The Role of the Gut Microbiota in Sanfilippo Syndrome’s Physiopathology: An Approach in Two Affected Siblings
, MarÃa Garriga-GarcÃa 2,†, Ana Moreno-Blanco 1,3, Esther Palacios 1, Pedro Ruiz-Sala 4,5, Saioa Vicente-SantamarÃa 2, Sinziana Stanescu 6, Amaya Belanger-Quintana 6, Guillem Pintos-Morell 7, Beatriz Arconada 8, Rosa del Campo 1,3,9,* and José Avendaño-Ortiz 1,3,*Round 1
Reviewer 1 Report
Comments and Suggestions for AuthorsBarbero-Herranz et al describe differences observed in the microbiome of two siblings with MPSIII. Although only two patients were analyzed, the cohort is interesting, considering both patients have the same genetic variants, share the same environment, and have similar diets while having distinct gastrointestinal symptoms.
The authors explore this by assessing the microbiome diversity and the abundance of bacterial strains. Furthermore, they evaluate the ability of some strains to degrade heparan sulfate and the inflammatory response to the fecal metabolites.
I have a few minor suggestions, mostly to increase the clarity of the manuscript, and one major question, which could potentially result from my lack of expertise in this specific assay.
Major issue:
In figure 4, why only fecal metabolites from MPSIII patients were used? Although there are some differences pointed out, I cannot rule out that these are simply from the fact that you are incubating the monocytes with fecal metabolites. I see the unstimulated control as the baseline only, not as a control to be used for direct comparison and statistical analysis. I believe including monocytes stimulated with fecal metabolites from healthy volunteers is a must, particularly considering you are assessing only 2 patients, and the responses seem to be highly variable between the patients.
Minor issues:
I find the sentence on lines 138-140 unclear. I suggest rewriting it for clarity.
On lines 148-153, the authors show that Levomepromazine has higher inhibitory activity in Bacteroides spp compared to other strains. This paragraph ends abruptly, and a final sentence mentioning this correlates with the patient who takes Levomepromazine having lower Bacteroides spp abundance would bring more fluidity and clarity to the text. When reading it, I had to go back and forth to make this connection.
Line 195 – “Bacteria were cultured in the presence of 75 µg/mL at 37°C under anaerobic conditions for 48h” – I believe the component is missing from the sentence.
Figure 5—This figure shows the in vitro GAG degradation activity of bacteria isolated from MPSIII patients. The description says the data are from 4 independent experiments. Please indicate how many patients were included (were these the 2 siblings, or are these samples from a larger patient cohort?). These details should be clarified to allow for proper assessment of these results.
Overall, the manuscript is very interesting and well-written. If I may, I would suggest adding a one-sentence discussion/conclusion line after each main result to contextualize the experimental finding with what is observed in the patient. I understand these are different writing styles, though I find the lack of these sentences makes the reading somewhat harder, as the text changes abruptly from one assay to another without much context and fluidity.
Author Response
Comment 1: Barbero-Herranz et al. describe differences observed in the microbiome of two siblings with MPSIII. Although only two patients were analyzed, the cohort is interesting, considering both patients have the same genetic variants, share the same environment, and have similar diets while having distinct gastrointestinal symptoms. The authors explore this by assessing the microbiome diversity and the abundance of bacterial strains. Furthermore, they evaluate the ability of some strains to degrade heparan sulfate and the inflammatory response to the fecal metabolites. I have a few minor suggestions, mostly to increase the clarity of the manuscript, and one major question, which could potentially result from my lack of expertise in this specific assay.
Response 1: We thank the reviewer for his/her kind summary of our work.
Comment 2: Major issue: In figure 4, why only fecal metabolites from MPSIII patients were used? Although there are some differences pointed out, I cannot rule out that these are simply from the fact that you are incubating the monocytes with fecal metabolites. I see the unstimulated control as the baseline only, not as a control to be used for direct comparison and statistical analysis. I believe including monocytes stimulated with fecal metabolites from healthy volunteers is a must, particularly considering you are assessing only 2 patients, and the responses seem to be highly variable between the patients.
Response 2: We are very grateful to the reviewer for this comment, which has helped us significantly improve our work. Following this recommendation, we have repeated the experiment including stimulation with monocytes from healthy individuals. Thanks to this suggestion, we have observed that the increase in oxidative stress and inflammatory cytokine production is significantly higher in monocytes stimulated with fecal metabolites from the GIS+ patient when compared to the response generated by metabolites from healthy individuals. The new figure with this new information is now included in our manuscript.
Comment 3: Minor issues: I find the sentence on lines 138-140 unclear. I suggest rewriting it for clarity.
Response 3: Following the reviewer’s suggestion, we have modified the sentence accordingly.
Comment 4: On lines 148-153, the authors show that Levomepromazine has higher inhibitory activity in Bacteroides spp compared to other strains. This paragraph ends abruptly, and a final sentence mentioning this correlates with the patient who takes Levomepromazine having lower Bacteroides spp abundance would bring more fluidity and clarity to the text. When reading it, I had to go back and forth to make this connection.
Response 4: We agree with the reviewer’s comment. In the current version, we have added a sentence explaining that the patient taking such treatment is the one with the lowest abundance of Bacteroides spp.
Comment 5: Line 195 – “Bacteria were cultured in the presence of 75 µg/mL at 37°C under anaerobic conditions for 48h” – I believe the component is missing from the sentence.
Response 5: We thank the reviewer for this comment. The compound we are referring to is Heparan Sulfate (HS). This error has been corrected in the revised manuscript.
Comment 6: Figure 5—This figure shows the in vitro GAG degradation activity of bacteria isolated from MPSIII patients. The description says the data are from 4 independent experiments. Please indicate how many patients were included (were these the 2 siblings, or are these samples from a larger patient cohort?). These details should be clarified to allow for proper assessment of these results.
Response 6: Following the reviewer's recommendation, we have specified in the current version that these are isolates from MPS III patients included in this study.
Comment 7: Overall, the manuscript is very interesting and well-written. If I may, I would suggest adding a one-sentence discussion/conclusion line after each main result to contextualize the experimental finding with what is observed in the patient. I understand these are different writing styles, though I find the lack of these sentences makes the reading somewhat harder, as the text changes abruptly from one assay to another without much context and fluidity.
Response 7: We thank the reviewer for this comment, which helped us improve our manuscript. Following his/her advice, we have added concluding sentences before the end of the main paragraphs of the results sections 2.2, 2.3 and 2.4.
Author Response File: 
Author Response.pdf
Reviewer 2 Report
Comments and Suggestions for Authors
The manuscript discovered a role of gut microbiota in gastrointestinal symptoms of MPS III. the sibling with chronic diarrhea exhibits lower abundance of Bacteroides spp. and Sus genes along with higher fecal HS and lower SCFAs than the symptom-free sibling. I do have a few questions and minor edits that I believe the authors can address to improve the quality of this manuscript.
1. Title page: would author please include English translation of your institutions?
2. Line 57: missing a space in between “MPSIII”.
3. Line 120 and Figure 1A: The only clear trend of decreased alpha diversity is in Chao1, the Shannon index does not seem to differ, and it is hard to tell for faith PD without statistics.
4. Figure 1B and C: the legend for bacteria family and genera are very blurry.
5. It would be nice to add a beta diversity plot in figure 1.
6. Line 125: “regardless of the statistic used,” The correct term should be alpha diversity metrics. Because there was no statistical involvement regarding the comparison.
7. Line 126-127”: the number in the text does not agree with the number in figure 1A.
8. Figure 2: Why there were only two data points for healthy volunteers, which two of the four volunteers’ samples were used for PCR? Or they are from different volunteers from figure 1?
9. Line 172-173: Include p-value when claiming statistically significant. Also, are oxidative stress in GIS+ and GIS- different?
10. Line 176-178: were you referring to the comparison between GIS+ and GIS-? “the other” was very confusing. You can include the actual p-value and claim there is a trend in cytokine production if the difference were numerically large.
11. Line 188-192: please expand the description of the result. Are group Bt and Bf different from each other? Are PBS and Bf different? Also include the corresponding statistics for the additional comparison.
12. Line 196: in the presence of 75 μg/mL what chemical?
13. Line 327: Which database was used for taxonomy analysis? Please also include the citation for the database and DADA2.
14. Line 331: In your SRA experiments from NCBI database, why all samples are called 16S of fecal samples lung cancer patient? https://www.ncbi.nlm.nih.gov/sra?linkname=bioproject_sra_all&from_uid=1113948
15. Please provide 16S result (e.g. an ASV table) in the supplemental materials.
16. Line 388-390: MALDI-TOF are not very reliable at species level identification. In Li et al 2019 manuscript, they reported Bacteroides fragilis and Bacteroide thetaiotaomicron can be incorrectly identified by Bruker MALDI Biotyper (see Table 4). https://bmcinfectdis.biomedcentral.com/articles/10.1186/s12879-019-4584-0.
Is the identity of two isolates confirmed by sequencing?
Author Response
The manuscript discovered a role of gut microbiota in gastrointestinal symptoms of MPS III. the sibling with chronic diarrhea exhibits lower abundance of Bacteroides spp. and Sus genes along with higher fecal HS and lower SCFAs than the symptom-free sibling. I do have a few questions and minor edits that I believe the authors can address to improve the quality of this manuscript.
Response: We would like to express our gratitude for the meticulous review and thoughtful suggestions of this reviewer. They have greatly enhanced the clarity and depth of the article.
Comment 1. Title page: would author please include English translation of your institutions?
Response 1: We agree that a translation of the institutions would help to understand the context of the work team. Unfortunately, our institutions force us to cite them in our native language to unify and help search engines when evaluating scientific production.
Comment 2. Line 57: missing a space in between “MPSIII”.
Response 2: We regret this typographical error, and thank the reviewer for its identification. This error has been corrected in the revised version.
Comment 3. Line 120 and Figure 1A: The only clear trend of decreased alpha diversity is in Chao1, the Shannon index does not seem to differ, and it is hard to tell for faith PD without statistics.
Response 3: We thank the reviewer for this insightful comment. The p-values are 0.06 for the Chao1 and Faith and 0.64 for Shannon. We thought it convenient not to add the statistics here because there were only 2 patients, and the statistical power is therefore low. However, it is clear that Chao1 and FaithPD are lower in the MPS III patients as the values from the 2 patients are all below the values from all the 4 healthy volunteers. Following the suggestion, we have corrected the generalization we stated in the previous version and now just state that the Chao1 and FaithPD rates are lower in patients.
Comment 4: Figure 1B and C: the legend for bacteria family and genera are very blurry.
Response 4: We fully agree with the reviewer feedback. In the current version we have improved the Figure 1 resolution.
Comment 5. It would be nice to add a beta diversity plot in figure 1.
Response 5: We thank the reviewer for this comment. In the current version, we have added a PCA plot of the Bray–Curtis beta diversity index.
Comment 6. Line 125: “regardless of the statistic used,” The correct term should be alpha diversity metrics. Because there was no statistical involvement regarding the comparison.
Response 6: We fully agree with this comment. In the current version, we have changed the term “statistic” for “diversity indexes.
Comment 7. Line 126-127”: the number in the text does not agree with the number in figure 1A.
Response 7: We would thank the reviewer for identifying this mistake. The data in the text corresponded to a preliminary analysis in which we only had data from two healthy volunteers. In the current version we have corrected it.
Comment 8. Figure 2: Why there were only two data points for healthy volunteers, which two of the four volunteers’ samples were used for PCR? Or they are from different volunteers from figure 1?
Response 8: We thank the reviewer again for identifying such details. As in the previous comment, the figure corresponded to a preliminary analysis when we only had data from two healthy individuals. The current corrected version already includes data from the 4 healthy individuals included in the study.
Comment 9. Line 172-173: Include p-value when claiming statistically significant. Also, are oxidative stress in GIS+ and GIS- different?
Response 9: We fully agree with this comment. Following the advice from another reviewer, we have repeated this experiment including stimulation with fecal metabolites from healthy volunteers. In the current version, we have included the p-values for the comparisons of fecal metabolite effects between healthy volunteers and MPS III patients, as well as separating MPS III patients into GIS+ and GIS- groups. We have found that GIS+ but not GIS- fecal metabolites induce significantly more oxidative stress and inflammation (IL-6, TNF-a) than those from healthy individuals.
Comment 10. Line 176-178: were you referring to the comparison between GIS+ and GIS-? “the other” was very confusing. You can include the actual p-value and claim there is a trend in cytokine production if the difference were numerically large.
Response 10: As mentioned in the previous response, the p-values are now included in the current version of the manuscript. The term “the other” has been also corrected.
Comment 11. Line 188-192: please expand the description of the result. Are group Bt and Bf different from each other? Are PBS and Bf different? Also include the corresponding statistics for the additional comparison.
Response 11: We appreciate the reviewer’s insight and agree with his/her evaluation. In the previous version, we performed the post Kruskal-Wallis multiple comparison with respect to the PBS control only. In the current version, we followed the recommendation and compared each group between each other. The p-values for both multiple comparisons and Kruskal-Wallis are now included in the manuscript.
Comment 12. Line 196: in the presence of 75 μg/mL what chemical?
Response 12: We thank the reviewer for this comment. The chemical we were referring to was Heparan Sulfate (HS). This error has been corrected in the revised manuscript.
Comment 13. Line 327: Which database was used for taxonomy analysis? Please also include the citation for the database and DADA2.
Response 13: In the current version, this information has been included in the methodology section.
Comment 14. Line 331: In your SRA experiments from NCBI database, why all samples are called 16S of fecal samples lung cancer patient? https://www.ncbi.nlm.nih.gov/sra?linkname=bioproject_sra_all&from_uid=1113948
Response 14: We appreciate the reviewer for notifying us this observation. This error is now corrected.
Comment 15. Please provide 16S result (e.g. an ASV table) in the supplemental materials.
Response 15: We thank the reviewer for this recommendation. We have included the ASV table of the 16S sequencing data as Supplementary Table 1.
Comment 16. Line 388-390: MALDI-TOF are not very reliable at species level identification. In Li et al 2019 manuscript, they reported Bacteroides fragilis and Bacteroide thetaiotaomicron can be incorrectly identified by Bruker MALDI Biotyper (see Table 4). https://bmcinfectdis.biomedcentral.com/articles/10.1186/s12879-019-4584-0. Is the identity of two isolates confirmed by sequencing?
Response 16: We agree with the reviewer that, although the MALDI Biotyper is the quickest method of identification, it may not yet be fully conclusive in identifying Bacteroides species. To confirm that the isolate identified as Bacteroides thetaiotaomicron is indeed this species, we performed PCR with the species-specific BTH primers described by Teng et al. (PMID: 10747167). This information is now included in the revised version of the manuscript. The image of the DNA PCR products of the strains identified as Bacteroides thetaiotaomicron and Bacteroides fragilis is attached below. Although, in the future we would like to whole sequence the isolates, we have not yet been able to do so.
Figure: PCR products analyzed by electrophoresis on a 1.5% agarose gel of a 30 cycles PCR at 56ºC annealing temperature using BTH primers from Teng et al. (PMID: 10747167) and AmpliTaq Gold 360 DNA Polymerase kit. 100pb, 100 pb DNA ladder; C-, negative control using elution water as template; BT, product using DNA from isolate identified as Bacteroides thetaiotaomicron as template; BF, product using DNA from isolate identified as Bacteroides thetaiotaomicron as template.
Author Response File: Author Response.pdf
Round 2
Reviewer 1 Report
Comments and Suggestions for AuthorsI appreciate the author’s efforts to address the reviewers’ concerns. However, I am concerned about the statistics and the conclusions drawn from some of the experiments.
In Figure 4, I can see that the MPSIII seems to increase the stress and inflammatory parameters assessed, but I see these plots and measurements as pseudoreplication. Take the GIS+ group, for example. You have only one patient, with 2 fecal samples and 5 different monocytes. If you keep all the 10 points, you are actually measuring the variability of your assay, of different monocytes, and the two fecal samples, and not the variability of the GIS+ MPSIII population. So you should be careful when inferring that “the fecal metabolites from GIS+ patient induced higher oxidative stress and inflammation than the HV fecal metabolites”
I am far from being a statistic expert, but I see it this way:
If you average the measurements between the 2 fecal samples for each monocyte, you will assess the differences between monocytes;
If you average the measurements between the 5 monocytes for each fecal sample, you will see the differences between the fecal samples;
If you average everything, you will get a representative value for the patient with GIS+. To add more data points to the plot, you would need to acquire data from more GIS+ patients.
Ideally, in my point of view, to obtain a more accurate measure of the GIS+ population, you should have more patients with multiple fecal samples (to average them and account for fecal sample variability) and use only one monocyte donor across all fecal samples (since monocytes can vary greatly). Or use multiple monocyte donors and average them per individual. The same should be done for all groups. This way, you would be isolating all variables and would be comparing the true value of each individual in each of the groups. Then, statistical tests can be applied.
The Kruskal-Wallis test does not account for repeated measures within individuals, and If you treat repeated measurements from the same individual as independent observations, you are pseudoreplicating your results.
To draw any of the conclusions obtained from Figure 4 that are supposedly backed up by statistical analysis, you need to include more patients. This also applies to Figures 2 and 3, which compare and statistically analyze HV and MPS III. You don’t have 4 measures for MPSIII; you have only 2.
This study is interesting, but I see it as more descriptive and suggestive of the potential differences that occur within MPSIII patients. Once the sample sizes are increased, we can get closer to the true population mean and draw more conclusions. Therefore, I suggest either increasing the sample size or reformulating the manuscript to be more descriptive and less conclusive.
Author Response
Comment 1: I appreciate the author’s efforts to address the reviewers’ concerns. However, I am concerned about the statistics and the conclusions drawn from some of the experiments. In Figure 4, I can see that the MPSIII seems to increase the stress and inflammatory parameters assessed, but I see these plots and measurements as pseudoreplication. Take the GIS+ group, for example. You have only one patient, with 2 fecal samples and 5 different monocytes. If you keep all the 10 points, you are actually measuring the variability of your assay, of different monocytes, and the two fecal samples, and not the variability of the GIS+ MPSIII population. So you should be careful when inferring that “the fecal metabolites from GIS+ patient induced higher oxidative stress and inflammation than the HV fecal metabolites”
Response 1: We would like to express our gratitude for the thoughtful suggestions regarding the statistics provided by this reviewer. We agree, it is not adequate to perform statistical comparisons in only two patients. Following his/her recommendation, in the current version, we have eliminated the statistical results in Figures 2, 3 and 4. In addition, for all these figures, to avoid pseudoreplication of technical replication, we have now represented as dots the mean from all the replicates. Each point now represents the mean value of the replicates for each fecal sample. This information has been included in the figure legends. We have also avoided generalizations by changing phrases and have replaced verbs such as "indicated" or "revealed" with "suggested" or "showed". All the changes in the manuscript carried in the second revision are highlighted in green.
Comment 2: I am far from being a statistic expert, but I see it this way: If you average the measurements between the 2 fecal samples for each monocyte, you will assess the differences between monocytes; If you average the measurements between the 5 monocytes for each fecal sample, you will see the differences between the fecal samples; If you average everything, you will get a representative value for the patient with GIS+. To add more data points to the plot, you would need to acquire data from more GIS+ patients. Ideally, in my point of view, to obtain a more accurate measure of the GIS+ population, you should have more patients with multiple fecal samples (to average them and account for fecal sample variability) and use only one monocyte donor across all fecal samples (since monocytes can vary greatly). Or use multiple monocyte donors and average them per individual. The same should be done for all groups. This way, you would be isolating all variables and would be comparing the true value of each individual in each of the groups. Then, statistical tests can be applied. The Kruskal-Wallis test does not account for repeated measures within individuals, and If you treat repeated measurements from the same individual as independent observations, you are pseudoreplicating your results.
Response 2: Following the reviewer recommendation, we have now represented as dots the average value from the 5 different monocytes stimulation. We thank the reviewer for this comment, as the dispersion of the data has been now reduced. As stated above, Kruskal-Wallis and all statistical analyses in figures 2, 3, and 4 have been also removed. Kruskal-Wallis statistic only remains in the Figure 5 for the HS in vivo degradation assay.
Comment 4: To draw any of the conclusions obtained from Figure 4 that are supposedly backed up by statistical analysis, you need to include more patients. This also applies to Figures 2 and 3, which compare and statistically analyze HV and MPS III. You don’t have 4 measures for MPSIII; you have only 2. This study is interesting, but I see it as more descriptive and suggestive of the potential differences that occur within MPSIII patients. Once the sample sizes are increased, we can get closer to the true population mean and draw more conclusions. Therefore, I suggest either increasing the sample size or reformulating the manuscript to be more descriptive and less conclusive.
Response 4: We understand the comment of the reviewer, although we do not fully agree with it. We would like to remind that MPS III is a very rare and extremely infrequent disease, so is difficult to recruit additional patients. In addition, there are up to 4 distinct subtypes (PMID: 37947910), each one with different associated mutations in different genes and different heparan-degrading enzyme activities. This makes it difficult to group patients and the analysis must be individualized. This is further complicated with respect to microbiota analysis because age, diet, or type of feeding (some MPS patients use a feeding tube) could be confounding variables. The strength of our work is that they were siblings with exactly the same mutation, the same diet, and practically the same age. Although we agree that the results cannot be generalized to all MPS III patients, we consider that our results are novel and relevant, particularly for patients suffering from gastrointestinal symptomatology. We have briefly expanded discussion on these weaknesses and strengths of our work is included in the discussion section. As mentioned above, we tried to avoid generalization by replacing some phrases stating “MPS III patients” to “the two MPS III patient included in the study.”
Reviewer 2 Report
Comments and Suggestions for AuthorsThe authors have successfully addressed all my questions. There is one small correction: in figure 1A, it should be principle coordinates analysis (PCoA) plot not PCA if you are using Bray-Curtis distance. PCA is a special case of PCoA with Euclidean distances.
Author Response
Comment: The authors have successfully addressed all my questions. There is one small correction: in figure 1A, it should be principle coordinates analysis (PCoA) plot not PCA if you are using Bray-Curtis distance. PCA is a special case of PCoA with Euclidean distances.
Response: We thank the reviewer for notifying us of this detail. In the revised version of the manuscript this error has been corrected.
Round 3
Reviewer 1 Report
Comments and Suggestions for AuthorsI would like to thank the authors for taking my suggestions into consideration and agreeing to revise the manuscript to improve its scientific rigor. I am pleased with the way the results are displayed now and the figure descriptions, stating how many technical replicates were performed. Although the statistical analysis cannot be done, I think the results are much clearer now, and other researchers in the field can use it and perhaps conduct their own studies with another population of MPSIII patients.
I completely agree with the difficulty of working with rare diseases, as I work with them as well. My comment about increasing the sample size was merely to justify the conclusions that were being drawn from the study. If the goal were to generalize for the MPSIII population (as it sounded before), then a larger sample would be required. However, as the study is presented now (as a descriptive study for the 2 siblings and not generalizing for the MPSIII patient population), I agree with the way it is being presented.
