Toxicological Impacts of Polypropylene Nanoparticles Similar in Size to Nanoplastics in Plastic-Bottle Injections on Human Umbilical Vein Endothelial Cells

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The study of Jie Wang, Zhong-Lan Chen, Cheng-Gang Liang, Hui-Ying Yang, Xian-Fu Wu and Hui-Min Sun, named “Toxicological impacts of polypropylene nanoparticles in plastic-bottled injections on human umbilical vein endothelial cells”, is devoted to the problem of clarifying the molecular-cellular mechanisms of action micro- and nanoplastics on the human body, especially the cardio-vascular system. The work has several strengths and weaknesses.

The introduction contains detailed quantitative data on the characteristics of plastic nanoparticles, their routes of entry, accumulation, transport through the body and elimination from the body, which justifies the choice of the studied doses of plastic nanoparticles. Figure 1 complements the text excellently.

The overall research plan is consistent and well thought out. The results obtained complement each other and allow the authors to draw well-founded conclusions.

The list of materials contains a list of catalog numbers, which significantly simplifies the reproducibility of experimental data by other authors.

However, the work can be significantly improved and clarified to attract more attention from readers. I believe that the work can be published in the journal Toxins after peer review.

Main comments:

The authors clearly indicate the impossibility of studying NPs from plastic bottles and the alternative use of commercially available NPs. I think that the title can simply be left as "polypropylene nanoparticles" or make a softer accent "plastic-bottled-like polypropylene nanoparticles". I think the word "injections" can be omitted from the title.

It is advisable to add information on the number of passages for the cell lines on which the experiments were performed. For endothelial cells, especially HUVEC, the passage number is critical for obtaining adequate results.

Brief information about healthy volunteers is also desirable to provide: total number, age, gender distribution, what details of the anamnesis were checked before the study.

For endothelial cells, special surface treatment for attachment is important. It is advisable to detail whether such treatment was done (e.g. pretreatment with gelatin or use of commercially available pretreated glassware).

Due to the high diversity of ROS, it is desirable to specify which forms are registered. The technical documentation states that this is especially superoxide and hydroxyl radicals. Please add clarification to the text. It would also be desirable to clarify which ROS pool is measured: extracellular, intracellular, or total.

It is important to add information about the lipopolysaccharide used. The immunogenicity of LPS depends significantly on the species and strain of the producer bacteria. Some LPS may not cause an immune response, while others may cause hyperactivation of cells. It is very important to indicate the species name of the bacteria and the strain, preferably with the serotype.

Please clarify at what temperature and for how long were the ELISA samples stored?

Using Student's t-test and one-way ANOVA with Tukey's test gives adequate results only in the case of normal distribution of values in the compared samples. The authors need to add information about the test of normality of distribution of sample values. In case the normality test (for example, the Shapiro-Wilk test) is not passed, then the authors will need to recheck the statistical hypotheses using more adequate methods of nonparametric statistics, for example, the Mann-Whitney U test or Kruskal-Wallace ANOVA with post-hock Dunn's test.

Figure 3. In the title, the word “necrosis” should be replaced with the more general “cell death”. Since this method analyzes the ratio of cells in apoptosis and necrosis. The authors extracted only one third of the information from their results. I suggest that the authors analyze the cytometry data in a classical way and determine the proportions of living cells (Q3), cells in early (Q4) and late apoptosis (Q2), necrosis (Q1). I believe that adding these data will strengthen the work and help with the discussion of the results of molecular methods. In addition, 2D dot plots in panels D-E appear insufficiently compensated (presence of a diagonal “tail of dots” at 45% angle). Please check your compensation matrix or change the gating according to the cloud shapes and recalculate results.

Please add description of sample preparation for SEM in the materials and methods section.

Figure 4. Panels Ab and Bf It are advisable to increase so that they are easier to read. Red letters are not very clearly readable on a gray background, perhaps the color should be changed. If there are examples of microphotographs of fluorescence microscopy, it is also advisable to provide them and add a color scale of brightness for fluorescence. I think that this will make the results more clear.

Line 282. The results demonstrated by the authors show the prevalence of cell death through apoptosis (with the majority of cells being in the early apoptosis phase, see Fig3 Q4). Annexin - V - FITC is a specific marker of apoptosis. The proportion of necrotic cells also increases, but less pronouncedly.

Line 288: The conclusion at the end of the subsection looks correct, but it could be strengthened by adding a quantitative assessment of the ratio of cells in apoptosis and necrosis.

Figures S 1 and S 2 provide insufficient information about LC3B fluorescence. The signal appears to be either absent or too low. In the first case, a positive control must be added to compare the experimental values obtained. In the second case, image post-processing (the same everywhere) must be performed to improve the signal display.

Figure 6H. The font is difficult to read. It is advisable to increase the size of the panel.

Figure 7. It is also necessary to specify the incubation time with LPS for each cytokine. If it is also 72 hours, it is advisable to add shorter incubations, for example, 4 or 24 hours, depending on the dynamics of LPS-induced cytokine secretion known from the literature. To obtain the most adequate results, in the case of PP-NPs, it is also critical to use their own incubation times for each cytokine, corresponding to their peak concentrations. In three days, all inflammatory reactions could have already passed. It is advisable to supplement measurements with adequate time points for each cytokine, if this is methodologically possible.

Figure 8. It seems that the figure does not always indicate statistical differences where they exist (e.g. panels b and c are LPS variants). Please recheck.

The discussion indicates a zeta potential value of less than 5 mV modulo. These values are typical for unstable colloids, in which NPs quickly aggregate with each other and precipitate. The authors should discuss this issue in more detail. Next comes a detailed description of the NPs dispersion procedure. Am I right in understanding that this is a natural consequence of aggregation? If so, it would be desirable to state this idea more clearly.

Do I understand correctly that 0.01% Tween 80 was also added to the control samples of cultures without NPs? If so, this clarification should be added in the materials and methods section.

The authors provided detailed theoretical data for potential extrapolation in vivo, however, I think it would be better to use a softer formulation in the introduction, for example, “potentially in vivo”

Since the study used the blood of healthy volunteers, it is necessary to provide information on obtaining written informed consent from the study participants, and the number of the conclusion of the bioethics commission with the date of receipt. It is strictly necessary to indicate whether the requirements of the Declaration of Helsinki were observed when working with volunteers.

Minor:

Authors are encouraged to check and accept all edits to the text (example, line 126) at the next stages of editing.

Line 132: Extra space in annexin V - fluorescein

 

Best regards

Comments for author File: Comments.pdf

Author Response

Comment 1：The authors clearly indicate the impossibility of studying NPs from plastic bottles and the alternative use of commercially available NPs. I think that the title can simply be left as "polypropylene nanoparticles" or make a softer accent "plastic-bottled-like polypropylene nanoparticles". I think the word "injections" can be omitted from the title”.

Response 1: We have modified the title as ‘Toxicological impacts of polypropylene nanoparticles similar in size to nanoplastics in plastic-bottled injections on human umbilical vein endothelial cells’.

Comment 2: It is advisable to add information on the number of passages for the cell lines on which the experiments were performed. For endothelial cells, especially HUVEC, the passage number is critical for obtaining adequate results.

Response 2: We have added the passage numbers of HUVECs to the section 2.2.

Comment 3: Brief information about healthy volunteers is also desirable to provide: total number, age, gender distribution, what details of the anamnesis were checked before the study.

Response 3: “This is a reference to the nanoplastics data in relevant literature: whole blood samples from 22 healthy, non-fasting adult volunteers. The gender ratio is unknown, and it is not certain whether the patients' medical history was investigated before the study”. We have added it to paragraph 2 in the section 2.2.

Comment 4: For endothelial cells, special surface treatment for attachment is important. It is advisable to detail whether such treatment was done (e.g. pretreatment with gelatin or use of commercially available pretreated glassware).

Response 4:  “…The surfaces of the purchased cell culture flasks and well plates have been treated with TC, and they can be directly used for the cultivation of umbilical vein endothelial cells without further processing ……”. We have added it to paragraph 2 of section 2.2.

Comment 5: Due to the high diversity of ROS, it is desirable to specify which forms are registered. The technical documentation states that this is especially superoxide and hydroxyl radicals. Please add clarification to the text. It would also be desirable to clarify which ROS pool is measured: extracellular, intracellular or total .

Response 5: “We measured the superoxide free radicals and hydroxyl free radicals within the cells.”. We have added it to the section 2.4.

Comment 6: It is important to add information about the lipopolysaccharide used. The immunogenicity of LPS depends significantly on the species and strain of the producer bacteria. Some LPS may not cause an immune response, while others may cause hyperactivation of cells. It is very important to indicate the species name of the bacteria and the strain, preferably with the serotype.

Response 6: “We have added the product numbers of lipopolysaccharides, as well as the species and sources of the strains.”. We have added the information to the section 2.1.

Comment 7: Please clarify at what temperature and for how long were the ELISA samples stored?

Response 7: The samples are prepared on the spot and centrifuged at 4℃. Before the Elisa reaction, the samples are stored in an ice bath, but completed the experiment within 1 hour.

Comment 8: Using Student's t-test and one-way ANOVA with Tukey's test gives adequate results only in the case of normal distribution of values in the compared samples. The authors need to add information about the test of normality of distribution of sample values.

Response 8: All the normality tests for the samples have been supplemented and are presented in Supplementary Figure 5.

Comment 9: 

Figure 3. In the title, the word “necrosis” should be replaced with the more general “cell death”. Since this method analyzes the ratio of cells in apoptosis and necrosis. The authors extracted only one third of the information from their results. I suggest that the authors analyze the cytometry data in a classical way and determine the proportions of living cells (Q3), cells in early (Q4) and late apoptosis (Q2), necrosis (Q1). I believe that adding these data will strengthen the work and help with the discussion of the results of molecular methods. In addition, 2D dot plots in panels D-E appear insufficiently compensated (presence of a diagonal “tail of dots” at 45% angle). Please check your compensation matrix or change the gating according to the cloud shapes and recalculate results.

Response 9: Thank you for your suggestion. Due to the limited time for response, it was not possible to purchase the corresponding reagents to separately count the cells at different periods. I hope you can understand. However, in future in vivo animal studies, I will definitely add such experimental items. I'm very sorry. Later, after checking the compensation matrix or changing the gating based on the shape of the cloud map, no problems were found. Please understand. Thank you. 

Comment 10: Please add description of sample preparation for SEM in the materials and methods section.

Response 10: “The description of sample preparation for SEM has been added to ‘Materials and Methods’ 2.2”. We have added it to the paragraph 2 of section 2.2.

Comment 11: Figure 4. Panels Ab and Bf It are advisable to increase so that they are easier to read. Red letters are not very clearly readable on a gray background, perhaps the color should be changed. If there are examples of microphotographs of fluorescence microscopy, it is also advisable to provide them and add a color scale of brightness for fluorescence. I think that this will make the results more clear.

Response 11: We have made the necessary changes as requested. Please refer to the figures in the manuscript for details.

Comment 12: Line 288: The conclusion at the end of the subsection looks correct, but it could be strengthened by adding a quantitative assessment of the ratio of cells in apoptosis and necrosis.

Response 12: We have added the descriptions in Section 3.2. Please refer to the manuscript for details.

Comment 13: Figures S 1 and S 2 provide insufficient information about LC3B fluorescence. The signal appears to be either absent or too low. In the first case, a positive control must be added to compare the experimental values obtained. In the second case, image post-processing (the same everywhere) must be performed to improve the signal display.

Response 13: We have added positive control images and revised the images. Please refer to the ‘Supplementary materials’ section.

Comment 14:  Figure 6H. The font is difficult to read. It is advisable to increase the size of the panel .

Response 14: We have made the necessary changes as requested. Please refer to the figures in the manuscript for details.

Comment 15: Figure 7. It is also necessary to specify the incubation time with LPS for each cytokine. If it is also 72 hours, it is advisable to add shorter incubations, for example, 4 or 24 hours, depending on the dynamics of LPS-induced cytokine secretion known from the literature. To obtain the most adequate results, in the case of PP-NPs, it is also critical to use their own incubation times for each cytokine, corresponding to their peak concentrations. In three days, all inflammatory reactions could have already passed. It is advisable to supplement measurements with adequate time points for each cytokine, if this is methodologically possible.

Response 15: Thank you for your suggestion. It will be implemented in future animal experiments. Due to the limited response time, we were unable to purchase the required reagents to complete the research. Please understand. Additionally, we assure you that the results obtained in this article are true and reliable.

Comment 16: Figure 8. It seems that the figure does not always indicate statistical differences where they exist (e.g. panels b and c are LPS variants). Please recheck.

Response 16: LPS was used as the positive control. The amounts of IL-2 and IL-6 induced were different. Moreover, in both graphs, I don't think it is necessary to statistically analyze the significant differences caused by the positive control.

Comment 17: 

The discussion indicates a zeta potential value of less than 5 mV modulo. These values are typical for unstable colloids, in which NPs quickly aggregate with each other and precipitate. The authors should discuss this issue in more detail. Next comes a detailed description of the NPs dispersion procedure. Am I right in understanding that this is a natural consequence of aggregation? If so, it would be desirable to state this idea more clearly.

Response 17: Since this paragraph mainly compares the toxicological differences caused by commercialized polypropylene particles and nanoplastic in bottles on cells through charge and surface area, the two are very similar. Therefore, the commercialized particles can represent the toxicological damage of nanoplastic in bottled injectables to cells.

Comment 18: Do I understand correctly that 0.01% Tween 80 was also added to the control samples of cultures without NPs? If so, this clarification should be added in the materials and methods section. 

Response 18: “Yes，you can. All the negative controls were obtained by culturing the cells in a medium containing 0.01% of Tween 80.”We have added it to the paragraph 2 of section 2.2.

Comment 19: The authors provided detailed theoretical data for potential extrapolation in vivo, however, I think it would be better to use a softer formulation in the introduction, for example, “potentially in vivo .

Response 19: Thanks to the reviewer's suggestions, I have added the word ‘potentially’ in the second paragraph of the "Introduction" to express it more gently.

Comment 20: Since the study used the blood of healthy volunteers, it is necessary to provide information on obtaining written informed consent from the study participants, and the number of the conclusion of the bioethics commission with the date of receipt. It is strictly necessary to indicate whether the requirements of the Declaration of Helsinki were observed when working with volunteers.

Response 20: The content of nanoplastics in the blood of healthy individuals as described in this article is based on the reported literature. The detailed information is elaborated in the second paragraph of ‘Materials and Methods’.

Comment 21: Authors are encouraged to check and accept all edits to the text (example, line 126) at the next stages of editing. Line 132: Extra space in annexin V - fluorescein .

Response 21: Yes, we will. We have removed the extra spaces in the section 2.9. Please refer to the manuscript for details.

Reviewer 2 Report

Comments and Suggestions for Authors

Respected Jie Wang and co-authors conducted a very interesting study evaluating the toxic effects of polypropylene nanoparticles on human umbilical vein endothelial cells. The ubiquity of plastic brings the problems of nanoparticle toxicity to humans, animals and plants to the forefront. Plastic nanoparticles are formed when liquid comes into contact with plastic, including medical liquids in plastic bottles. Polypropylene is one of the six food plastics, and its effects are less studied than the effects of polystyrene. To test their hypothesis, the authors used model standard nanoparticles, and I think this approach is correct for the reproducibility of the experiments. The authors assessed cell survival, determined ROS, which are one of the causes of toxicity, the level of LDH as a marker of membrane damage, a cytokine test, annexin staining for apoptosis, and also a study of RNA using PCR. The obtained data convincingly demonstrate the toxicity of nanoparticles in relation to human cells. I highly appreciate this work and believe that it is useful from both a fundamental and a practical point of view.

The manuscript consists of standard sections, is well structured, the content corresponds to the title. The study design, choice of data and statistical processing methods seem adequate to me. The methods are described in detail and allow the experiments to be reproduced. The manuscript contains 8 figures and a table, as well as supplementary materials that correctly reflect the main results of the article and are easy to interpret. The authors' conclusions correspond to the evidence provided. The discussion is written interestingly and at a good scientific level. The overwhelming majority of references (almost 90%) are from the last five years, so the article contains the most up-to-date information.

I recommend the article for publication; I have only a few minor comments.

1. The lower boundaries of the error bars are missing in the diagrams in Figures 2A, 3F, 4B,F, 5F, 6F, 7, and 8.
2. Please indicate the statistical software used to perform the calculations in subsection 2.12.
3. Please reorganize the text so that the references to the figures are before the figures.
4. Subsection "2.2. Necrosis, not autophagy, mediated PP-NP-induced decrease in viability" should have the number 3.2.
5. Some figures are of insufficient quality. These are the diagrams in Figures 4, 5, 6. I would recommend making the size of the panels larger, and this will improve the quality of the figures.

Author Response

Comment 1: The lower boundaries of the error bars are missing in the diagrams in Figures 2A, 3F, 4B,F, 5F, 6F, 7, and 8.

Response 1: We have changed the display method of the error bars. Now they are all shown in the graph. Please refer to the document for details.

Comment 2: Please indicate the statistical software used to perform the calculations in subsection 2.12.

Response 2: We have added the software information to Section 2.12, please refer to the manuscript for details.

Comment 3: Please reorganize the text so that the references to the figures are before the figures.

Response 3: We have re-edited the text and moved the textual description to before the cited chart.

Comment 4: Subsection "2.2. Necrosis, not autophagy, mediated PP-NP-induced decrease in viability" should have the number 3.2.

Response 4: Thank you for your reminder. We have corrected this mistake.

Comment 5: Some figures are of insufficient quality. These are the diagrams in Figures 4, 5, 6. I would recommend making the size of the panels larger, and this will improve the quality of the figures.

Response 5: We have increased the size of the corresponding images by 30% as per the requirements, thereby improving the quality of the images. Please refer to the manuscript for details.

Reviewer 3 Report

Comments and Suggestions for Authors

Please refer to the uploaded peer review report file for a complete breakdown of the manuscript revision assessment.

Comments for author File: Comments.pdf

Comments on the Quality of English Language

The authors are invited to submit their manuscript for the correct use of the English language not only in terms of form but also employed style.

Author Response

Comment 1: As for the front matter, despite the abstract appears correctly focused (although it surely needs adjustments upon the completion of all amendments required for publication), the title does not appear really informative about the actual findings presented in the text. In addition, chosen keywords could be changed/improved to guarantee a correct article dissemination.

Response 1: We have added ‘similar in size to nanoplastics’ to the primary title, which reflects the actual findings. We have changed the ‘Tissue damage’ to ‘Cell damage’, which may guarantee a correct article dissemination.

Comment 2: Regarding the introduction section, despite not framing MNPs as endocrine disruptors, an improvement in terms of writing style (both in form and structure, more scientific article-oriented) is certainly required. In addition, while presenting MNPs carcinogenic properties, it must be noted that they may act as contributing factor rather than the reason behind colorectal cancer development (lines 73-74). Finally, regarding the content presented in lines 69-98, I strongly suggest the authors to switch from text to a summarizing table, which is more reader-friendly and less dispersive.

Response 2: We have added the fact that "micro-nano plastics carry endocrine-disrupting substances and the related interference mechanisms" into the section of introduction.

Comment 3:  As for the materials and methods section, the authors are invited to properly reference each method where possible, particularly for the primers employed. In this regard, the authors are invited to use a different housekeeping gene (e.g. beta-actin, rpl6, 18S), since GAPDH in context of inflammation and altered energetic state (as observed after cell viability, caspase-3 and Bcl-2 levels) may not be the best option for normalization. Moreover, in addition to moving Fig. 2 to the Results section, it is not clear if NPs size is the same in all experiments. If not, it must be clarified each time. 

Response 3: We have newly synthesized the master gene and performed a study on the transcriptional levels of related factors after NPs stimulation.

Comment 4: Regarding the results section, multiple issues arise: a. As for the apoptosis investigation (Fig. 3), why the employed cells display such elevated levels of early apoptosis (i.e. Q4 quadrant) even in the controls (panel A)?

Response 4：This might be due to the higher generation number of HUVECs in the later generations, but this does not affect the final result of cell necrosis caused by the nanoplastics.

Comment 5: 

Moreover, the authors suggest that NPs induce necrosis. However, necrotic cells are identified in Q1 quadrant (PI positive, Ann. V negative), while the treatment with NPs appears to induce an increase in cells positive to both (PI and annexin V) staining (e.g. presence in Q2 quadrant), indicating either late apoptosis or necroptosis. Can the authors evaluate cell death pathway in other ways (e.g. Bcl-2/BAX ratio via immunoblot, use of specific inhibitors like Z-VAD or NEC-1)? Also, if this is the case of a late apoptosis, shorter exposure times (e.g. 24h) may be more suitable. Finally, besides better clarifying treatments in Fig 3 for each panel, the authors are invited to include gating strategy and unstained cells in the supplementary information.

Response 5: Thank you for your reminder. However, since our laboratory does not have the necessary conditions to conduct experiments such as immunoblotting, it is difficult for us to purchase the required reagents and conduct the experiments within the given time frame. We sincerely hope for your understanding. In future research, I will definitely follow your advice and make the research more standardized.

Comment 6: In all figures, can the authors better specify how significance was evaluated? Sometimes changes deemed significant appear minimal. Moreover, a general improvement for image quality is necessary.

Response 6: Firstly, I believe that in the article, the main charts used to support the main idea or conclusion should be presented in the main body, while the secondary ones should be placed in the supplementary materials. Secondly, for the experimental results charts that show significant differences from the control group, I will provide detailed or focused descriptions, and for those without changes, I will give brief descriptions. Finally, I am not sure what you mean by "the changes that are considered significant seem negligible", but I respect the facts. Sometimes, theoretically, it may be thought that the experimental group results could show a significant difference from the control group, but contrary to expectations, the actual results will be presented in the charts. The quality of the charts has been improved. Please refer to the manuscript for details.

Comment 7: In line 318, the authors stated that wound healing scratch assays were performed to investigate NPs ability to affect angiogenesis. However, this kind of in vitro assay cannot be employed to investigate such effects, for which cell tube formation assays and VEGF protein levels are more correct means of investigation.

Response 7: To avoid any disputes, we have accurately described it as ‘tube-forming capacity’ in the section 3.4. This is because the injury tissue healing and Transwell® experiments have confirmed the migration ability of umbilical vein endothelial cells, and the migration ability is the basis of angiogenesis. Therefore, it can indirectly reflect the impact on angiogenesis.

Comment 8: Regarding inflammation investigation reported in Fig. 8, since the actual players are represented by proteins, immunoblot evaluation of the investigated targets (NLRP3, BAX, Bcl-2, p53, caspase-3 and ZO-1) must be performed also to corroborate actual apoptosis involvement in NPs mechanism of action.

Response 8: Thank you for your suggestion. Proteins are indeed actual participants in inflammatory and apoptotic responses, if such results do exist, they will indeed add more credibility to the argument. The level of proteins is determined by mRNA, so the level of mRNA can to some extent reflect the level of the corresponding proteins. Due to the limited short time frame, it is impossible to purchase the corresponding antibodies for WB determination. we hope you can understand.

Comment 9:  The authors attempt to mimic realistic exposure by estimating PP-NP concentrations based on cumulative infusion volumes. However, the rationale for using up to 1050 µg/mL (far exceeding expected human exposure levels) requires stronger justification. Can the authors elaborate further on how this maximum concentration relates to worst-case human exposure scenarios? Are these physiologically relevant or only intended for establishing potential cytotoxic thresholds? 

Response 9: Due to the average annual fluid infusion volume per person reaches 10.9 bottles, and the measured concentration is 23 µg/L, based on common volumes of 100, 250, and 500 mL, it can be calculated that approximately 71 µg of nano-plastics enter the body each year through infusion therapy for treating diseases. If the excretion amount is not considered, it will take approximately 14.8 years for the total amount to accumulate to 1050 µg in the body. On the other hand, the currently measured concentration of nano-plastics in the blood is 1.6 µg/mL (10.1016/j.envint.2022.107199), but in the future, the concentration is certain to increase like the accumulated nano-plastic content in the brain (10.1038/s41591-024-03453-1). Therefore, the current research has certain sustainable value.

Comment 10: The manuscript lacks detailed physicochemical characterization of the PP-NPs used. The authors are invited to include dynamic light scattering (DLS) and polydispersity index data– in addition to zeta potential data reported in Table S1 – since they are crucial to confirm size distribution, stability, and potential aggregation in the exposure medium.

Response 10: Thank you for your suggestion. I have added the particle size distribution data obtained from the DLS measurement. Please refer to Supplementary Figure 3 for details. Due to the instrument malfunction after two measurements and the inability to complete the third measurement within the specified response time, please understand.

Comment 11: While the use of 0.01% Tween 80 as dispersant is common, can the authors provide control data to ensure that this concentration is indeed biologically inert in their system? A vehicle control with Tween 80 alone should be explicitly presented in all relevant figures and statistical analyses.

Response 11: “Yes, the negative control results of all the research projects were obtained by measuring the cells in a culture medium containing 0.01% Tween 80”. We have added the description to the Section 2.2.

Comment 12: Generally, there is an inadequate investigation of NPs mechanisms. Although the study shows an increase in oxidative stress, inflammation, and apoptosis, the manuscript falls short of integrating these findings into mechanistic pathways. Was mitochondrial dysfunction assessed? Did the authors investigate nuclear translocation of NF-κB or other inflammatory signaling components? Could NPs surface reactivity or adsorbed biomolecules (protein corona) have played a role? Also, autophagy involvement is underdeveloped. The manuscript briefly mentions that PP-NPs did not induce autophagy based on LC3 staining (Figures S1, S2), but this is not thoroughly explored. In this regard, the authors are invited to provide an additional marker such as p62 to support this claim along with clearer figure legends and quantification.

Response 12: This study did not conduct research on mitochondrial dysfunction. Although qRT-PCR was used to measure NF-κB, stable results were not obtained. It is currently unclear whether the surface reactivity of the nanoparticles or the adsorbed biomolecules (protein corona) played a role. The autophagy results have been described clearly in the text. Since only punctate fluorescence was detected at the maximum concentration of 35 mg/mL, it was described as almost not causing autophagy. Due to the time limit for returning for manuscript is short, while the purchase cycle of reagents is long, it is impossible to complete the detection of other markers. Please understand. Thank you.

Comment 13: The authors speculate about increased cardiovascular risk or atherosclerosis based on in vitro effects on HUVECs. This is a considerable extrapolation. While the findings are suggestive, the conclusions should be more cautious and clearly limited to in vitro relevance.

Response 13: Yes, what you said makes sense. The results of the in vitro experiments cannot prove the pathological effects in the body, but they can indirectly reflect the possible outcomes, that is, the decrease in ZO-1 expression will affect the tight junctions between cells (10.1111/nyas.14798), and this may lead to tissue-level damage. Moreover, vascular barrier damage is related to atherosclerosis (10.1007/s12012-013-9208-0). This also follows the principle of "drawing conclusions with caution". Therefore, in the abstract and conclusion sections, it is not stated that NPs will increase vascular risk or cause atherosclerosis.

Comment 14: As for the discussion section, I believe that it would benefit from a brief but focused consideration of the potential endocrine-disrupting activity of PP-derived nanoplastics. Polypropylene is often overlooked as an EDC source, yet its degradation products and additives may interfere with hormone-regulated pathways. Moreover, your findings on ZO-1 reduction and inflammation intersect with pathways previously linked to endocrine disruption in epithelial barriers and immune responses. The observed effects on inflammation, apoptosis, and tight junction disruption — notably ZO-1 downregulation — may intersect with endocrine-related signaling axes. For instance, recent studies have shown that RACK1, a key scaffold protein implicated in immuneendocrine signaling, also plays a critical role in regulating endothelial junction proteins such as ZO- 1 and VE-cadherin (e.g. 10.1186/1478-811X-11-2). Furthermore, prior studies have shown that multiple EDCs can modulate RACK1 in immune and epithelial systems (e.g. 10.1007/s00204-020- 02756-9; 10.3389/fphar.2021.743991; 10.1016/j.etap.2022.103971; 10.1016/j.tox.2022.153321), and that inflammatory stimuli or GILZ deficiency can reduce ZO-1 expression via the GILZ/cRel/RACK1 pathway (e.g. 10.1093/ecco-jcc/jjae191). In this regard, the significant structural and functional similarities between the intestinal epithelial barrier and the vascular endothelial barrier (both barriers rely on ZO-1, are disrupted by similar inflammatory triggers, and engage overlapping signaling pathways to regulate junctional integrity.) strongly suggest that the GILZ/cRel/RACK1 axis plays a comparable regulatory role in both systems. Therefore, an integration to the discussion section implementing and connecting these mechanisms could enrich the manuscript's broader toxicological implications and open mechanistic hypotheses for future in vivo work. 

Response 14: We have added this part into the 9_th paragraph of the discussion section.

Minor Comments

Comment 15：The manuscript would benefit from careful language editing to correct grammar, avoid redundancy, and improve clarity and the correct use of acronyms/abbreviations (e.g., “NPs,” “PP-NPs,” “HUVECs”) .

Response 15: Based on the previous editing by Elsevier, and after being checked by the grammar software, the grammatical errors have been corrected.

Comment 16: Figures 2–8 should include clearer scale bars, consistent labeling (e.g., “µg/mL”), and full legends. The authors must ensure that statistical significance is consistently marked and defined in each figure.

Response 16: We have finished the revisions, ensuring the consistency of all legends, marks and statistical significance. Please refer to the manuscript for details.

Comment 17:  For Figure S3 (Endotoxin Testing), please reference this explicitly in the main text when ruling out endotoxin contamination as a cause of inflammation.

Response 17: We have already cited to and described supplementary figure 3 in the discussion section of the manuscript, as indicated in paragraph 8 of discussion section.

Comment 18: The authors should consider expanding the discussion comparing the toxicity of PP-NPs with other commonly encountered nanoplastics such as PS and PET. This would help contextualize the novelty and risk relevance of PP. 

Response 18: The comparisons of the toxicity of PP-NPs with other common types of nanoplastics (such as PS and PET) was presented in the 6th, 7th, 8th, 9th, 10th, 11th and 13th paragraphs of the discussion section.

 

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The study of Jie Wang, Zhong-Lan Chen, Cheng-Gang Liang, Hui-Ying Yang, Xian-Fu Wu and Hui-Min Sun, named “Toxicological impacts of polypropylene nanoparticles in plastic-bottled injections on human umbilical vein endothelial cells” has been improved. All comments were answered by authors. I believe that the work can be published in its present form.

Suggestions for the future:

Escherichia coli and other species should be italic. Please, check carefully

The proportions of living, early apoptotic, late apoptotic and necrotic cells can be assessed using previously obtained experimental data if double staining with Annexin-V + PI is present. Please see examples in works 10.1038/s41598-021-02697-y and 10.1016/j.bbagen.2025.130777. Perhaps this approach can be applied in new works by the authors.

Best regards

Author Response

Comment 1： “Escherichia coli and other species should be italic. Please, check carefully”

Response 1：We have italicized the species names of Escherichia coli mentioned in Section 2.1.

Comment 2: “The proportions of living, early apoptotic, late apoptotic and necrotic cells can be assessed using previously obtained experimental data if double staining with Annexin-V + PI is present. Please see examples in works 10.1038/s41598-021-02697-y and 10.1016/j.bbagen.2025.130777. Perhaps this approach can be applied in new works by the authors.”

Response 2：Thank you for your suggestion. "We have added the ‘proportion of early, late and necrotic cells at the concentration of 35 µg/mL’ that significantly increased the number of late apoptotic cells compared to the negative control in section 3.2."

Reviewer 3 Report

Comments and Suggestions for Authors

I would like to thank the authors for their time required for these revisions. However, considering the level of detail given in my peer review report and despite the language barrier that may have played a role in how the tone of their answers was perceived, I believe that the way the authors handled this peer review process raises multiple issues.

 

First of all, the authors totally and arbitrarily ignored what I deemed as "extremely major issue" (i.e. a pivotal lacking point in their dissertation, which I thought clearly asked for prompt amendments), describing NPs only as EDCs carriers and not as also EDCs themselves despite the literature data I provided that clearly highlighted this aspect (see for reference: 10.3389/fendo.2022.1084236; 10.1016/j.tiv.2024.105938; 10.3390/ijms26136156). As I specified in the previous round of revisions, this aspect is of central importance for both general and molecular mechanisms-linked toxicological aspects, paramount points of investigation of the present study. This unreferenced gap still calls for a more proper framing of NPs topic, in light of the definition of EDC (e.g. 10.3390/jox15010013), their effects in cancer context (e.g. 10.3390/ijms21239229), and the complex membrane-initiated toxicological mechanisms (e.g. 10.3390/cells10112999). As I previously underscored, due to the hormone-responsiveness nature of the vascular endothelium, direct EDC-linked effects of NPs (besides those as EDC carriers) cannot be ruled out in the interpretation of their detrimental effects on endothelial cell function through hormonal signaling axes – not just via oxidative or inflammatory pathways (which, nevertheless, crucially contribute to NPs toxicological aspects) – and, therefore, should be proper presented to correctly frame the study rationale. A comprehensive implementation of these different lines of evidence is still needed to add a further level of in-depth investigation that better routes the present work but also future studies.

 

In the methodology section, regarding the issue related to the use of GAPDH as housekeeping gene for normalization in their conditions, the authors stated that they “newly synthesized the master gene and performed a study on the transcriptional levels of related factors after NPs stimulation”. However, despite the slight change of layout, the presented graphs appear the same as the previous ones. Although this may indicate data robustness across different housekeeping normalizing genes, minimal differences and fluctuations should be at least expected. Is there a chance that the authors inadvertently embedded the previous GPADH-normalized data instead of the beta actin-normalized ones?

 

As for the concerns raised from the Results section, I would like to respectfully point out that each instance of additional experiments request (comprehensively very limited in number and specifically required to ascertain the correctness of what the authors claimed or to substantiate/rule out what the authors hypothesized/interpreted) has been refused, claiming contrasting issues with the given time, inability to purchase reagents or instrument malfunction. Although I completely understand the circumstances, if issues of this importance arise during the peer review, proper time should be given to answer and the authors are supposed to actually respond to the raised concerns, keeping in mind that the pursuit of scientific rigor and soundness must be the priority. If actual circumstances prevent the execution of specific experiments, the resulting lack of substantiation must be acknowledged in the text, although this should be the last resort. If appropriate time were granted, all instances – or part of them – of further experimental detail (i.e. NLRP3, BAX, Bcl-2, p53, caspase-3, ZO-1, LC3, p62 immunoblot; cell viability with specific inhibitors like Z-VAD or NEC-1) should be properly addressed.

 

Finally, regarding the discussion section, the authors only they briefly implemented what I suggested but without the proper and required contextualization (which was given in the peer review report to exactly help and rout reference search and literature consultation) or misreporting the outcome (i.e. lines 529-530).

 

Although there are other points of discussion on which I may disagree (e.g. wound assay to investigate angiogenesis; direct correlation mRNA levels = protein levels; HUVEC generation number and reliability of obtained apoptotic data), I recognize that it may just be a matter of point of view or different interpretation, while I strongly believe the concerns listed above still mine the scientific soundness of the study and should be properly addressed given the general quality of the present work.

Comments on the Quality of English Language

As I also stated in the peer review report, if the authors circumstances actually prevent the execution of the requested experiments (i.e. they are not able to perform such experiments in an appropriate time frame), clear study limitations must be implemented, although as a last resort.

Author Response

Comment 1: First of all, the authors totally and arbitrarily ignored what I deemed as "extremely major issue" (i.e. a pivotal lacking point in their dissertation, which I thought clearly asked for prompt amendments), describing NPs only as EDCs carriers and not as also EDCs themselves despite the literature data I provided that clearly highlighted this aspect (see for reference: 10.3389/fendo.2022.1084236; 10.1016/j.tiv.2024.105938; 10.3390/ijms26136156). As I specified in the previous round of revisions, this aspect is of central importance for both general and molecular mechanisms-linked toxicological aspects, paramount points of investigation of the present study. This unreferenced gap still calls for a more proper framing of NPs topic, in light of the definition of EDC (e.g. 10.3390/jox15010013), their effects in cancer context (e.g. 10.3390/ijms21239229), and the complex membrane-initiated toxicological mechanisms (e.g. 10.3390/cells10112999). As I previously underscored, due to the hormone-responsiveness nature of the vascular endothelium, direct EDC-linked effects of NPs (besides those as EDC carriers) cannot be ruled out in the interpretation of their detrimental effects on endothelial cell function through hormonal signaling axes – not just via oxidative or inflammatory pathways (which, nevertheless, crucially contribute to NPs toxicological aspects) – and, therefore, should be proper presented to correctly frame the study rationale. A comprehensive implementation of these different lines of evidence is still needed to add a further level of in-depth investigation that better routes the present work but also future studies.

Response 1：

We have added the descriptions below into the section of “Introduction”, as the 4_rd paragraph.

Both the MNPs themselves and the additives contained within them may cause toxicological damage to cells. Endocrine-disrupting chemicals (EDCs) are natural or synthetic substances that can interfere with hormonal systems and alter their physiological signalling (Buoso et al., 2025a). EDCs may trigger the transformation towards hormone-sensitive cancers by promoting cell proliferation and increasing the number of random genetic errors, such as prostate cancer, breast cancer, ovarian cancer, testicular germ cell cancer, etc. (Masi et al., 2021). Moreover, the signalling hub protein RACK1 (Receptor for Activated C Kinase 1), a relevant EDCs target that responds to steroid-active compounds, could be considered a molecular bridge between the endocrine-regulated tumour microenvironment and the innate immune system (Buoso et al., 2020). In the early stage, we have acknowledged that MNPs contain EDCs such as bisphenol A, BPS, 1,3,5-trimethyl-2,4,6-tris(3,5-di-tert-butyl-4-hydroxybenzyl)benzene (Nikitakos et al., 2025), BPA can directly (through glucocorticoid receptor α agonism) and indirectly (through an increased glucocorticoids release due to HPA axis hyperactivation) induce RACK1 downregulation, leading to an anxiety-like behavior and neuroinflammation (Buoso et al., 2025a), while BPS acts predominantly through androgen receptor (AR)-RACK1 pathway, minorly through G protein coupled estrogen receptor (GPER)-AR-RACK1 (65). Some studies have regarded MNPs as carriers of EDCs, which can interfere with the effects of different hormone signalling pathways and induce functional disorders of the gonads, thyroid, and adrenal glands through the HP axis [29]. NPs (＜100 nm) and plastic additives co-exposure modulate estrogen–androgen–thyroid–steroidogenesis (EATS) pathways and show to disrupt fish embryo–larval development in the F1 generation (Dasmahapatra et al., 2025). Nevertheless, the latest research indicates that MNPs themselves are also regarded as EDCs, and they make harmful effects on the human reproductive systems (Zhang et al., 2025). When PS-NPs overload the lysosomes of human placental primary trophoblast cells, they induce autophagy and activate the Nrf2/HO-1 antioxidant pathway, ultimately leading to endocrine disruption through a decrease in ß-hCG levels in the extracellular compartment (Poinsignon et al., 2025). PS-NPs can increase the expression of the SOD1 gene and decrease the level of estrogen triol in H295R cells (Boxel et al., 2024). PS-MPs can reduce the testosterone level in mice through Glutathione peroxidase 1 (GPX1)-PERK-eukaryotic translation initiation factor 2α‌ (EIF2ɑ)-Activating Transcription Factor 4 (ATF4)-C/EBP homology protein (CHOP)-SRD5A2 signalling pathways, and also disrupt the testosterone balance through the HPG axis (Qu et al., 2024). PS-MPs can induce a significant increase in luteinizing hormone, simultaneously causing a significant decrease in estradiol and follicle-stimulating hormone levels. The hormonal imbalance eventually leads to polycystic ovary syndrome and ovarian fibrosis (Adhikari et al., 2024).

Comment 2: In the methodology section, regarding the issue related to the use of GAPDH as housekeeping gene for normalization in their conditions, the authors stated that they “newly synthesized the master gene and performed a study on the transcriptional levels of related factors after NPs stimulation”. However, despite the slight change of layout, the presented graphs appear the same as the previous ones. Although this may indicate data robustness across different housekeeping normalizing genes, minimal differences and fluctuations should be at least expected. Is there a chance that the authors inadvertently embedded the previous GPADH-normalized data instead of the beta actin-normalized ones?

Response 2：We’re very sorry, our previous reply was submitted in a hurry, and I forgot to replace the figures. The figures in the manuscript are still those that measured the gene transcription data of inflammatory, apoptotic and adhesion factors using GAPDH as the internal reference. I have attached the figure showing the corresponding gene expression levels measured with β-actin as the internal control for your reference. The overall data of the two are quite similar.

We have added “The data normalized against the levels of GAPDH mRNA was similar to β-actin (Figure S6).” in the section of 3.6.

Comment 3: As for the concerns raised from the Results section, I would like to respectfully point out that each instance of additional experiments request (comprehensively very limited in number and specifically required to ascertain the correctness of what the authors claimed or to substantiate/rule out what the authors hypothesized/interpreted) has been refused, claiming contrasting issues with the given time, inability to purchase reagents or instrument malfunction. Although I completely understand the circumstances, if issues of this importance arise during the peer review, proper time should be given to answer and the authors are supposed to actually respond to the raised concerns, keeping in mind that the pursuit of scientific rigor and soundness must be the priority. If actual circumstances prevent the execution of specific experiments, the resulting lack of substantiation must be acknowledged in the text, although this should be the last resort. If appropriate time were granted, all instances – or part of them – of further experimental detail (i.e. NLRP3, BAX, Bcl-2, p53, caspase-3, ZO-1, LC3, p62 immunoblot; cell viability with specific inhibitors like Z-VAD or NEC-1) should be properly addressed.

Response 3: Thank you very much for your suggestions. We do indeed attach great importance to the scientific rigor and reliability. However, the actual situation is that the purchase cycles of reagents such as NLRP3, Bax, and Z-VAD are quite long, and thus it is impossible to complete the related research, whereas I will add the limitations to the "Conclusion". The added content is as follows:

“Based solely on the changes in mRNA levels of NLRP3, p53 and ZO-1, we preliminarily confirmed that PP-NPs induced inflammation, apoptosis and disruption of the barrier function in human umbilical vein endothelial cells. In the future, WB experiments can be conducted to further rigorously verify the above-mentioned toxicological effects.”

Comment 4: Finally, regarding the discussion section, the authors only they briefly implemented what I suggested but without the proper and required contextualization (which was given in the peer review report to exactly help and rout reference search and literature consultation) or misreporting the outcome (i.e. lines 529-530).

Response 4: We have re-edited and added the following content to the discussion.

“It is known that glucocorticoids (GCs) can inhibit the proliferation, migration and tube formation of human umbilical vein endothelial cells (Shan et al., 2023). Estrogen promotes the proliferation of HUVECs and induces autophagy by inhibiting the Phosphoinositide 3-kinase (PI3K)-RAC-alpha serine/threonine-protein kinase (AKT)-mammalian target of rapamycin (MTOR)-LC3 signalling pathway (Yu et al., 2025). Stress signals can induce apoptosis, oxidative stress and inflammatory responses in HUVECs cells (Wu et al., 2025). Just like how PS-NPs activate the ROS-driven NF-κB/NLRP3 pathway, thereby inducing the barrier defect in NCM460 cells (He et al. 2022), the main reason was that the increase of TNF-α damaged the cell membrane of HUVECs, causing the release of LDH, and ultimately leading to the decrease of ZO-1 in this study. However, the decrease in ZO-1 may also be related to the hormone pathways induced by EDCs. Recent studies have shown that RACK1, a key scaffold protein implicated in immune endocrine signalling, also plays a critical role in regulating endothelial junction proteins such as ZO-1 [63] and inflammasomes such as NLRP3 [64]. Furthermore, prior studies have shown that multiple additive-type EDCs can modulate RACK1 in epithelial systems [65]. Due to the hydrophobic nature of PP itself - although it is generally believed that its toxicity is lower than that of PVC or PS, its degradation products and potential additives (such as plasticizers, antioxidants, and catalysts) may have hormonal effects, especially at the nanoscale. Therefore, the possible another reason is that the EDCs contained in PP-NPs may interfere with the normal hormone regulation, by increasing the inflammatory response, specifically the increase of NLRP3, to downregulate the expression of ZO-1, which is similar to the situation where glucocorticoids induce the downregulation of ZO-1 through RACK1/SRC/E-cadherin, resulting in intestinal damage [Buoso et al., 2025b, 64]. In summary, at the cellular level, the toxicological damage caused by PP-NPs to HUVECs is mainly characterized by particle-induced oxidative stress and inflammatory responses, with the hormone effects induced by EDCs acting as a secondary component. This is because the latter is more likely to disrupt the balance of glucocorticoids and other substances by interfering with the HPA axis in the body.”