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Dear authors,
After vigorous reviews and revisions, our reviewers are satisfied with the manuscript in present form. Therefore, with pleasure I inform you that the manuscript is accepted at editorial level.
All the best for your further submissions.
[# PeerJ Staff Note - this decision was reviewed and approved by Vladimir Uversky, a PeerJ Section Editor covering this Section #]
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Dear authors,
After repeated comments and your efforts to resolve the issues, our reviewers still feel that there are certain points to be addressed sincerely. Therefore, I invite you to address them and do the needful. Title also may be revised as requested by thereviewer. Please address all the issues and resubmit with all changes asap.
All the best
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The authors addressed most concerns adequately, but the multiple comparisons issue and limited power analysis remain valid concerns that could affect the robustness of their conclusions.
The authors have not addressed the multiple comparisons issue and limited power analysis concern that could affect the robustness of their conclusions. Claiming Asb3 is "dispensable" may be overstated given low power. Given the present experimental profile, I guess authors should revisit the title and clearly state Asb3 knockout does not produce detectable fertility defects under current experimental conditions" rather than definitively "dispensable".
Dear Authors,
We appreciate your efforts to improve the manuscript, but a new reviewer still has some points to be addressed. Please do the needful and submit asap.
All the best.
All ok and aligns well with the conventional scientific reporting format, facilitating comprehension of the methodological approach and findings.
Statistics is confusing as to why authors have used both ANOVA and t-tests for comparing just the two groups (Asb3+/- vs Asb3-/-). Why use both? T-tests would work fine here. Also, with only 3 mice per group authors really need to show that data meets the assumptions for these tests. Did you check if the data was normally distributed? If not, consider non-parametric tests instead.
Another thing tests run on lots of different parameters without mentioning any correction for multiple comparisons. This raises the risk of finding false positives by chance. And I'm wondering why you used heterozygous mice as controls rather than wild types? This choice needs some explanation.
My suggestion is to revise the statistical section, give us the actual p-values (not just p>0.05), and acknowledge the limitations of your small sample size. Your conclusion about Asb3 being dispensable might be right, but these changes would make your case much stronger.
The paper shows that knocking out Asb3 doesn't seem to impact male fertility or sperm development in mice. While the data looks consistent across experiments, I have some reservations about how conclusive we can be.
Firstly, i will like to see the actual p-values with confidence intervals rather than just "P>0.05" throughout the manuscript. This would give readers a better feel for how close any differences might be to significance.
With only 3 mice per group, the study is honestly underpowered. This small sample size makes it hard to catch subtle changes in fertility or sperm function that might still be biologically relevant. Have you considered whether other Asb family members might be compensating for the loss of Asb3? This seems especially important given your previous finding that Asb3 expression increases in Asb12 knockout mice "https://pmc.ncbi.nlm.nih.gov/articles/PMC8899140/". Maybe running some expression analysis on other family members in your knockouts would strengthen your "dispensable" conclusion.
Rest all is ok
Dear authors,
We appreciate your efforts to improve the quality of the manuscript but one of our reviewers still feels that some points need to be addressed regarding materials and methods. Please do the needful and resubmit asap.
All the best
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No comment.
When I asked the following question: "3. It is not clear how many animals were used in total. Did the authors use 3 mice/group or more, which were separated into several experiments?", the authors answered that "For each experiment, two mice are selected and divided into a knockout group and a control group. The experiment is repeated three times to ensure that the data meets statistical requirements."
From my understanding, these authors used 2 mice/group (n=2) and performed 3 technical replicates using each mice. A technical replicate does not substitute an experimental unit, which was in fact n=2. Using just 2 experimental units per group is too low to provide reliable, reproducible, and statistically meaningful results. With only 2 experimental units per group, this study lacks sufficient statistical power to detect even large differences between groups (effect size) and the estimate of the variability will be extremely imprecise. Even for a pilot or exploratory study, 2 experimental units would be too short. There are cases that 3 experimental units may be sufficient; however, it comes with a high risk of type I errors. Therefore, I recommend increasing the experimental units size to improve the study design and increase the statistical power.
In addition, the authors mentioned that "Sperm motility was measured through sperm swelling experiments". The hypo-osmotic swelling test (HOST) is a method used for membrane integrity evaluation (indirect indicator of sperm vitality) and not motility. Usually, sperm motility is evaluated using a pre-warmed microscope slide and microscopically evaluated through counting and classifying at least 200 sperm cells in random fields (non-motile, in situ, slow progressive and rapid progressive).
As aforementioned, I have serious concerns on the validity of the present findings since only 2 experimental units were used in this study.
In addition, the authors failed to provide an explanation for the >10ºC variation on the qPCR melting curve data for the same target using different samples, which suggests that the primers may not be specific.
Moreover, the antibodies lack proper validation and, as the authors mentioned, resulted in several non-specific signals in both IF and WB.
Overall, the results could be interesting but I have serious concerns on the used methodology and data validity. Further experimental units are required to improve the study design and increase the statistical power.
I hope that the authors can use the comments of both reviewers to improve the study design and the validity of their findings; however, I cannot recommend this work to be published at the present form.
Dear authors,
As per the recommendations of our expert reviewers, the manuscript has some points to be addressed. Therefore, I invite you for major revision of manuscript.
Please do the needful and resubmit asap.
All the best.
The font size in the figure should be uniform, and the format in the text should be unified in accordance with the standards, such as leaving a space between numbers and units. Please check the details of the article throughout.
The author constructed ASB3 gene knockout mice and conducted tests on reproductive capacity, sperm quality and spermatogenesis process, indicating that ASB3 is not essential in spermatogenesis. This paper has made some contributions to the exploration of the mechanism of spermatogenesis, but the experimental group design of the article is not perfect enough, and the standards for drawing are not strict enough, which should be further improved.
1. Did the absence of ASB12 lead to any changes in the protein expression of ASB3? If you are unable to complete this experiment, please explain the reason.
2. This study examined the reproductive capacity and sperm quality of heterozygous and KO mice. Why were WT mice not checked? I think that WT mice as the Control group would be more appropriate. Therefore, some experiments on the reproductive capacity and sperm quality of WT mice should be added.
3. Is there a difference in the expression of Asb3 between WT mice and heterozygous mice? It should be detected at both mRNA and protein levels.
4. The sperm morphology detection results in Figure 4B should be more logically consistent with the sperm HE staining image after Figure 3G.
5. What is the expression of ASB3 in the sperm of WT and KO mice?
6. According to the HE image in Figure 4c, the structure of the seminiferous tubules in the heterozygous mice is not normal. Therefore, it is necessary to add the HE staining of the testicular sections of the WT group in Figure 4C.
In the article entitled "Asb3 is dispensable for spermatogenesis and male fertility in mice" by Changtong Xu et al., the authors produced an Abs3-KO mice model to study the role of this protein on male fertility.
I am pleased that the authors decided to report a often called "negative results" work, where it is suggested that the lack of ABS3 in mice does not impact spermatogenesis. The fact that this protein seems to not be relevant for spermatogenesis and male fertility, at least at the macro level, is a valid result and important finding for the field.
Overall, I found the article clear and concise. The introduction clearly describes the state-of-the-art on the research topic and how this project fills a gap in knowledge in the field. I only have a small correction for the introduction: at line 36, when the authors mention "TTLL3 and TTLL8" please italicize the gene name to comply with the correct nomenclature for mice.
The article follows a classic structure. I found the figures relevant for the article content and with good resolution, despite some concerns I raised (see next sections). However, I think the legends should be improved as they contain some typing mistakes. The respective raw data is included in the submission, according to the journal guidelines; nevertheless, I think some raw data might be missing, dependent on how the methods were conducted (see next sections).
Despite the clarity of the article, I have several concerns on the methods and results, which I highlight on the following sections.
The research question is well defined: "does ABS3 knockout affect male fertility in mice?". The gap in knowledge as well as the relevance of this study for the field are well defined.
However, I have several concerns about the methods and results that I would like the authors to address. Starting with methods:
1. In my opinion, the information concerning the mice strain and Ethical Approval should be right at the beginning of the "Animals" section and not on lines 104-107.
2. On lines 94-99, the authors describe how mice were sacrificed. This is a very long and detailed description that, in my opinion, could be substituted for "Mice were sacrificed using CO2 and according to the ethical guidelines for animal experiments". In addition, it is mentioned on line 99 that mice "were disposed of humanely". Do you mean you used a confirmation method? Please elaborate on the meaning of "humanely".
3. It is not clear how many animals were used in total. Did the authors use 3 mice/group or more, which were separated into several experiments?
4. On line 126 the authors mentioned that the heterozygous Asb3+/- mice were used as control. It is not clear why did the authors use these mice as control and did not include wildtype mice.
5. On lines 126-127 the authors describe how the fertility test was conducted. This test should be described in more detail. Mating pairs were placed together each morning, but what were the conditions? For how long? During how many days were their paired? On line 127-128 the authors mentioned "litter details", I would suggest replacing for "Data on the litter were collected".
6. The RT-qPCR topic (lines 130-137) is poorly described. The authors did not mention which mRNAs were quantified; no primer data; no RT-qPCR conditions and cDNA dilution (if any); no polymerase or probe references; nor how the data quality and primer specificity was assessed; nor how the relative expression was calculated. For instance, I could see a 10 degree variation on the melting curve data for the same target on different samples, which raises some concerns on the validity of this assay.
7. The epididymal sperm collection method (lines 153-161) is also poorly described. The epididymis was cut and suspended in HTF media, but for how long? Did the authors use agitation? On line 159, the authors mentioned that sperm viability was assessed. How? eosin-nigrosin staining? Hypo-osmotic swelling? The authors also report motility and morphology data. How were motility and morphology assessed? How many sperm cells were counted per slide? Were they counted by the same operator? Which counting technique was applied? On line 160, it is mentioned that "each experiment requires a pair of Asb3+/- and Asb3-/- mice". Does it mean that these experiments were conducted as n=2 and 3 slides per mice?
8. On the IF section (lines 172-182) the authors did not mention which primary or secondary antibodies were used or the dilution. Without the antibody reference or proof of its validity/specificity, the results might not be valid.
9. I recommend the authors to plot all data with SD instead of SEM. In terms of statistics, SD provides more information; moreover, the SEM gives the illusion of a decreased error when, in fact, the value is diluted the bigger sample sizes are. In addition, I recommend including data points if using bar plots (combine scatter plots with bars) or, as an alternative, box and whisker plots. Please also include how data normality was calculated.
I have several concerns about the validity of findings, mainly due to the poorly described methods.
1. The first topic (lines 197-204) describe the Asb3 relative expression on the testes of Asb12 KO mice. This result seems to arise from the authors previous work; if the authors repeated the experiment, the methods section fails to describe it. I would recommend to remove this topic, as it is already included in the introduction section that Asb3 is upregulated in Asb12 KO mice, suggesting a potential compensatory mechanism.
2. Does Fig. 1B refer to 8-week old mice?
3. In my opinion, Asb3 expression peaks at 4-week old but begins to be highly expressed at 2-week old.
4. Fig. 1D compares wildtype to Asb3 KO mice, however all other results use Asb3+/- as control. Why not include both wildtype and heterozygous in the study, and use wildtype as the control?
5. Also in Fig. 1D, the antibody for Asb3 seems to not be specific, as some peritubular myoid cells and Leydig cells are strongly stained even in the KO mice. Did the authors validate the antibody? Is there any Western Blot to supplement these result?
6. On line 228, the authors do not need to mention that GraphPad was used for statistical analysis as it is already mentioned in the methods section.
7. Concerning the spermatogenesis markers (Fig. 5), it is not clear how stain-positive cells were counted or how the positive cells/tubule ratio was calculated. Raw data only contains 1 picture of each antibody and group, which does not provide enough data to evaluate the results. Once again, the authors fail to mention antibody data and respective validation/specificity. For instance, the SOX9 antibody, which is reported as a exclusive Sertoli cell marker, also stains spermatids and Leydig cells.
8. Did the authors consider to test for the remaining Asb family members expression on the Asb3 KO mice? Since there is evidence of a compensatory mechanism on Asb12 KO mice, which exhibited an upregulated Asb3, could the same happen with other family members in the Asb3 KO mice? In my opinion, it would be a valuable addition to this work and would validate the requirement for further double KO studies.
The discussion section should also be improved, as some generalizations are made that do not reflect the observed findings:
9. In the discussion section (lines 283-286), the authors mentioned that existing studies primarily focus on phenotype analysis and not on molecular mechanisms, which is exactly the case of this observational study. Are the authors considering these as future perspectives?
10. On lines 288-289, authors mentioned "research into the mechanisms of E3 ubiquitin ligase inactivation (...) offers medical evidence and a foundational research framework for the development and translation of male contraceptives". In my opinion, this work does not provide any advance towards the development of novel male contraceptives nor exists sufficient evidence that this enzyme family can be used as target for that purpose. This sentence should be reconsidered.
11. On lines 290-291, the authors mentioned "this research serves as a reference point for subsequent clinical diagnosis and genetic screening". How? Since Abs3 KO seem to not produce any effects on male fertility, how can these results be used for clinical diagnosis? What would be the relevance to screen the infertile men population for Abs3 mutations? I would also reconsider this sentence.
Overall, I found the results interesting but I have several concerns on their validity. The methodology should be described in more detail or the results cannot be correctly validated and interpreted.
I consider that the manuscript cannot be published at the present form. However, I would consider giving the authors the opportunity to clarify the methodology, antibody specificity, and data analysis.
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