis in glia in Ednrb-/- mice (Mueller, Jessica L., et al. "Intramuscular enteric glia persist in Hirschsprung disease and undergo neurogenesis in response to GDNF-NCAM1 signaling." Scientific Reports 15.1 (2025): 33200), and will add to our understanding of neural development.

Reviewer #4 (Public review):

Summary: The manuscript by Gary et al works to reveal processes that generate enteric neurons in the distal colon of Holstein mutant mice that experience aganglionosis and are an established model of Hirschsprung disease (HSCR) following GDNF enema infusion. The primary goal of the study is to determine the how rectal infusion (enema) of GDNF drives neurogenesis in these mutants. The studies focus on determining the molecules that mediate this GDNF effect and identifying the cellular origins of the newly formed neurons. Given that prior work from this group and others has indicated formation of postnatal enteric neurons is feasible, understanding this process is an important step for the field. The data presented partially support the claims of the study. The analysis described do not support unequivocable conclusion that "transdifferentiation" is occurring. To instill confidence in the stated conclusions and make the text appropriately clear, clarifications of the methods and additional information is needed.

Strengths:

(1) The authors use in vivo experimentation with multiple mouse lines including Dhh-cre, Slc18A2-cre, and GFAP-creERT2 to trace the production of enteric neurons in the context of GDNF enema in the established Holstein mouse model of Hirschsprung disease over a time line of postnatal days 4 (P4) to P10.

(2) The authors generate novel molecular profiles of enteric neurons induced in the distal colons of Holstein HSCR mice after GDNF enema induction by flow sorting for fluorescently labeled and adjacent populations with novel gating parameters followed by single cell RNA-sequencing.

(3) The authors recognize broad expression of NCAM1 amongst the induced neurons in scRNA-seq data and apply experimental approaches to further investigate the role NCAM1 in generation of GDNF-induced ENS neurons.

(4) The authors apply a widely utilized experimental approach, EdU-labeling, to assess proliferation in the immediate timeframe of GDNF-inducation in an effort to discern the timing of when the newly produced neurons exit the cell cycle.

Weaknesses:

(1) The article lacks sufficient information justifying use of the Holstein HSCR mouse model for the study. Authors need be more thorough when introducing the readers to the various HSCR mouse models they consider analyzing and provide an expanded justification for use of the Holstein model in the introduction so the audience can appreciate the rationale behind the analysis presented.

(2) The text minimally describes the G4-RFP reporter that is a critical element of the analysis and upon which the scRNA-seq profiling hinges. Given the data presented in this submission it's not clear how much of the ENS this G4-RFP line labels.

(3) The authors state that "NCAM1 is already present in SOX10+ cells before GDNF treatment begins at P4, both within and outside extrinsic nerve fibers (Fig.3b,c)." However, the data shown in Figure 3 panels B and D do not allow one to conclude co-localization of Sox10 with NCAM1 or FAK. Because ENS cells are so closely positioned with one another the signal the authors present could be due to adjacent cells or processes of cells above and below the plane of Sox10+ nuclei.

(4) The authors use the inhibitor PF-562271 in an attempt to specifically inhibit phospho-FAK[Y397] shown in Figure 4. This particular inhibitor has the known side effect of causing apoptosis in phospho-FAK[Y397]+ cells as shown by Hu et al 2017 Cancer Sci (DOI: 10.1111/cas.13256). Because this compound causes apoptosis in phospho-FAK[Y397]+ cells, the data presented do not prove that the lack of neurons produced in this condition is due to inhibition of phospho-FAK[Y397]+ cells making the neurons versus those phospho-FAK[Y397]+ cells simply dying very early in the process.

(5) In the text describing the results of Figure 1A compared to Figure 1B the authors have missed an opportunity to elaborate on the spatial distribution of what appear to be small ganglia in the GDNF treated colon of Holstein mutant mice. The schematic shown is rather simple and it's unclear from the text where these ganglia are distributed circumferentially around the gut wall.

(6) The immunohistochemical labeling for Phox2b shown in Figure 6 is odd. Phox2b is expressed in neuronal progenitors, enteric glia, and ALL enteric neurons as shown in multiple publications. The images shown in Figure 6 offer an outlined region that appears to be a ganglion; however, within that encircled area fewer than half of the cells are labeling with Phox2b by this study.

(7) The authors conclude that "transdifferentiation" is the origin of the ENS neurons that appear in GDNF-treated Holstein mice. However, the data show simply that most of the newly produced neurons have not recently gone through cell division based on lack of EdU incorporation. Given the data presented, other mechanisms may be occurring and should be considered as possibilities.

(8) The authors utilized a Wnt1-cre2 transgenic line that has known issues with expression in the male germline and ectopic expression in cells that are dependent upon the reporter line utilized, like the Rosa26-YFP of this study. The methods lack information on whether crosses were performed in such a manner as to avoid issues with male germline activation of this reporter and the potential for ectopic expression cannot be excluded based on the information provided in the study.

(9) The study lacks data on how GDNF enemas affect enteric neuron density and ganglia distribution in wildtype animals. If the signaling mechanism that produces new neurons in the Holstein model is also operating in wildtype animals, this could be crucial information for investigators interested in neuronal replacement to treat ENS damage resulting from environmental damage, disease, or age.