Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: ALTERED PROTEOME OF A BURKHOLDERIA PSEUDOMALLEI MUTANT DEFECTIVE IN SHORT-CHAIN DEHYDROGENASE AFFECTS CELL ADHESION, BIOFILM FORMATION AND HEAT STRESS TOLERANCE
Review round: 1
Reviewer: 2

Output:
Basic reporting: In their manuscript “Altered proteome of a Burkholderia pseudomallei 1 mutant defective in short-chain dehydrogenase affects cell adhesion, biofilm formation and heat
stress tolerance”, Onrapak Reamtong and co-authors analzed a former generated B. pseudimallei mutant that lacked SDO and showed decreased virulence. Albeit the proteome analysis was carried out with a rather old technique using 2D-PAGE, the results are sound and 5 proteins were found to be significantly altered. The regulation was also confirmed by quantitative PCR. This is carefully executed study and the claims made by the authors are fully supported by the data. The manuscripts also well written. The display of the data (Figure 2&3) could be improved (see specific comments below), but this is only a minor comment. Therefore, I cannot recommend publication if the minor issues below are addressed.

Minor Comments:
Figure 2: The 5 bar charts could be placed in one chart. When the fold change is reported, the first bar with a ratio of 1 does not need to be reported. Also, please consider to show the individual data points in the graph together with the SD. This is a much better presentation of the quantitative data than the current charts.

Figure 3: Similar to above. Please show all individual data points instead of the bar starting at 0, which makes no sense. If there are more than 10 data points per bar, a box plot should be used.
Experimental design: no comment
Validity of the findings: no comment
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: ALTERNATIVE DIETARY PROTEIN AND WATER TEMPERATURE INFLUENCE THE SKIN AND GUT MICROBIAL COMMUNITIES OF YELLOWTAIL KINGFISH (SERIOLA LALANDI)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The manuscript is well written in a professional language, though I have noticed a few spelling mistakes:

1) Line 101: The authors should specify the control treatment, as stated afterward in line 266 “one control treatment (22 FM) and three experimental treatments (22 SPC, 26 FM and 26 SPC)”. Here is a suggestion: The orthogonal combination of diet type and water temperature resulted in four treatments; hereafter a control treatment (22 FM) and three experimental treatments (22 SPC, 26 FM and 26 SPC).

2)Line 247: spelling mistake “calculated”

3) Line 270: spelling mistake “temperature”

The literature references are appropriate, and the introduction provides sufficient information to understand the aims of the experiment. However, here are of few comments:

1) Line 73: While the authors mention that reports on yellowtail kingfish microbiome are limited to 3 studies, more recent reports have been conducted such as one investigating the impact of diet on the larvae associated microbiota (Wilkes et al 2019, https://doi.org/10.1111/1751-7915.13323). In addition, a report on the selection of native probiotics for yellowtail kingfish was recently published and highlights the potential role of the microbiota in yellowtail kingfish health (Ramirez et al 2019, https://doi.org/10.1007/S12602-019-09550-9).

2) The authors cite 3 review papers to highlight the role of the microbiome in fish health (line 63). However, some of these reviews are mainly focused on structure and diversity rather than on the role of the fish microbiome. In this regard, more appropriate reviews could be cited (e.g. Banarjee and Ray 2017. Bacterial symbiosis in the fish gut and its role in health and metabolism. Symbiosis. https://doi.org/10.1007/s13199-016-0441-8; Legrand et al 2019. A microbial sea of possibilities: current knowledge and prospects for an improved understanding of the fish microbiome. Reviews in Aquaculture. https://doi.org/10.1111/raq.12375).
Experimental design: The aims of the experiment are well defined. The authors examined juvenile yellowtail kingfish microbiota at different body sites (skin, gut mucus and digesta) in response to changes in temperature and diet. They also investigated changes in immune-related health parameters with the aim to correlate them with shifts in the fish microbiota.

Overall, the methods used in this study are robust and well described. Though a relatively large proportion of the samples were not successfully sequenced, the authors had sufficient replicates to perform robust data analysis. The collection of a water sample at the beginning of the experiment would have been valuable to compare the microbial diversity between sample types (Figures 2 and 3). However, it does not impact the conclusions drawn from this work.
Validity of the findings: All important data and information are included in the manuscript. However, a few corrections should be made to improve the quality of the paper:

1) Even though the authors mentioned that only samples with a minimum of 10,000 sequences were kept for downstream analysis (line 231), a rarefaction plot would be useful to show sufficient sequencing depth and should be added in the supplemental files.

2) Significant differences are presented in line 269 and 281 with p-values of 0.12, 0.22 and 0.12 using one-way ANOVA. Since an alpha of 0.05 is commonly used to differentiate significance, authors should provide a table summarising the complete results of the different statistical tests performed (e.g. one-way ANOVA) in order to prove significant differences. If significant differences are not found, authors should change the wording accordingly (e.g. was found to be substantially affected though not significant).

3) The authors generated Spearman correlations using the R package Hmisc (line 247). Significant correlations were then imported in Cytoscape to generate a network. However, to the best of my knowledge, the correlation p-values generated by Hmisc are not corrected and therefore, a multiple testing correction, MTC,  (e.g. Bonferroni) is needed before importing significant correlations in Cytoscape (for an example, see Sylvain et al. 2019, https://doi.org/10.1111/mec.15184 ). Since the MTC is likely to influence the number of significant correlations, this would impact the number of nodes and edges of the network which would have to be reconstructed. If MTC was applied and not mentioned by the authors, this should be stated in the methods section.

4) The authors investigated microbial diversity using different indexes. Among them, Simpson was used to evaluate the microbial community evenness (line 304). However, the Simpson index (symbol D) generated by Phyloseq does not reflect the microbial community evenness but instead provide information about diversity and richness (Simpson, E.H. (1949). “Measurement of diversity". Nature. (163): 688). As a result, another index should be used in order to investigate the microbial community evenness such as the Simpson evenness measure (symbol E) or Pielou’s evenness measure.
Additional comments: Horlick et al investigated the effect of soy-protein concentrate and water temperature on juvenile Yellowtail Kingfish microbiota. They found that both water temperature and diet perturbed the skin and gut bacterial communities, associated with changes in immune parameters in some cases. The data generated in this study provides additional information on the yellowtail kingfish microbiota and highlights the need to consider the combined effect of diet and environmental factors on yellowtail kingfish health. Therefore, I believe that this manuscript deserves to be published if the previously cited revisions are made.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: ALTERNATIVE DIETARY PROTEIN AND WATER TEMPERATURE INFLUENCE THE SKIN AND GUT MICROBIAL COMMUNITIES OF YELLOWTAIL KINGFISH (SERIOLA LALANDI)
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper by Horlick et al. is an important contribution to the skin and gut microbiome of a cultivated fish species with very limited knowledge on this issue. The paper is based on a very well designed experimental set up and the methods used are some of the most appropriate to date. Finally the paper is adequately structured and its presentation is very reader-driendly despite the ample volume of data/information it contains.
Experimental design: The authors have based their analysis on some of the most appropriate methodological tools available to date. Also, the bioinformatics and statistical analysis they used in just about right, without providing any unnecessary analyses.
Validity of the findings: This is a very important contribution for the field of fish microbiomes. The authors explain all the presented results in a very comprehensive way, supported by the relevant literature and scientifically sound speculations.
Additional comments: I was not able to find any "mistakes" that need to be corrected. For this I have several suggestions but only because the data you analysed are so meaningful, and this is your paper I will leave it as it is. What needs to be included, though, is (a) a short justification of how you chose 26oC and not higher/lower than optimal. and (b) how did you end up using a 30% replacement in the diet (and not 50% or 20% or other)?.
A final comment is about Photobacterium and its increased abundance at 26oC, despite it is known to do better at lower temperatures. It is very hard to distinguish whether its increased abundance is due to the increased temperature or the diet substitution. Another issue relted to this genus is its high number of 16S rRNA copies (as it is for several other Proteobacteria) which ranges between 9 and 21 (mean 15±3.8). If one corrects for such high numbers, then its relative abundance drops significantly. Kormas (2011) suggested that when Proteobacteria dominate in a sample, the effect of multiple 16S rRNA gene copy numbers might impact considerably the big picture of bacterial diversity (Kormas KA (2011) Interpreting diversity of Proteobacteria based on 16S rRNA gene copy number. In: Sezenna ML (ed) Proteobacteria: Phylogeny, metabolic diversity and ecological effects. Nova Publishers, Hauppauge, NY, p. 73-89. ISBN: 978-1-61761-810-9).


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: ALTERNATIVE DIETARY PROTEIN AND WATER TEMPERATURE INFLUENCE THE SKIN AND GUT MICROBIAL COMMUNITIES OF YELLOWTAIL KINGFISH (SERIOLA LALANDI)
Review round: 1
Reviewer: 3

Output:
Basic reporting: The article “Alternative dietary protein and water temperature influence the skin and gut microbial communities of yellowtail kingfish (Seriola lalandi)” contributes with new knowledge regarding the microbiome of yellowtail kingfish. It is well written and clear. However, there are some issues that need to be addressed, specially with the performance results and the microbiome`s statistical analyses.
Experimental design: The experimental design is clear. Nevertheless, there are some point to consider/clarify regarding the experimental design:
-	Is there any reason to use only 7 fish per tank? This amount of fish does not represent what may happen in the aquaculture industry at any scale
-	Growth performance is only represented by weight gain. This is insufficient to have a clear view of the performance, some other performance parameter should be included in the analyses (SGR, TGR, others). Also, the weight gain was not stated (grams gained), only a difference in % between group. In order to understand results, the weight gain and other performance parameters should be stated (with variation) in the manuscripts and the tables (not only the %)
-	It is unclear how the FCR was calculated. Did you collect feed waste? If so, Feed intake should be corrected by feed waste. If feed waste was not collected, this should be stated in the manuscript as a limitation in the results/discussion
-	Line 160-161 need clarification of the method of collection of digesta. Could this method affect the results?
-	Microbiota analysis should include tanks as a factor in the statistical analysis. If not, you would need to pool the number of samples per tank., as variation among tanks in each treatment should be taking into account.  Another alternative is to use a linear mixed model approach using tank as random factor and diet and temperature as fixed factors
-	How was the microbiota data filtered regarding contamination during DNA extraction and PCR steps? Was the PCR product of controls sequenced and analyzed?  The results from the controls should be considered in order to remove contamination (you can check this article: Simple statistical identification and removal of contaminant sequences in marker-gene and metagenomics data. doi: 10.1186/s40168-018-0605-2).
Validity of the findings: The findings are interesting, although they should modify the points suggested for the experimental design.
Other comments regarding results and findings:
-	Line 269-270, weight gain should be specified (with variation)
-	Line 269-270 Not significantly affected? Or is there a typo error?
-	Line 314 make sure that the OTUs from Cyanobacteria are not coming from chloroplast. Be sure to remove the reads belonging to OTUs assign to chloroplast
-	358-359 unclear. 22FM is the control treatment
-	Line 446-455 This is a repetition of the results with no discussion
-	Line 524-527 More studies are needed to be able to state this
-	Line 560 increase relative abundance, not total abundance
-	Line 561-565 Only MPO was measured, it could only be an indication of immune compromise. More studies and several other analyses are needed to validate this finding
Additional comments: -	Figures need to have bacterial genera in cursive
-	Figure 5 difficult to see, it needs to be turn around
-	Figure 8 needs to be bigger
-	Line 42-44 need update information, as for now, feed for carnivorous fish such as Atlantic salmon are not dependent on fishmeal


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: ALTERNATIVE DIETARY PROTEIN AND WATER TEMPERATURE INFLUENCE THE SKIN AND GUT MICROBIAL COMMUNITIES OF YELLOWTAIL KINGFISH (SERIOLA LALANDI)
Review round: 1
Reviewer: 4

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The manuscript entitled “Alternative dietary protein and water temperature influence the skin and gut microbial communities of yellowtail kingfishn (Seriola lalandi)” submitted by Horlick et al. reports the effect of fishmeal substitution with 30% soy-protein concentrate (SPC) combined with rearing water temperature on skin and gut microbiome of yellowtail. The present study examines in detail the interactive effects of diet and environmental factors on microbiome health and, partly, on innate immunity of host. In the last years, intestinal microbiome gathered interest of aquaculture scientist since it potentially regulates host health status and thus productivity of aquaculture industries. In fact, in these years and increasing numbers of studies have indicated that the microbiome plays an important role in fish health and diet is considered one of the main factors putting selective pressure on the gastrointestinal microbial composition in vertebrates. Hence this paper deal with a key topic and provides valuable outcomes that should be out in public. In addition, commendable effort that the sequencing data have been deposited on public GenBank Sequence Read Archive (SRA) database. For all these reasons, I recommend this paper for publication, although some relevant changes are necessary to the currently submitted version of the manuscript. Authors should consider the following points carefully and revise the paper.
Major revisions
•	The SPC diet formulation reported in Supplementary Table 6 does not correspond with what reported at line 109-110 “The SPC diet was made by blending the FM mash and SPC in a 70:30 ratio”. Indeed from Suppl. Table 6 the SPC diet contains besides FM also wheat flour. Therefore, the ratio 70:30 has to be referred to (FM + Wheat flour):SPC.

•	At line 269 authors state that “Relative weight gain of fish was found to be significantly
affected”, however in the text they report a p-value > 0.05. Is it a typing error?
Moreover, concerning weight gain data, they report that no interaction was found between two main factors (diet and temperature), but in table 1 they indicate a statistical significance between 26FM vs 22FM and 26SPC vs 22FM. It has no sense when no interaction diet x temperature has been found.

•	Differences between communities (beta diversity) based on Bray Curtis distance should be represented also by PCoA plots in order to better understand and graphically verify the results of PERMANOVA analysis made.

•	Since the water microbiota has been analysed, why was not the same done for feed-associate microbial communities? It is known that undigested feed could influence transient gut microbial community composition

Minor points
Figures 1, 5, 6-9 are difficult to read I suggest increasing the font.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: ALTERNATIVE DIETARY PROTEIN AND WATER TEMPERATURE INFLUENCE THE SKIN AND GUT MICROBIAL COMMUNITIES OF YELLOWTAIL KINGFISH (SERIOLA LALANDI)
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment
Experimental design: No comment
Validity of the findings: No comment
Additional comments: The authors have addressed all suggested revisions which I believe improved the quality of this publication.
The results presented in this manuscript are novel and useful for the fish farming industry and other researchers working on fish microbiome. As a result, I believe that this article should be accepted.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: ALTERNATIVE DIETARY PROTEIN AND WATER TEMPERATURE INFLUENCE THE SKIN AND GUT MICROBIAL COMMUNITIES OF YELLOWTAIL KINGFISH (SERIOLA LALANDI)
Review round: 2
Reviewer: 2

Output:
Basic reporting: The authors have properly revised the manuscript based on all comments.
Experimental design: The authors have properly revised the manuscript based on all comments.
Validity of the findings: The authors have properly revised the manuscript based on all comments.
Additional comments: The authors have properly revised the manuscript based on all comments.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: HEEDING THE PSYCHOLOGICAL CONCERNS OF YOUNG CANCER SURVIVORS: A SINGLE-ARM FEASIBILITY TRIAL OF CBT AND A COGNITIVE BEHAVIORAL CONCEPTUALIZATION OF DISTRESS
Review round: 1
Reviewer: 1

Output:
Basic reporting: This manuscript describes a study in which their primary aims were to examine the feasibility and efficacy of CBT for AYA survivors of cancer and to describe cancer related concerns and maintaining factors for this group. The introduction provides a strong framework for the significance of the study and importance for understanding the treatment needs of the group. The authors did a nice job of explaining their aims and the results and outcomes they examined clearly related to the main purpose. Overall, the writing was clear.
Experimental design: Some strengths of the study design include well-defined aims and questions and the inclusion of a breadth of measure of mental health outcomes and psychological function. However, the article would benefit from providing more detail about their screening procedures and unstructured interviews. Specifically, during the screening assessment (lines 161-170), why did they only screen for depression? Why did they not screen for anxiety or PTSS/PTSD – which are also common in this AYA population? Was that included in the M.I.N.I? Further, more information and detail about the unstructured interviews (described in lines 219-226) would be beneficial. Were there any other standardized questions asked of all participants (besides the one in lines 221-222)?

The authors should also provide support and reasoning for why they did not assess therapist fidelity to CBT. If one of the goals of the paper was to understand efficacy of CBT in this AYA population, it seems that it would be important to show that the treatment participants received was actually CBT.

Most importantly, I think this article would benefit from providing more detail about how the interview data was analyzed (lines 280-288). How did they come up with the themes? Did they use any formal method of analyzing the qualitative interview data (like content analysis) to come up with the four themes? If not, why? Was the interview data only reviewed by members of the research team? Why did they not get input from other sources – oncologists, patients, parents? Asking AYA survivors “what do you think of these themes, do they resonate with you?” would support the validity of the themes. The authors should provide more information as to how they came up with the themes and could provide more support for their approach to this data.
Validity of the findings: The findings of this study provide support for using CBT for AYA cancer survivors, and offer meaningful evidence for providing psychological treatment for this population. However, I am concerned about the strength of the validity of the themes they came up with (see comments above). The manuscript would benefit from the authors providing more of an explanation as to why they think using CBT in this population might be different than the general population. The authors should comment on how CBT can be adapted specifically to incorporate the four cancer-specific concerns and maintaining factors they identified.

The authors did a nice job of presenting their results and conclusion with caution – recognizing that this is a small sample, and may not generalize. They provide support for doing future research in this area.
Additional comments: The article could also be strengthened with more suggestions regarding getting AYA more engaged in psychological treatment, especially considering the low engagement and enrollment. In lines 438-452 the authors explain that AYA don’t often utilize psychological services for a number of reasons. What do the authors then proposed we do to get AYA survivors more willing and engaged in treatment?


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: HEEDING THE PSYCHOLOGICAL CONCERNS OF YOUNG CANCER SURVIVORS: A SINGLE-ARM FEASIBILITY TRIAL OF CBT AND A COGNITIVE BEHAVIORAL CONCEPTUALIZATION OF DISTRESS
Review round: 1
Reviewer: 2

Output:
Basic reporting: 1. Overall the paper is well-written and easy to follow. There are one or two spots which would benefit from further editing for clarity, e.g., Results section “previous reception of psychological support” sounds a little awkward
Experimental design: 1. The single-arm design of the study is fine given the small numbers, but there is a lack of detail or information provided regarding the sample size that would/should have been expected for this population (from a local context, and also from previous literature where psychological interventions have been offered to survivors). Similarly, there are no hypotheses presented, and although the authors outline that the aim of the study is to establish feasibility, no a priori thresholds for what would constitute reasonable or acceptable levels of feasibility have been presented. This makes it difficult to establish (a) if the findings are consistent with what might have been expected, and/or (b) if what was found justifies the use of this intervention – i.e., is it in fact reasonably feasible? Later in the Discussion the authors state that they were not able to reach data saturation, but again it is not clear what sample they would have needed in order to do so.
2. I also felt that the construct of ‘feasibility’ was defined and examined in fairly narrow terms. There are a number of other aspects of the intervention that could have been examined, either from the AYA participant, or psychologist perspectives, or even ‘system’ perspectives (e.g., cost?). Other elements related to the ‘safety’ of undertaking this type of psychological intervention, with this group, could also have been explored. Clearly these pieces of information are not likely to be available after the fact, but I think some acknowledgement may need to be made in the Limitations section that these aspects were not evaluated. As an example of other ways of establishing/exploring feasibility, please see:
-	Sansom-Daly UM, Wakefield CE, McGill BC, Patterson P. (2015). Ethical and clinical challenges in delivering group-based cognitive-behavioural therapy to adolescents and young adults with cancer using videoconferencing technology. Australian Psychologist, Special Issue: Tele-Psychology: Research and Practice, 50(4), 271-278. DOI:10.1111/ap.12112
-	Sansom-Daly, U.M., Wakefield, C.E., Bryant, R.A., Patterson, P., Anazodo, A., Butow, P., Sawyer S., McGill, B.C., Evans, H., Cohn, R.J., and The Recapture Life Working Party. (2018). Feasibility, acceptability, and safety of the Recapture Life videoconferencing intervention for adolescent and young adult cancer survivors. Psycho-Oncology, 09 Nov 2018
-	Campo RA, Bluth K, Santacroce SJ, et al: A mindful self-compassion videoconference intervention for nationally recruited posttreatment young adult cancer survivors: feasibility, acceptability, and psychosocial outcomes. Support Care Cancer 25:1759-1768, 2017
Validity of the findings: 1. 	In the introduction, the authors highlight two models but then state that these models do not adequately pinpoint mechanisms that may drive/underpin distress. (“…neither model recognizes the full range of cancer-related distress” – what does this mean? In terms of severity? Or types?) I felt that the authors missed an opportunity here to describe in more detail, or unpack, what mechanisms they propose may be driving post-cancer distress, and indeed that they hypothesized they would target via CBT tailored to this group? I realize that some of this information is contained in the CBT conceptualization that is later presented, but in order to have done the study and offered the CBT intervention to these 10 patients I would expect that the authors and therapists would have already had a reasonable idea, at the outset, of what they may be targeting so as to be able to provide a solid therapeutic rationale. There are also other recent papers that have hypothesized about different mechanisms and psychological processes that may contribute to maintaining distress in this population, that may be worth examining to add more nuance to this aspect of your rationale/discussion: See,
-	Sansom-Daly, U.M., Wakefield, C.E. (2013). Distress and adjustment among adolescents and young adults with cancer: An empirical and conceptual review. Translational Pediatrics, 2(4):167-197.
-	Sansom-Daly, U.M., Wakefield, C.E., Robertson, E.G., McGill, B.C., Wilson, H.L., Bryant, R.A. (2018). Adolescent and young adult cancer survivors' memory and future thinking processes place them at risk for poor mental health. Psycho-Oncology 27(12):2709-2716 -  this paper could add to your discussion of identity issues and the way in which not being able to imagine the future impedes goal-setting etc
2.	I recognize that this field is constantly evolving, however I think the authors could better situate their intervention in the context of some of the most recent literature, which I believe may be lacking from the present manuscript. For example, recent work has been done by Sansom-Daly and colleagues in Sydney, which also evaluates a CBT focused intervention for AYA cancer survivors. As such, there are a few points in the intro/discussion that may need to be tempered a little to acknowledge that although the present study is novel, it in fact builds on/adds to other work that is also looking at how the CBT model applies to this sort of post-cancer distress, in this group.  (e.g., intro: “so far no CBT-based psychological intervention has been developed and tailored for this population” – this is not true).
3.	It is a bit unclear how the CBT therapy was ‘sold’ to the participants – how was it presented, what was the rationale presented in terms of what it was targeting/focusing on? As n=61 said they had ‘no need for support’ it would be good to better understand what this actually means. And is it correct that participants did not need to be clinically distressed in order to participate? If this is the case, (and I think this could be made clearer throughout) then it would be helpful for the authors to unpack a little more what it was the survivors thought they were getting/being offered, and for what reason. E.g., were they told it was a coping skills intervention to help them build resilience?
4.	Relatedly, if it is true that participants did not need to be clinically-distressed in order to participate, then I’m not completely convinced as to whether the authors’ argument regarding distress and the low rates of opt-ins holds? I think this element of the Discussion may need to be tempered a little bit and with further information regarding what participants were actually told/advertised to inform it.
5.	Case formulations are typically tailored to the individual in clinical psychological practice. Consequently, while it is interesting to see the aggregated ‘mechanisms’ that are presented in this paper, it is not clear how clinicians should or could use the aggregate version of all the maintaining factors to inform their practice? It might be informative to add a de-identified worked example of one individual’s case formulation to show how these mechanisms functioned at the individual level to maintain their distress and any other related issues.
6.	Relatedly, I think what would add value to this article, particularly for clinician readers, is having a sub-section within your CBT conceptualization section, where after discussion of each ‘mechanism’ you briefly describe what CBT strategies can be used, how they can be tailored, etc to target each mechanism. Presumably this would also involve reflecting on what was used within your own intervention. I think the authors need to be conscious of the fact that within the broader psycho-oncology literature it is not simply agiven or automatically accepted that CBT is the most appropriate therapeutic approach for cancer-related distress (eg., see work by Nick Hulbert-Williams from the UK). I do believe that CBT can play a useful role, and I think the authors have the potential to make a really strong case here with their conceptualization, but I think a little more work is needed to make a strong case as to why the CBT strategies, tailored to the cancer-related mechanisms identified, were highly appropriate and effective.  (It would also be useful to know, for the purposes of this paper, to what extent the decision to use various CBT strategies (as in Table 1) was a collaborative decision between AYA-psychologist, versus being solely driven by the therapist. This could speak to the appeal or acceptability of different strategies from AYA perspectives).
7.	I also felt that the section where the authors suggest that recruitment may be remedied through the assistance of social media, was not entirely convincing. I think certainly some citations are needed here; while I believe there is some research to suggest this, I think it also depends on the type of study being recruited for, and other reviews have shown that rather in-person recruitment e.g., from a nurse yields the highest success rates in terms of opt-ins. As the authors note, this is an issue that does seem to plague AYA research, particularly intervention studies. The present study seemed to use a single-site design, but there are considerations also to think about regarding where resources are placed in terms of time investment in recruitment – eg., see this recent commentary,
-	Sansom-Daly, U.M., Evans, H.E., Ellis, S.J., McGill, B.C., Hetherington, K., Wakefield, C.E. (2017). Something’s got to give: Time-cost trade-offs in site-specific research approval can negatively impact patient recruitment in multi-institutional studies. Internal Medicine Journal, 47(9), 1088-1089.
8.	A lot of measures were used, yet there do not seem to be any indices of acceptability or benefit/burden from the perspective of the participants. Can the authors comment on this? Possibly in the limitations?
9.	Do the authors have information regarding whether there were any systematic differences between the registry AYAs who opted in vs. out?
Additional comments: I think all my comments have been captured in the above. All the best with the revisions.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: THE EFFECT OF PERSONALITY MEASUREMENT CONDITIONS ON SPONTANEOUS SWIMMING BEHAVIOR IN THE PALE CHUB ZACCO PLATYPUS (CYPRINIDAE)
Review round: 1
Reviewer: 1

Output:
Basic reporting: The study itself seems robust, although some essential details are missing from the methods that need to be included to make this judgement. There is much room for improvement in the analysis (including further data that was collected but not analysed), interpretation of results and presentation. I think the importance of the findings may be obscured by the current presentation.

There are a number of improvements to be made in the presentation of the text, including grammar and choice of words/terminology. I have made various comments below but these are by no means exhaustive. Figure legends are multiple short paragraphs and different fonts.

L 83, “the local fisherymen” should be “local fishermen”. L 85, “Two-tenths” should be “One-fifth” or “20%”. What does “properly” refer to in “properly placed”? Delete “i.e.” in “i.e., the pale chub”. Generally, “i.e.” is overused throughout.

The abstract is rather long and detailed, and should be made clearer and easier to read, and possibly made shorter.

The Introduction is too short and mostly one very large paragraph. The Introduction should be longer and broken up into multiple paragraphs to aid readability.

The Discussion should include a paragraph on why the measured variables are important, i.e. what consequences do they have for fitness? For example, encountering food:
Search rate, attack probability, and the relationship between prey density and prey encounter rate
CC Ioannou, GD Ruxton, J Krause, Behavioral Ecology 19 (4), 842-846
Experimental design: This was generally good but some details are missing to make a full assessment.
Validity of the findings: See specific comments.
Additional comments: L 20: What is meant by “spontaneous” in “spontaneous movement traits” and elsewhere? It is used frequently without its meaning being clear.

L 28-30: This is unclearly written.

L 36: It is surprising to see the repeatability of the behaviours being presented at the end of the abstract, like an afterthought, when the title focuses on personality.

L 37: Rather than “the personality of pale chubs is quite conservative”, is “the personality of pale chubs is conserved” meant?

L 42: Cite reviews / meta analyses here for this general point, such as
Bell AM, Hankison SJ, Laskowski KL. 2009 The repeatability of behaviour: a meta-analysis. Anim. Behav. 77, 771–783.
rather than primary literature using fish; there is no reason the literature cited should be so fish orientated.

L 50: “inspection” is referred to here, but inspection of what? I think the general consensus is exploration is movement in an unfamiliar area, but behaviour toward a novel object measures neophobia. The literature should be checked, and the choice of terminology justified in the manuscript with the supporting references (ideally highly cited reviews on the subject).

L 56: Is this not referred to as a behavioural syndrome? This term is not in the manuscript except the references, which is surprising.

L 64: It is not clear what “or relevant” means here.

L 68-69: How are these different in practice?

L 122: Measures such as the time taken to first leave the refuge, or to reach a certain point in the arena, are used in such assays of boldness, rather than the behaviour of the animal when outside the refuge. See, for example:
Bevan PA, Gosetto I, Jenkins ER, Barnes I, Ioannou CC. 2018 Regulation between personality traits: individual social tendencies modulate whether boldness and leadership are correlated. Proc. R. Soc. B Biol. Sci. 285. (doi:10.1098/rspb.2018.0829)
This should be measured and its relationship with the trajectory data tested for.

L 133: It is essential to include here what the time interval was between fish being tested. Also, I don’t think it is stated whether tests were done in a randomised order for each fish? Does testing order have any effect?

L 129: It’s not clear how relevant “distance to the center of the open area” is when it becomes apparent that the test tank is long and thin; even in the centre of the arena, the fish will still be close to a wall. This variable would be more appropriate in a circular or square arena, where the centre is far from the nearest wall.

L 136: There’s a reference here for the choice of this threshold, but it needs more justification.

L 143: There needs to be more justification for the choice of term “head-turning rate”. Presumably the tracking software tracks the centre of mass of the fish, so this variable is absolute turn angle of the trajectory. Due to the morphology of fish where the body is not rigid, this is not necessarily the same as the head-turning rate.

L 147: “almost identical” is a poor choice of words in “were almost identical between the activity and exploration contexts”. Almost identical in what sense? Same mean and variance? Or strongly correlated? Or something else? This also sounds like it should be in the results, and it doesn’t need to be here.

L 160: How have the assumptions of the tests been tested for, and are the assumptions met? This is essential to include.

L 166: The repeatability of the response to the novel/fake object isn’t tested for? Also, the method of testing for repeatability seems rather outdated and there are more sophisticated and powerful tests that allow for control over covariates such as body size.

L 172 onward: Why is repeatability presented first, then average differences, then repeatability again?

L 176: Rather than ‘control condition’, it would be better to refer to ‘activity context’ (or similar) to match the figures better. Consistency helps the reader.

L 185: Why isn’t repeatability for these variables explored too?

L 187: This seems to directly contradict the statement in the abstract that “pale chubs might ignore the existence of a so-called ‘novel’ object.”.

L 193: “might not have cared” is anthropomorphic.

L 195: Doesn’t this contradict the result in Fig 4c?

L 196: It is written as if the results presented are different to those found elsewhere, but it’s not made clear this is the case.

L 210: This statement needs more justification.

L 217: Since this data was collected, it should be analysed (see comment above). It would be of interest to see how it correlates with data from the fish’s trajectories when outside the refuge.

L 228: Again, “All variables in the present study were quite similar across the different contexts.” is too vague.

L 232: I think this should be deleted, as unpublished data is being referred to that has not been peer reviewed.

L 237-239: This needs more explaining, it seems contradictory.

Figure 3: It looks like a lot of data points are obscured by the opaque filled circles.

Christos Ioannou
University of Bristol


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: THE EFFECT OF PERSONALITY MEASUREMENT CONDITIONS ON SPONTANEOUS SWIMMING BEHAVIOR IN THE PALE CHUB ZACCO PLATYPUS (CYPRINIDAE)
Review round: 1
Reviewer: 2

Output:
Basic reporting: Overall, I commend the author on the quality and accuracy of the English writing. That being said, there are a few lines that require editing, below are a few examples:

-line 60- ‘trauts’ should be 'traits'
-lines 69-70- add ‘be able to’ to “researchers may ______ acquire data…”
                       add ‘if correlated’ to “For example, ________, one can measure”

Also, there is some inconsistency in the format of in-text citations. Some have a comma after the authors names, some do not...

The figures all look fine, and I appreciate the diagram of the experimental arena.
Experimental design: The Methods section is the section that I believe needs to be greatly improved to be published in PeerJ.

-First, the authors need to describe the order in which the fish experienced the three tests (activity level, exploration, and boldness). Did all fish experience the tests in the same order? Also, if boldness was not the first test, I suspect that the fish may have had too much experience in the experimental arena for it to be considered a true boldness test of leaving a refuge (considering that the fish may already have information that they would be safe outside of the refuge). Please refer to Balaban-Feld et al. (2019) Influence of predation risk on individual spatial positioning and willingness to leave a safe refuge in a social benthic fish. Behav Ecol Sociobiol 72: 87.

- For the boldness test, did the authors only measure time spent in refuge versus time spent in open area. Did the authors not measure latency to leave the refuge? This would seem to be the most important indicator of boldness.

-Where exactly were the fish placed into the tank for the exploration test and the general activity test. Along the side of the tank? This needs to be explained in detail.

-Please provide a more detailed explanation of how repeatability was calculated.

-Finally, I believe the hypothesis and purpose of the study should be more clearly defined. For me, I only really understood the major finding of the study in the second to last paragraph of the discussion (lines 228-236)
Validity of the findings: I think that the study does have merit, in that it demonstrates how researchers may be able to skip overall activity testing and simply run exploration or boldness tests to find personality differences. I believe this result should be the result that is most clearly explained as it is the most important (lines 234-236).

I also believe the abstract should be heavily edited, it was very hard to follow and I think it could explain the experiment design more clearly, and spend less time focusing on the novel object result.

Furthermore, I am not sure I understand or agree with the author’s assertion that the fish did not care about the presence of a novel object. Although the authors found similar movement metrics between the exploration and general activity tests, they found that fish in the exploration experiment reached the novel object quicker than fish reached the ‘invisible object’…line 204-205 states “the fish purposefully encountered the object earlier for exploration”. Does this not clearly show that the fish did care about the presence of a novel object. So, if this is true, it may be possible for researchers to find important information about differences in exploratory behavior among fish individuals (even if swimming speeds and other metrics don’t change between contexts).
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: THE EFFECT OF PERSONALITY MEASUREMENT CONDITIONS ON SPONTANEOUS SWIMMING BEHAVIOR IN THE PALE CHUB ZACCO PLATYPUS (CYPRINIDAE)
Review round: 2
Reviewer: 1

Output:
Basic reporting: Points detailed below in General comments, otherwise OK.
Experimental design: Points detailed below in General comments, otherwise OK.
Validity of the findings: Points detailed below in General comments, otherwise OK.
Additional comments: The manuscript is much improved and it is much clearer what the aim of the study is.

As I stated in my first review, the distance to the centre does not seem appropriate because the test arena is narrow (20cm, which is around 3 body lengths (L172)) – the centre of the arena is still very close to the nearest tank wall. As there weren’t any significant trends with this variable, it should be removed from the paper entirely. It just adds unnecessary text (e.g. L 230) so the story is less clear, and due to the tank size is probably not biologically of value anyway; there is nothing lost by removing it.

The abstract needs to start with a general sentence that sets the background and context for the present study which then justifies the next sentence starting “The aim of the present study”. Similarly, there should be a concluding sentence at the end that puts the study’s results back into this broader context.

L 31-33: Here it needs to be stated what direction the trend is in rather than just that the behaviour “significantly differed between the two contexts”. It also needs to be clearer why the results for this mean that this might be “a potential variable … in the future”; currently this is not clear.

L 38: Cite either just across-taxa reviews or a papers on non-fish too. This is a general biology journal, not a fish-specific one.

L 43: Cite an early paper to use the tendency to leave a refuge as a measure of boldness, not a recent one.

L 51: “behavioral syndrome” not “behavior syndrome”.

L 73: The results can’t be stated in the Introduction. Instead the paragraph could start with “To test further whether the novel object is a sufficient stimulus…”.

L 79-80: This is unclear.

L 102: “an opaque canvas to stimulus from the observers during the experiments” is unclear.

L 123: “the linking threat manipulated remotely” is unclear.

L 135: What evidence is there that 10 minutes is enough “to eliminate the effect of the exploration context”? How could this even be tested?

L 149: This line can be deleted as the information is already given earlier.

L 151: It is still not clear why a threshold “above 1.75 cm s-1” is used – both the references are from the author’s research group. There needs to be a proper justification in this paper rather than the reader having to search the cited papers for the details (presuming the justification is actually given in these papers, rather than being arbitrarily chosen).

L 153: Cite Ioannou et al. 2015 after “as opposed to goal-directed behavior in fish”.

L 187: It needs to be stated why it is just the median swimming speed for these pairwise comparisons.

L 188: It is nonparametric, not nonparameter.

L 240-248: This section needs rewriting. Firstly, it needs to be clear that the faster speeds and more time spent moving in the boldness test could be because the fish can rely on returning to the shelter when threatened, while when not available, they reduce activity (speed and time spent moving) because a refuge is not available (assuming this is the point being made). References need to be included here, such as
Herbert-Read, J. E., Kremer, L., Bruintjes, R., Radford, A. N., & Ioannou, C. C. (2017). Anthropogenic noise pollution from pile-driving disrupts the structure and dynamics of fish shoals. Proceedings of the Royal Society B: Biological Sciences, 284(1863), 20171627. https://doi.org/10.1098/rspb.2017.1627.
which show that activity is reduced when perceived threat increases.

The next point that “it might have little biological significance given the large difference among individuals.” needs fuller explanation. In terms of ecological impact, e.g. the effect the fish have on their prey, it may be true that inter-individual variation may be more important than whether the fish have a shelter or not. Again, references need to be included, i.e. those that look at the ecological consequences of personality variation, such as
Ecological consequences of the bold–shy continuum: the effect of predator boldness on prey risk
CC Ioannou, M Payne, J Krause Oecologia 157 (1), 177

Finally, it is surprising to see the point that “variables that have been frequently used in previous studies, such as the percentage of time spent outside of a shelter, might be reliable indicators of boldness in fish species” when these variables have not been included in the current study but could easily be measured from the videos and included in the analysis. Either the current study is only focused on movement behaviour outside a shelter (if present) or it is broader than that. This last part (L 245-247) should either be deleted or such analyses included in the paper and the broadness of the paper expanded.

L 266-273: Again, I found this section unclear. I would expect the
Herbert-Read JE, Krause S, Morrell LJ, Schaerf TM, Krause J, Ward AJW. 2013. The role of individuality in collective group movement. Proceeding Royal Society B 280: 20122564
paper to be cited here.

L 276: Unclear. Also it is surprising not to see mention of neophilia in this section of the Discussion. Or that the fish perceived the ‘novel’ object as something that was potentially rewarding, such as food. These are biologically plausible explanations for the result that the fish approach the novel object sooner than expected if it wasn’t present (a very strong effect, based on Fig. 5b) but these aren’t considered at present.

There are a number of inconsistencies in the references list e.g. spacing and punctuation in the volume and page numbers. Bevan et al. is listed here with no page numbers, and not cited in the main text (it can be cited on L 44), and is not on its own line in the reference list.

Figure 1: The height and width dimensions are not consistent with the Methods.

Christos Ioannou
University of Bristol


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: MICONIA LUCENAE (MELASTOMATACEAE), A NEW SPECIES FROM MONTANE ATLANTIC FOREST IN ESPÍRITO SANTO, BRAZIL
Review round: 1
Reviewer: 1

Output:
Basic reporting: The authors consistently present the description of a new species of Miconia, including comparison with closely related species and their position in phylogeny. The taxon is richly illustrated and is presented in real and potential geographical distribution.
Experimental design: nothing to add
Validity of the findings: The authors have long experience in the systematics of this plant group based on fieldwork and phylogenetic analysis.
In addition, the closely related species were satisfactorily compared, and the observed variations: morphological and geographical were tabulated.
Although these have recently published taxonomic changes, species are named by old names.
Despite their justification in Materials & Methods that "old names is more easily understandable", nomenclatural updates should be included in the paper. Included in the table with the Genbank access number.
I missed an analysis of the state of conservation of this new species. Although few individuals have been collected so far, there is no analysis of the degree of threat suffered. Even more so, it honors a researcher recognized for his work in conservation policy in the state of Espírito Santo.
The sequences of atpF-atpH and trnS-trnG of the new species are not available on genbank.
But they were sent as a complementary txt file.
>Miconia_lucenae_T813_atpF-atpH_MN557427
>Miconia_lucenae_T813_trnS-trnG_MN557428
Other comments and suggestions are presented in the text.
Additional comments: My biggest suggestions are for the inclusion of the new taxonomic combinations next to the old names, and the presentation of the state of conservation.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: MICONIA LUCENAE (MELASTOMATACEAE), A NEW SPECIES FROM MONTANE ATLANTIC FOREST IN ESPÍRITO SANTO, BRAZIL
Review round: 1
Reviewer: 2

Output:
Basic reporting: The paper titled ''Miconia lucenae (Melastomataceae), a new species from montane Atlantic Forest in Espírito Santo, Brazil'', is well written. However there are typos e.g. see page 2 lines 28. I have made several comments in the document regarding this.
The literature cited is appropriate and update. However, the authors need to check the in text citation style in the guideline again. In several places the authors use et al. and  & al.  (e.g. compare lines 37-40 and 65) . All these have been highlighted in the text.
The figures, tables and supplementary data are well done. However the titles of the table 1 and figures 1 & 3 need to checked again.
Overall the paper is well written with just some minor things to check especially in text citation.
Experimental design: The methods and analyses provided are sound.
Validity of the findings: The authors have provided enough evidence to support the description of this new species Miconia lucenae.
Additional comments: No additional comments


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: IRON HOMEOSTASIS IN A MOUSE MODEL OF THALASSEMIA INTERMEDIA IS ALTERED BETWEEN ADOLESCENCE AND ADULTHOOD
Review round: 1
Reviewer: 1

Output:
Basic reporting: This work investigates age-dependent differences in iron metabolism in the Th3/+ mouse model of thalassemia. The authors report changes in serum and tissue iron parameters, as well as in expression of iron genes between young and adult mice. The findings are interesting and adequately discussed.
Experimental design: My major concern is that it is not clear which of the reported changes are specific to thalassemia and which (if any) are related to age-dependent variations that also occur in wild type animals. Thus, it will be important to present hematological data and serum/tissue iron data in wild type mice. I would also suggest to report the qPCR data of wild type and Th3/+ mice side by side, instead of normalizing the Th3/+ data relative to wild type. The way the data are presented does not allow comparison of expression levels in wild type mice of different age groups. Hepcidin mRNA data could be normalized to liver iron for clarity. Finally, the data would be strengthened by showing serum hepcidin levels, as well as expression of proteins encoded by the shown mRNAs (at least for the ones where antibodies are commercially available).
Validity of the findings: The findings are generally appropriately discussed. However, the discussion should be modified if age-dependent differences in wild type mice are identified. In the Discussion (lanes 338-341) the authors argue that the age-dependent differences in ferroportin mRNA are linked to hepcidin. This is completely wrong! Hepcidin controls ferroportin protein, not mRNA expression.
Additional comments: There are several statements in the Introduction which are inaccurate. For instance:
a) lanes 76-78: If there is indeed any evidence that DMT1 mediates NTBI uptake in hemochromatosis or thalassemia, references should be provided. To the best of my knowledge, experiments with liver-specific Dmt1-/- mice have excluded any role of this transporter in iron overload (PMID 23508576).
b) lanes 86-87: The rate-limiting step for heme biosynthesis in non-erythroid cells is the generation of aminolevulinic acid, catalyzed by ALAS1. By contrast, the rate-limiting step for heme biosynthesis in erythroid cells is iron uptake (PMID 10522552).
c) lanes 90-91: “IRP” stands for “iron regulatory protein”
d) lane 92: ALAS2 is not an iron transporter


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: IRON HOMEOSTASIS IN A MOUSE MODEL OF THALASSEMIA INTERMEDIA IS ALTERED BETWEEN ADOLESCENCE AND ADULTHOOD
Review round: 1
Reviewer: 2

Output:
Basic reporting: I. BASIC REPORTING:
Clear, unambiguous, professional English language used throughout:
No

1. Specific comments
The standard of English language used is generally satisfactory in most parts of the manuscript, but there are parts where language editing is required for grammatical correctness and better clarity.

Intro & background to show context
2. Specific comments on the introduction:
A lot of the introduction section is a very generalised review of iron homeostasis, which is unnecessarily long. A more concise account would suffice.

3. Specific comments on the background to show context
The rationale and context that prompted the work done is not clear. This should be clearly explained.

Literature well referenced & relevant.
No.

4. Specific comments
Page 7, lines 49 -56:
The first paragraph of this section gives an overview of thalassemia, stating facts that are available in any standard textbook on the subject. The authors have provided, as a reference for these statements, an article published in 2013 in a journal that is not of high quality. More appropriate and better quality references should be provided in support of these statements.

5. Page 7, lines 57 -58:
“Iron, one of essential trace elements, is involved in several biological processes such as oxidative phosphorylation and hemoglobin synthesis (Hentze et al., 2004).”
The fact, stated in the above sentence, is almost common knowledge for anybody in the field of biology. This statement, therefore, needs to be supported by a more appropriate reference than a review article published in 2004, as done by the authors.

6. Page 7, lines 66-78: These sentences outline basic facts about iron absorption. No references have been provided for any of the statements made. Appropriate references need to be provided for the whole of this paragraph.

7. Page 8, lines 90-96: References need to be provided for these statements.
Experimental design: Research question well defined, relevant & meaningful. It is stated how the research fills an identified knowledge gap.
No.

8. Specific comments
The rationale and context that prompted the work done is not clear. What was the research question the authors hoped to address? What is the relevance of such information, in the context of thalassemia?

9. Age-related changes in events involved in iron homeostasis and in thalassemic mice have been reported before (De Franceschi et al., 2006; Chen et al, 2009; Gardenghi et al, 2007). These studies have been cited by the authors of this manuscript. What is different about what the authors of the present manuscript have studied or found from their work? The authors should clearly state what lacunae their work addressed and why it was important to address these.

Rigorous investigation performed to a high technical standard.
10. No. The authors have carried out only gene expression studies done, when protein expression studies would have been more relevant and appropriate.

Methods described with sufficient detail & information to replicate.
No.

11. Specific comments
Methods:
The authors should provide references to support their rationale to use mice aged
6-7 weeks old, 8-12 weeks old, and 16-20 weeks in their study. Mice in the first 2 groups can actually be very close in age. For example, a 7-week old mice would be expected to be very similar to an 8-week old mouse, but they fall into 2 different groups as per the methodology used by the authors. Perhaps a wider difference in the ages may have been a better strategy to use. The authors should substantiate their rationale for choosing these ages to study, and the importance and relevance of parameters of interest in adolescent, young adult and adult mice.

12. What was the source and iron content of the chow used to feed the mice?

13. Were age and gender-matched WT mice also studied for purposes of comparison? There is no mention of such mice in the methodology section. Such comparisons would be necessary in the context of this study.

14. How many mice were used in each of the age groups studied and for each parameter? There is no information provided about this.

15. Why was ANOVA chosen for analysis? The numbers are small and the data could hardly be normally distributed. Non-parametric tests are more appropriate in such situations.
Validity of the findings: 16. Table 2: How do the authors explain their observation the liver iron content was lower in the older mice than the youngest ones, with levels at 8 to 12 weeks being lowest?

17. The legend for the table should state n=? and what statistical tests were used for the analyses.

18. Data for all the parameters studied should have been shown for age-matched WT mice, to make meaningful comparisons.

19. Page 11, lines 187-189: It is stated “Hematological parameters of BKO mice demonstrated thalassemia phenotype including low hemoglobin, hematocrit, MCV and RBC count along with high RDW (Table 2).”
What is the comparison group the authors have used to state that the parameters, listed in the above sentence, above were low? Comparison with age and gender-matched WT mice would be necessary to make such a statement. Such data has not been shown. The authors should show these data.

20. Page 11, lines 189-190: It is stated “No significant difference in RBC count, hemoglobin and hematocrit was found.” Please state clearly which groups are being compared when making this statement.

21. Table 3: Please explain how it is that the scores shown in this table are just these single numbers.
The reference, quoted for the methodology used to get the scores shown in Table 3, gives scores based on percentage of hepatocytes that contained iron. How many fields were studied for each section? How were these fields chosen? What numbers of hepatocytes were counted in each field? What was the mean score obtained? What was the SD? How many mice were used for these studies?
The authors should provide all this information.

22. Page 11, lines 198-199: It is stated “….Additionally, a slightly positive iron staining was observed in brush border of duodenal enterocytes…..”
What does “a slightly positive iron staining” mean? This is an ambiguous statement. Please clarify.

23. Page 11, lines 200-201: It is stated “..An increase in iron deposition score was found in the spleen of the 16-to-20-week old BKO group …...”.
To what group is the data being compared to make this statement?

24. Page 12, lines 206-207: It is stated “Microscopic examination of liver and spleen tissue samples revealed the presence of extramedullary hematopoiesis in BKO mice (Fig. 2)….”.
Please describe what features in these sections indicate “the presence of extramedullary hematopoiesis”. This figure also shows H and E sections of the duodenum. Do the authors mean to say that extramedullary hematopoiesis is seen in the duodenum also?

25. Legends for figures 3 and 4 state that n= 5 for each group. With such small numbers, use of ANOVA is not appropriate. Non-parametric tests should have been employed for analyses. The authors should re-analyse their data to see what their results really show.

26. Why did the authors not study erythroid regulators of hepcidin in the bone marrow, in addition to the extra-medullary sites, in their experimental mice? Erythroid factors produced during ineffective erythropoiesis in the bone marrow may have profoundly affected hepcidin expression in the thalassemia mouse model they studied. How have they ruled this out?

27. Fig 4: The authors show increased hepcidin expression in the liver in the 16-20 weeks-old BKO mice. However, there is no increase in BMP6 expression in the liver, or significant decreases seen in the erythroid factors in the liver, which are the expected biological changes associated with increased hepcidin expression. How do the authors explain their findings?

28. There is some decrease in expression of these erythroid factors in the spleen. If the authors mean to link these changes to the hepcidin expression in the liver, they needed to have measured blood levels of these regulators and also their expression levels in the bone marrow. Such data are necessary to suggest such an association.

29. What were the serum concentrations of hepcidin in these mice?

30. How do the authors interpret their findings in Fig 4?

31. Figure 5: There are 2 bar charts each in Fig 5A and 5B. One cannot give 2 figures the same number. These need to be re-named appropriately for greater clarity. The text that describes these results also lack clarity.

32. Page 13, lines 237-238:
It is stated “Liver ferroportin mRNA levels of BKO mice were 2-3 times higher than age-matched WT mice (Fig. 5A).”
If one looks at the data shown for ferroportin in the figure, the above sentence is not quite an accurate statement of the results shown. The authors have made an overall generalized statement. This is the results section, not a summary of their results. In view of this, it is important that they state their results more accurately.

33. Page 13, lines 238-239:
The authors go on to state “It is noteworthy that ferroportin mRNA expression was marginally induced with increasing age although the difference was not statistically significant.”
Once again, this is not a factually correct statement of the data shown for ferroportin in the figure. Why do the authors think this is “noteworthy”?

34. Page 13, lines 243-245:
“Furthermore, splenic ferroportin mRNA levels in BKO mice were significantly increased in the 16-to-20-week old group than the younger age groups.”
How do the authors interpret this observation, in the view of the increased hepcidin expression they report in the liver? In this context, it would be relevant to know what the serum levels of hepcidin are in these mice.

35. Page 13, lines 247-248:
“…….shown in Fig. 6, duodenal DMT1 and ferroportin mRNA expression was significantly suppressed in 16-to-20-week old BKO mice compared to the other BKO groups”
How do the authors interpret these observations?

36. The effect of hepcidin on ferroportin  has been shown to be at the post-translational level (Drakesmith et al, Cell Metab 2015 [review]) and DMT1 (Brasse-Lagnel C et al, Gastroenterology. 2011; Yamaji et al, Blood 2004). Studying protein expression of these proteins would have been the more meaningful analyses to have carried out in the context of this study. Simply making observations of mRNA expression, without accompanying data on protein expression or functionality, is not meaningful.
Additional comments: DISCUSSION
Overall, the discussion section of this manuscript is not well-written.

27. Page 13, lines 253-256:
It is stated “Several factors including age, gender and strain have been shown to influence iron parameters as well as the expression of hepcidin and other iron regulatory genes (Courselaud et al., 2004; Krijt et al., 2004; Weizer-Stern et al.2006; McLachlan et al., 2017).”
All the above references show the effect of gender and strain on hepcidin and iron-related parameters. They have not studied the effect of age on these parameters. Hence, it is factually incorrect to cite the above references in the context of studying the effect of “age”.

28. The present study appears to be similar in many ways to part of the work done by Gardenghi et al (Blood 2007), where they studied mice (similar to those in the present study) across a much wider range of ages. What new information does the present study provide across a very narrow range of ages and why did the authors think this was important to study? This is unclear.

29. Page 13, lines 261 to 263:
“….Moreover, iron status and iron homeostasis might be altered in adolescents as a result of increased body iron requirement for growth and development.”
Please provide references in support of the above statement.

30. Page 14, lines 263 to 264:
 “However, it has not been clearly elucidated whether iron homeostasis during adolescence differ from adulthood particularly under thalassemic condition….”
The above statement is not factually correct. Gardenghi et al (Blood 2007) have studied the same model as in the present study, where they studied such mice at 2, 5, and 12 months of age. The first 2 time periods they studied (more than 12 years ago) have similarities to the time periods in the present study (6-7 weeks, 8 to 12 and 16 to 20 weeks). Hence, the above statement is not justified.

31. The reference (Laviola et al., 2003) cited by the authors in support of the ages of mice they have used states:
“…….In rodents, the term ‘adolescence’ covers the whole postnatal period ranging from weaning (PND 21) to adulthood (PND 60), that is to be considered no longer infancy, but not yet adulthood. This is indeed a period of behavioral transition, which has been adopted by several authors as a suitable animal model in order to study the psychobiological characteristics of human adolescence……an adolescent rodent has been classified by the use of three age-intervals, namely early adolescence (prepubescent or juvenile, PND 21-to34), middle adolescence (periadolescent, PND 34-to-46), and late adolescence (young adult, PND 46-to-59).…..”

32. According to the above statements, mice in 2 of the 3 groups studied (6 to 7 weeks and 8 to 12 weeks) fall into the adolescent category. What was the purpose of these choices of ages for the mice in this study?
The relevance of using these specific ages is not quite clear. What is the relevance to be able to designate mice as being adolescent or early adults or adults and study the parameters of interest at these time points?

33. Page 14, lines 275- 279: It is stated “In the present study, hematological results revealed relatively lower red blood cell count and hemoglobin levels in BKO mice than previously reported values (De Franceshi et al., 2006; Weizer-Stern et al., 2006; Gardenghi et al., 2007; Vogiatzi et al., 2010; Nai et al., 2012; Gelderman et al., 2015; Kautz et al., 2015; Li et al., 2017). Similar trends were also observed in WT mice (data not shown).”
Data on WT mice need to be shown.

34. Page 14, lines 279- 282: It is stated “….It is noteworthy that the study conducted in 20-week old WT and BKO mice obtained from the same animal facility as our study also reported comparable hematological parameters to our finding (Wannasuphaphol et al., 2005).”
The authors should explain why they consider this observation “noteworthy”.

35. Page 14, lines 282- 283: It is stated “….Although significant differences in MCV, MCHC and RDW across the studied age ranges were found, similar findings were also observed in WT mice and appeared to be transient.”
It is not acceptable to simply make such statements without showing data for WT mice. Readers need to see the data to decide for themselves the credibility of such statements.

36. Page 14, lines 284- 286: It is stated “…In this study, both tissue non-heme iron measurement and histopathological examination revealed progressive iron accumulation in the spleen of thalassemic mice particularly during adulthood whereas liver iron deposition appeared to be generally steady….”
What does the statement “…liver iron deposition appeared to be generally steady…” mean? Please define “generally steady”. What is the data that this statement is based on?

37. Page 14, lines 286- 288: “….Furthermore, a pronounced increase in spleen iron content was observed in BKO mice during late adolescence and early adulthood…..”

And

Page 15, lines 293- 294: “….the pattern of tissue iron deposition between adolescence and adulthood suggests that systemic iron homeostasis could differ with age….”
What do the authors think is the relevance or importance of such changes at these specified time periods?

38. Page 15, lines 309 - 312: “….Our data is in agreement with the work by Gardenghi et al. (Gardenghi et al., 2007) which proposed that the expression of hepcidin may be determined by the relative ratio between anemia and iron overload which may vary depending on age.”
What is mean by the terms “relative ratio between anemia and iron overload”?
It is also not clear how the authors of the present study make the claim they have in the above sentence; please explain.

39. What were the changes in relevant proteins involved in erythropoiesis in the bone marrow, when this site is a major site of the erythroid factors that suppress hepcidin? Why did the authors study only extra-medullary erythropoiesis and not the bone marrow also?

40. Page 16, lines 333 - 335: “….On the other hand, hepcidin expression is induced in
adulthood leading to relatively normalized intestinal iron absorption and relatively stable liver iron accumulation.”
How do the authors explain the induction of hepcidin in adulthood? What is the basis of their saying that this supposed induction led to “….relatively normalized intestinal iron absorption and relatively stable liver iron accumulation…”? If hepcidin was induced, it should have resulted in decreased protein expression of DMT1 and ferroportin in the duodenum. Without data on serum hepcidin concentrations and protein expression of duodenal DMT1 and ferroportin, how do the authors make these claims?

41. Page 16, lines 335 - 337: “….Additionally, the increased erythropoiesis in adult BKO mice could lead to splenic iron acquisition from senescent red blood cells and, thus, resulting in the shift of predominant site of tissue iron accumulation from the liver to the spleen.”
What do the authors base the above statement on?

42. Page 16, lines 338 - 339: “…It is also noteworthy that ferroportin mRNA expression was affected by age in tissue-specific manner….”
What is the basis of the authors making such a statement?

43. Page 16, lines 339 - 341: “…The reciprocal expression between hepcidin and duodenal ferroportin suggests that the expression of ferroportin in the duodenum was under the regulation of hepcidin at least during 6-20 weeks of age….”
Ferroportin is well known to be regulated by hepcidin at the post-translational level (see Drakesmith H, Nemeth E, Ganz T. Ironing out Ferroportin.Cell Metab. 2015 Nov 3;22(5):777-87 for an excellent review). The authors have studied mRNA expression of ferroportin and attempt to explain their observations of changes in mRNA levels in the duodenum as effects of hepcidin. This is not convincing. Data on protein expression or functionality is required to support such a statement.

44. Page 16, lines 341 - 343: “…. ferroportin mRNA expression in the spleen was markedly induced in adulthood and corresponded with the expression pattern of genes involved in hemoglobin synthesis and degradation…..”
This observation can be well-explained by what is known about the transcriptional regulation of ferroportin. However, the authors have made no attempt to do so. They should refer to the review mentioned above (Drakesmith et al, 2015) to enable them to discuss their findings.

45. Page 16, lines 345 - 346: “…. it is likely that increased erythropoiesis is responsible for the increased splenic ferroportin expression in adult BKO mice…”
This is a statement that conveys a superficial understanding of what is known about these phenomena. The authors should discuss these findings (and possible mechanisms) better.

46. Page 16, lines 346 - 348: “…. In the liver, ferroportin mRNA expression was
generally induced in adolescence and adult, possibly, as a result of liver iron accumulation which were steady during this period of lifespan.”
What is the basis for stating that liver iron accumulation was “steady” in adolescent and adult mice? What does “steady” mean in this sentence?

47. On page 12, lines 207-210, it is stated “As shown in Table 4, an increasing age was associated with increased number of liver mononuclear cell infiltration and hematopoietic cells suggesting that the extent of extramedullary hematopoiesis progressively increased at least during the studied age range.”
The relevance/significance of the above observations have not been discussed. The authors should do so.

48. Increased Tfrc mRNA expression, which is one of the observations in the spleen, is an indication of iron deficiency in the cells. How do the authors interpret this observation? They have also not discussed its relevance/significance.

49. Page 16, lines 352 - 354:
“In conclusion, our study demonstrated the differences between iron homeostasis as well as the expression of genes involved in iron transport and metabolism in a mouse model of thalassemia intermedia between adolescence and adulthood.”
This is a poorly constructed sentence and need to be re-phrased for clarity.

50. Page 16, lines 354 - 356:
“During adolescence, a markedly induced Erfe expression results in hepcidin suppression, intestinal iron hyperabsorption and liver iron accumulation.”
A statement of conclusion as above is not warranted in the absence of data on ERFE in the bone marrow and serum levels of ERFE and hepcidin. They have also not shown data to support their conclusion of “intestinal iron hyperabsorption”.

51. Page 17, lines 354 - 356:
 “In adulthood, extramedullary erythropoiesis is enhanced and Erfe induction is relatively diminished leading to BMP6-mediated hepcidin upregulation.”
The above statement is not warranted based on the data shown in this manuscript. No induction of BMP6 has been shown, to indicate that the upregulation of hepcidin in the liver is “BMP6-mediated”, as claimed.

52. Page 17, lines 357:
“Subsequently, intestinal iron absorption is suppressed…”.
No data on measurement of intestinal iron absorption are shown. Hence, the above statement is not warranted based on the data shown in this manuscript.

53. Page 17, lines 358 - 361:
“The present study underscores the significance of age on the pathophysiology of iron loading in thalassemia intermedia. Therefore, the age of thalassemic mice should be considered in the study of iron homeostasis under thalassemic condition.”
The authors make statements that are far too sweeping. They have also not shown anything new that was not shown in the publication by Gardenghi et al, 2007, which is a publication that they themselves have quoted.

54. The authors have provided no information on ethical approval having been obtained for the work done on the mice in the study.

55. The abstract of the manuscript:
a. The language in the manuscript needs improvement for grammatical correctness.

b.  “….by iron regulatory hormone, hepcidin” to be replaced by “by iron- regulatory hormone, hepcidin…”

c. “Notably, effects of age on iron homeostasis in this mouse model particularly during adolescence have not been explored”.
The authors should mention why it would be necessary to explore this.

“Results.
d. Significant differences in the expression of hepcidin and several iron-related molecules across age groups were found.”
This is a very non-specific statement that gives little useful information. The authors should briefly state their findings.

e. “In adolescent BKO mice, ineffective erythropoiesis results in inappropriately low hepcidin expression and upregulation of duodenal iron transporters.”
What was the comparison group? This should be mentioned.

f. “On the other hand,increased expression of hepcidin and several genes involved in hemoglobin metabolism along with normalized expression of duodenal iron transporters was observed in adult BKO mice”
What was the comparison group? This should be mentioned.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: IRON HOMEOSTASIS IN A MOUSE MODEL OF THALASSEMIA INTERMEDIA IS ALTERED BETWEEN ADOLESCENCE AND ADULTHOOD
Review round: 1
Reviewer: 3

Output:
Basic reporting: The use of English is appropriate.
Some references are missing and these have been pointed out in comments to author.
Article structure, figures and tables are appropriate.
Raw data has been given in the supplementary material.
Results are relevant to hypothesis
Experimental design: The manuscript is within the scope of the journal
The research question is well-defined and the results fill a gap in knowledge
The experiments carried out are elegant and well designed.
Methods have been described in sufficient detail. Some comments for improvement have been given in the comments to author.
Validity of the findings: Findings are valid and robust.
The conclusion section is speculative and not entirely supported by the data. Some suggestions for improvement are given in comments to author below.
Additional comments: Abstract:
Methods section of abstract: It is not clear whether comparisons were made between BKO mice and wild-type mice of the same age, or between BKO mice at different ages.
Mention the age of mice in brackets for adolescent, young adult and adult mice.
Results section of abstract: Data are reported only for adolescent and adult mice. There is no mention of results in the young adult group.

Introduction
If Gardenghi et al 2007 have already shown that age influences iron regulatory parameters in BKO mice, then what was the rationale for doing this study? This must be clarified.
Line 50: “In thalassemia…” Change to “In beta thalassemia…”
Lines 66-78: Insert references for the statements made.
Lines 90-97: Insert references for the statements made.
Lines 114-116: May be relevant to provide some more details regarding the phenotype of the Hbbth3/+ mice. For example, what is the extent of anemia in these mice? what are the tissues that are iron overload? Is the spleen iron loaded in these mice? Is there extramedullary erythropoiesis in this model? Is there growth retardation compared to wild-type mice?
Briefly describe what is known about the effect of age on iron metabolism in wild-type mice fed a normal chow diet.
The Introduction section can be shortened by deleting some of the irrelevant portions.

Materials and methods:
Mention C57Bl/6 J or C35Bl.6 N
What is the iron content of the rodent chow that was provided to the mice?
Authors are encouraged to submit the ARRIVE checklist as a supplementary file

Results:
Tables 1 and 2: Is there data available for age-matched wild-type mice?
Table 1 shows a 50% reduction in liver iron in young adult mice. However, this reduction is not reflected in the histopathological scoring in Table 1. What is a possible reason for this?
Figure 3: From the figure legend, it is not clear how the authors calculate the fold change compared to WT mice. However, from the raw data provided in supplementary material, it is apparent that the average obtained for WT mice at each age was used for normalization. This information must be provided in the legend.
Since there are likely to be age-related changes in wild-type mice as well, it may be better to show the data for wild-type and BKO mice at each age (rather than show fold change compared to wild-type). The y-axis can show delta Ct values instead of fold changes. This will yield more information. If the authors do this, then 2-way ANOVA will be the correct statistical test.
Figure 4: Same comment as for Fig 3 regarding showing the data for WT mice. Line 221: The authors state the hepcidin mRNA was marginally lower than the corresponding WT group. This is difficult to appreciate in Fig 4 because the data for WT is not shown. It is also not clear if the decrease was statistically significant even if it is “marginal”.
Line 221-222: It is possible to show that hepcidin expression was inappropriately low for liver iron content in BKO mice by showing data for the ratio of hepcidin mRNA to liver iron content. This will also clarify if in adult mice the hepcidin expression (which was increased) was appropriate for liver iron content.
Figure 4: It would be interesting to know the actual mRNA expression levels of GDF-15, TWSG-1 and ERFE in the liver and spleen in WT mice (since the expression of these “erythroid regulators” are usually looked for in the bone marrow). This would provide baseline information in order to interpret the increase seen in BKO mice.

Discussion
Lines 265 to 271 which gives the rationale for selecting the ages of mice for this study should probably be given at the end of the introduction section or in methodology. This will make better sense as the mice are described here and an obvious question would be why these particular ages were chosen.
It would be interesting to see if Zip14 mRNA levels in the liver changes with age in WT and BKO mice
Lack of data on protein levels must be mentioned as a limitation of this paper.
Lines 301 and 306: Contrary to what the authors have stated, I would argue that the hepcidin levels are not explained by ERFE in the spleen since ERFE in spleen is decreased both in young adults and adults while hepcidin is increased only in adults. Therefore, the increase in hepcidin expression seen only in adult BKO mice is not explained by changes in ERFE in the spleen alone. Do the changes in liver hepcidin expression reflect the changes in expression of the erythroid regulators in the bone marrow? Lack of data on the expression of GDF-15, TWSG-1 and ERFE in the bone marrow is also a limitation of the paper.
Lines 331 -333: The ERFE-mediated suppression in hepcidin that the authors refer to is not clearly shown as per data in Fig 4.

Conclusion:
Lines 352 – 358: The description in these lines is not entirely supported by the data presented in the paper. They may be considered speculations based on data obtained. The authors are encouraged to call it as such and maybe provide a summary figure to describe it better. This must not be included in the conclusion section.
Lines 358 to 361 accurately state the conclusions that can be drawn from this study and can be retained.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: IRON HOMEOSTASIS IN A MOUSE MODEL OF THALASSEMIA INTERMEDIA IS ALTERED BETWEEN ADOLESCENCE AND ADULTHOOD
Review round: 2
Reviewer: 1

Output:
Basic reporting: No comment.
Experimental design: The authors have addressed the key points raised in my review. I have a minor issue with the way qPCR data are presented. The authors show ΔCt values, where an increase means decrease in mRNA expression. This is counterintuitive for the reader. I would suggest to show normalized values relative to β-actin in wt young mice. Alternatively, they could show -ΔCt values.
Validity of the findings: No comment.
Additional comments: The overall manuscript is improved.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: IRON HOMEOSTASIS IN A MOUSE MODEL OF THALASSEMIA INTERMEDIA IS ALTERED BETWEEN ADOLESCENCE AND ADULTHOOD
Review round: 2
Reviewer: 2

Output:
Basic reporting: Language needs editing.

Relevance of study unclear

Several issue raised not satisfactorily addressed.
Experimental design: The observations do not seem to contribute to knowledge in the field; it is unclear how they.are relevant.
Validity of the findings: Relevance of the observations unclear.
Additional comments: The authors have revised the manuscript to rectify very fundamental defects in their original submission. They report various observations. However, how their observations are relevant or add to knowledge in the field are unclear. Why would it matter if “Iron homeostasis in a mouse model of thalassemia intermedia is altered between adolescence and adulthood”? The authors state that their study “underscores the importance of the age of thalassemic mice in the study of molecular or pathophysiological changes under thalassemic condition”. It is hard to understand how this is relevant. They have not studied many key parameters, such as serum levels of hepcidin or expression of erythroid regulators involved, which may have been added something to the new and different to the study. In addition, they have addressed many of the reviewer’s comments in a rather lazy way, and not very meticulously. Too many of the issues raised have merely been mentioned in the manuscript as limitations. I do not think the manuscript adds anything significant to the field.

English language editing is required.


Instruction: You are one of the reviewers, your task is to write a review for the article. You will be given the title of the article, the number of the round in which the article is located, and your order among the reviewers.

Input:
Title: IRON HOMEOSTASIS IN A MOUSE MODEL OF THALASSEMIA INTERMEDIA IS ALTERED BETWEEN ADOLESCENCE AND ADULTHOOD
Review round: 2
Reviewer: 3

Output:
Basic reporting: N/A
Experimental design: N/A
Validity of the findings: N/A
Additional comments: It is well-appreciated that the authors have addressed most of the comments and re-analyzed the data by 2-way ANOVA which I think is the correct statistical test to be used for the 2 x 2 design of this study.
Some points to note and address in the revised manuscript are listed below:

Important
1.	Whenever a significant interaction is present (in 2-way ANOVA) post-hoc tests should be done for ALL the relevant pair-wise comparisons. For example, in table 2, the superscript “a” and “b” have been used for comparisons between adolescent and adult mice within phenotypes. Although the results section state that values for Hb etc were significantly higher in WT than BKO for both adult and adolescent mice, this fact is not shown in the table. The authors are encouraged to used additional superscripts to show significant differences between WT adolescent and adult mice and similarly for BKO adolescent and adult mice. This will give a clearer picture. Same applies for liver iron, spleen iron etc in Table 2 and in Table 4 and also for all the figures.
2.	The figure legends shown just above each figure in the pdf provided for review states that the statistical test used was 1-way ANOVA. I suppose this is from the original submission and must be deleted. The list of figure legends given after references is correct.
3.	The authors have now shown the delta Ct values in the figures instead of fold changes and this is very good. However, the fact that delta Ct (and not minus delta Ct) was shown makes interpretation a little complicated because a decrease in value indicates induction and an increase in value indicates repression. To overcome this, I suggest minus Ct be shown on the y-axis so that an increase will indicate induction and a decrease will indicate repression. This will make interpretation a little easier and straight-forward for the reader.

Minor:
Discussion:
1.	It is interesting that in adult BKO, hepcidin mRNA increased compared to adolescent but the hepcidin-liver iron ratio did not change, suggesting that the increase in hepcidin was appropriate for the increase in liver iron in these mice. Recently it has been shown that ERFE acts by binding to BMP6 (Arezes J et al Blood 2018). This can be added to the discussion.
2.	The increase in mRNA expression of duodenal iron transporters is not explained by the effects of hepcidin because these changes were seen in adolescent mice when hepcidin was similar between WT and BKO mice. Perhaps the effect of hypoxia (due to anemia) on stability of duodenal HIF2 (which is known to regulate dcytb, dmt1 and ferroportin mRNA levels) may be involved. This can be discussed.
3.	It is good practise to submit the ARRIVE checklist for all animal-based studies. I would strongly suggest that this checklist be submitted with the revised manuscript as a supplementary file.