Review Reports

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The manuscript submitted under ID applsci-4165344, entitled “Efficient Adsorptive Removal of Methyl Orange from Aqueous Solution Using a Cu2O/CuO Nanocomposite,” reports on the synthesis, characterization, and application of a Cu2O/CuO nanocomposite for the adsorption of methyl orange from aqueous solutions. The topic falls within the scope of Applied Sciences and addresses an environmentally relevant problem. However, several major issues must be addressed before the manuscript can be considered for publication.

# Comments

01 - The similarity index is relatively high, particularly in relation to the articles 10.3390/ijms22083882 and 10.3390/app152413271. The authors should revise the manuscript to reduce textual and conceptual overlap.

02 - The novelty of the manuscript is not sufficiently emphasized in the Introduction. The authors are encouraged to clearly state the main original contributions and explain how their work advances the existing literature.

03 - In the Abstract, the authors state that “there is a need to develop effective and low-cost adsorbents,” but it is not clear whether the proposed Cu2O/CuO nanocomposite can indeed be considered a low-cost material. Please justify this claim with appropriate cost analysis or discussion.

04 - The analysis of the effect of the initial methyl orange concentration on adsorption capacity and percentage removal (Section 3.2.1) is incomplete due to insufficient experimental data. The authors investigated only a narrow concentration range, within which both the removal efficiency and adsorption capacity increase with increasing initial concentration, with the adsorption capacity showing an almost linear trend. This suggests that adsorption saturation was not approached under the tested conditions. A wider concentration range should be explored, or the limitation should be properly justified and discussed.

05 - Figure 8 appears to use a non-linear x-axis scale, but this is not indicated or discussed in the manuscript. The authors should clarify and, if applicable, justify this choice.

06 - The presentation of percentage removal together with adsorption capacity in Figure 11 is almost redundant, since the initial adsorbent mass and initial adsorbate concentration are the same for all experiments. Under these conditions, both metrics convey essentially the same information.

07 - The use of linearized forms to fit adsorption kinetic and equilibrium models is not recommended, particularly for a journal of this quality, as linearization can introduce significant bias and lead to inaccurate parameter estimation. Non-linear regression should be preferred for model fitting. The only exception is the Weber-Morris intraparticle diffusion model, which is commonly analyzed in linearized form; however, in this case, the authors did not adequately explore or discuss the two distinct adsorption regimes observed in Figure 12d. 

08 - The units for the x-axis in Figure 12a are missing. Please include them for clarity. 

09 - Based on Figure 12a, it appears that adsorption equilibrium was not fully reached within 180 minutes, which may affect the reliability of the kinetic model fitting. Moreover, several experiments reported in Section 3.2 used 180 minutes as the contact time, which could compromise the validity of the reported adsorption capacities.

10 - The use of linearized fitting has produced non-physical and inconsistent parameter estimates, as demonstrated by the substantial differences between the pseudo-first-order and pseudo-second-order kinetic parameters and the negative maximum adsorption capacity obtained from the Langmuir model, whose purpose is to estimate a physically meaningful maximum adsorption capacity.

# Conclusion

The authors are encouraged to carefully address all the comments above, especially the major concerns, and submit a substantially revised version that meets the publication standards of Applied Sciences (ISSN 2076-3417) .

Author Response

Comments 1: “The similarity index is relatively high, particularly in relation to the articles 10.3390/ijms22083882 and 10.3390/app152413271. The authors should revise the manuscript to reduce textual and conceptual overlap.”

Response 1: We have searched the mentioned articles and realized that the article 10.3390/ijms22083882 corresponds to a marine biology study focused on the transcriptomic analysis of wild and farmed sea cucumbers (Isostichopus badionotus). Similarly, article 10.3390/app152413271 addresses the simulation and design of an agricultural machine intended for the harvesting of seaweed.

 

Comments 2: “The novelty of the manuscript is not sufficiently emphasized in the Introduction. The authors are encouraged to clearly state the main original contributions and explain how their work advances the existing literature.”

Response 2: We thank the reviewer for their suggestion. We have revised the last paragraph of the introduction section to state the contribution. Manuscript lines 75 to 81.

 

Comments 3: “In the Abstract, the authors state that “there is a need to develop effective and low-cost adsorbents,” but it is not clear whether the proposed Cu2O/CuO nanocomposite can indeed be considered a low-cost material. Please justify this claim with appropriate cost analysis or discussion.”

Response 3: We appreciate the reviewer pointing this out. We considered our nanocomposite to be low-cost based on the facile synthesis method using relatively easy to find and inexpensive reagents. To ensure our claims do not exceed the data provided, we have agreed to remove the word “low-cost” from the manuscript, as we believe that a cost analysis is out of the scope of the present paper.

 

Comments 4: “The analysis of the effect of the initial methyl orange concentration on adsorption capacity and percentage removal (Section 3.2.1) is incomplete due to insufficient experimental data. The authors investigated only a narrow concentration range, within which both the removal efficiency and adsorption capacity increase with increasing initial concentration, with the adsorption capacity showing an almost linear trend. This suggests that adsorption saturation was not approached under the tested conditions. A wider concentration range should be explored, or the limitation should be properly justified and discussed.”

Response 4: We thank the reviewer for their comment. We have conducted new batch adsorption experiments to address this limitation. The initial methyl orange concentration range has been expanded to 10-100 mg L^-1 and the dose of the nanocomposite has been reduced to 0.2 mg mL^-1 to guarantee saturation. We have completely rewritten Section 3.2.1 (manuscript lines 244 to 269) and updated Figure 8 (previously numbered Figure 7) in the revised manuscript to include this wider concentration range and to explicitly discuss the saturation limits.

 

Comments 5: “Figure 8 appears to use a non-linear x-axis scale, but this is not indicated or discussed in the manuscript. The authors should clarify and, if applicable, justify this choice.”

Response 5: Figure 8 used a linear x-axis scale. We understand that it may have appeared otherwise because of formatting. To resolve the issue, the figure now depicts a clear linear scale for the x-axis to avoid confusion. 

 

Comments 6: “The presentation of percentage removal together with adsorption capacity in Figure 11 is almost redundant, since the initial adsorbent mass and initial adsorbate concentration are the same for all experiments. Under these conditions, both metrics convey essentially the same information.”

Response 6: We agree that both metrics conveyed redundant information in the figure. The removal percentage of MO axis has now been removed from the figure to better present our results. Figure 11 has also been renumbered to Figure 12 and the caption renamed. It now reads:

“Figure 12. Effect of contact time on the adsorption capacity (q_e) using the Cu₂O/CuO nanocomposite.”

 

Comments 7: “The use of linearized forms to fit adsorption kinetic and equilibrium models is not recommended, particularly for a journal of this quality, as linearization can introduce significant bias and lead to inaccurate parameter estimation. Non-linear regression should be preferred for model fitting. The only exception is the Weber-Morris intraparticle diffusion model, which is commonly analyzed in linearized form; however, in this case, the authors did not adequately explore or discuss the two distinct adsorption regimes observed in Figure 12d.”

Response 7: We thank the reviewer for pointing this out. We have completely recalculated our kinetic (PFO, PSO) and equilibrium models (Langmuir, Freundlich and Langmuir-Freundlich) models using non-linear forms. Table 1 and Table 3 present now the revised parameters. As for the Weber-Morris intraparticle diffusion model, we increased the number of samples taken in the initial stage of the process and we have identified three distinct linear adsorption stages. Figure 13b (previously numbered Figure 12d) presents the Weber-Morris plot along with its relevant data in Table 2. We have substantially revised Section 3.3 (Adsorption Kinetics) to detail our new findings.

 

Comments 8: “The units for the x-axis in Figure 12a are missing. Please include them for clarity.”

Response 8: The units for the x-axis have been added to the figure.

 

Comments 9: “Based on Figure 12a, it appears that adsorption equilibrium was not fully reached within 180 minutes, which may affect the reliability of the kinetic model fitting. Moreover, several experiments reported in Section 3.2 used 180 minutes as the contact time, which could compromise the validity of the reported adsorption capacities.”

Response 9: We understand the concern of the reviewer. The contact time was confirmed based on experimentation in section 3.2.4. Effect of contact time, where we performed batch experiments in the range of 0 to 300 minutes, and we concluded from the adsorption capacity results that after 180 minutes of contact time no significant changes took place. 

 

Comments 10: “The use of linearized fitting has produced non-physical and inconsistent parameter estimates, as demonstrated by the substantial differences between the pseudo-first-order and pseudo-second-order kinetic parameters and the negative maximum adsorption capacity obtained from the Langmuir model, whose purpose is to estimate a physically meaningful maximum adsorption capacity.”

Response 10: We agree that the previous linearized fitting introduced mathematical distortions, such as the non-physical negative maximum adsorption capacity. To resolve this, we recalculated all kinetic and isotherm parameters using non-linear fitting. The Langmuir model now yields a positive maximum capacity of 409.661 mg g⁻¹. Furthermore, the Langmuir-Freundlich model, which provided the best fit (R² = 0.9922), predicts a maximum capacity of 254.759 mg g⁻¹. This closely matches our experimental maximum of 249.48 mg g⁻¹. The calculated capacities for both the pseudo first order (34.62 mg g⁻¹) and pseudo second order (36.48 mg g⁻¹) models are now highly consistent with the experimental value of 36.71 mg g⁻¹.

We have updated Tables 1 and 3 and corrected Sections 3.3 and 3.4.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

Comments on the manuscript entitled “Efficient adsorptive removal of methyl orange from aqueous solution using a Cu2O/CuO nanocomposite” authored by Yordani Arce-Argote et al. (applsci-4165344).

(1) Introduction section. What is the benefit of these processes in comparison with other systems? The authors should put some effort in discussing in the introductory part other relevant studies performed with other types of systems in order to highlight the innovative aspects (e.g cost, efficiency) compared to other processes. In other words, the authors should comment on the costs and the scaling of the adsorption process for this type of contaminant or wastewater in the introduction.

(2) Author should clarify why these experimental conditions were selected and if the selection was based on the real application, for example, in the effect of operational parameters on Qre.

(3) The number of data points and repetitions (with error bars) must be increased to achieve a reliable model. In addition it is necessary to identify whether the error is significant or not the error bars in the graphs.

(4) The adsorption-desorption isotherm at 77K for the material must be provided. The surface area value is missing. Authors should relate these values to those obtained for adsorption process.

(5) Adsorbent reusability experiments should be done.

(6) The adsorption kinetics should be compared with others reported in literature.

(7) Conclusions should present more clearly not only the new findings as done in the previous sections but rather focus on the new insight came out of this work.

Other remarks:

(8) I recommend a full revision of the language in order to avoid further editorial work.

This paper needs a major revision and suggestions should be addressed in a revised manuscript before it can be reconsidered for publication.

Author Response

Comments 1: “Introduction section. What is the benefit of these processes in comparison with other systems? The authors should put some effort in discussing in the introductory part other relevant studies performed with other types of systems in order to highlight the innovative aspects (e.g cost, efficiency) compared to other processes. In other words, the authors should comment on the costs and the scaling of the adsorption process for this type of contaminant or wastewater in the introduction.”

Response 1: We thank the reviewer for their comment. We have expanded the Introduction section of the revised manuscript to include a critical comparison of current wastewater treatment systems. We now explicitly discuss the limitations of biological degradation, membrane filtration, and advanced oxidation processes (AOPs), particularly regarding their high operational costs, energy demands, and scaling challenges. Furthermore, we have highlighted why adsorption remains one as one viable and scalable process for treating dye-contaminated effluents, particularly when paired with highly efficient, easily synthesizable nanomaterials that minimize dosage requirements. The new paragraph is shown in manuscript lines 43 to 51.

Comments 2: “Author should clarify why these experimental conditions were selected and if the selection was based on the real application, for example, in the effect of operational parameters on Qre.”

Response 2: We appreciate the reviewer’s comment. While the selected parameters were not chosen to simulate one specific real-world industrial effluent, they were established after consecutive experimentation. For example, the working pH and contact time were tested over a range, and the optimum values were chosen to achieve the highest removal efficiency in less time. Furthermore, the initial MO concentration range was expanded from 25 mg L⁻¹ up to 100 mg L⁻¹ specifically to address comment #4 of reviewer 1 requesting to widen the concentration range to confirm adsorption saturation. Consequently, a lower adsorbent dosage of 0.2 mg mL⁻¹ was utilized to guarantee the system would saturate. Only then was it possible to determine the optimized adsorbent dosage of 1 mg mL^-1 for the conditions studied in this work. We have clarified this in the last paragraph of the Introduction section (manuscript lines 78 to 81).

 

Comments 3: “The number of data points and repetitions (with error bars) must be increased to achieve a reliable model. In addition it is necessary to identify whether the error is significant or not the error bars in the graphs.”

Response 3: The kinetic and adsorption experiments were now performed in triplicate after major revision of the manuscript, and we confirmed that the error was below 3% indicating that the data is reproducible. We now have added error bars to key figures used for the kinetic and isotherm modeling (Figure 13 and Figure 14). We also have included a statement in the Materials and Methods section (Section 2.4) mentioning the use of triplicate measurements. The added sentece is shown in manuscript lines 135-136.

 

Comments 4: “The adsorption-desorption isotherm at 77K for the material must be provided. The surface area value is missing. Authors should relate these values to those obtained for adsorption process.”

Response 4: We thank the reviewer for this comment. We realized the surface area value was missing and we have added a new subsection for its characterization. The analysis is provided in the new subsection “3.1.3. Surface and pore analysis”. The analysis revealed a Type IV isotherm with a hysteresis loop and the specific surface area, calculated via the BET method, was determined to be 19.54 m² g^-1 with a total pore volume of 0.103 cm³ g^-1 . The added section is shown in the manuscript lines 200 to 208.

 

Comments 5: “Adsorbent reusability experiments should be done.”

Response 5: We appreciate the reviewer’s comment. The aim of this study was to prove the efficiency of the Cu₂O/CuO nanocomposite. While we completely agree that stability of the adsorbent over multiple cycles is vital, we believe that our nanocomposite would require a thorough evaluation of the structural integrity and phase composition before and after regeneration as well as long-term cyclic testing, which could be presented in a separate publication given that more time will be required to perform these evaluations as well as a budget increase.

 

Comments 6: “The adsorption kinetics should be compared with others reported in literature.”

Response 6: We thank the reviewer for the comment. We have updated table 4 “Kinetic and adsorption parameters of different adsorbents for MO.”, where we provide a comparison between our nanocomposite and other adsorbents in the literature.

Comments 7: “Conclusions should present more clearly not only the new findings as done in the previous sections but rather focus on the new insight came out of this work.”

Response 7: The revised conclusion section now highlights the synergistic dual-action mechanism (simultaneous adsorption and partial degradation) revealed by our comparative TOC analysis. We have also replaced broad generalizations with grounded, data-driven suggestions for future research, specifically regarding the optimization of mineralization pathways for the detected colorless intermediates.

 

Comments 8: “I recommend a full revision of the language in order to avoid further editorial work. This paper needs a major revision and suggestions should be addressed in a revised manuscript before it can be reconsidered for publication.”

Response 8: We thank the reviewer for the recommendations. We have carefully proofread the manuscript and edited the text to improve grammar and syntax as well as revising several sections to include the reviewer’s suggestions and corrections.

Author Response File: Author Response.pdf

Reviewer 3 Report

Comments and Suggestions for Authors

The manuscript contains numerous methodological shortcomings. In my opinion, the work requires substantial revision, which will necessitate significant changes throughout the manuscript. Specific comments are as follows:

• In the Introduction, Figure 1 presents pH values obtained from experimental work. It is unclear why these values appear in the Introduction section and why they are specifically attributed to the Cu2O/CuO composite. Would this process not occur in other systems at different pH values? The figure overly narrows the general concept of electrostatic attraction.
• The manuscript discusses "removal efficiency," yet nowhere is it demonstrated that the pollutant is actually removed. It is highly probable that the dye undergoes reductive transformations and converts into a transparent form that is not detectable by the optical methods employed. Consequently, this represents not the removal of the contaminant (even if model), but merely its conversion into another form. I believe the title and description of the work do not adequately reflect what is actually being investigated.
• What is the state of the composite before and after sorption? To confirm sorption, it is necessary to provide, for example, IR surface analysis or demonstrate by other means that methyl orange has indeed adsorbed onto the surface. This could be accomplished using XPS, for instance, by detecting the appearance of corresponding elemental states on fractions of the Cu2O/CuO composite separated from the suspension.
• "The absence of new absorption peaks suggests that the predominant mechanism is the effective adsorption of dye molecules onto the surface of the mixed copper oxide, rather than their transformation into intermediate by-products detectable within this range." Indeed, the forming intermediates may not absorb in the examined range. To properly confirm adsorption of the substance, it is necessary to conduct TOC (or COD) analysis of the solution to demonstrate the decrease of this parameter due to removal of the compound from the solution. Without such confirmation (or an equally demonstrative alternative), claims regarding adsorption are meaningless.
• "These results indicate that a concentration of 25 mg L^-1 favors the highest performance under the conditions studied." This is the highest value examined and represents the boundary of the investigated range. This means that the indicated value is not truly the maximum within the examined concentration range, but is limited specifically by the scope of the investigation and cannot be cited as a genuinely characteristic value. In this light, the section on concentration effects remains unresolved due to incomplete studies.
• "access the available active sites on the surface of the nanocomposite" - if the authors use this terminology, what constitutes an active site on the surface in this context?
• "the adsorption capacity (q_e) showed a drastic decrease from 239.20 mg g^-1 to 29.50 mg g^-1" - according to the presented data, the "removal" of the pollutant is nearly 100%, indicating that the sorbent is in deficit in this case. The obtained "adsorption capacity" data therefore do not reflect the true properties of the investigated sorbent, as the process is limited by the supply of substance to the surface rather than by the properties of the sorbing surface itself.
• "the PZC was established at 8.39" — given the stated precision of the measurements, the determined value can at best be reported as 8.4, but certainly not with precision to hundredths.
• "Cu2O/CuO system as a viable, stable" — the manuscript presents no data regarding the stability of this composite either over time or after multiple "adsorption-desorption" cycles. Such claims should therefore be considered unsubstantiated.
• There is confusion regarding the identification of copper oxide phases in Figure 3. In fact, the red color and the peak at 29 degrees correspond to Cu2O, not CuO as indicated in the figure legend. This misidentification requires correction.

Author Response

Comments 1: “In the Introduction, Figure 1 presents pH values obtained from experimental work. It is unclear why these values appear in the Introduction section and why they are specifically attributed to the Cu2O/CuO composite. Would this process not occur in other systems at different pH values? The figure overly narrows the general concept of electrostatic attraction.”

Response 1: We thank the reviewer for their comment. Indeed, Figure 1 presented pH values obtained experimentally in this work and the scheme should have been displayed in its corresponding section. After consideration, we have decided to eliminate the figure to avoid oversimplification of the process.

 

Comments 2: “The manuscript discusses "removal efficiency," yet nowhere is it demonstrated that the pollutant is actually removed. It is highly probable that the dye undergoes reductive transformations and converts into a transparent form that is not detectable by the optical methods employed. Consequently, this represents not the removal of the contaminant (even if model), but merely its conversion into another form. I believe the title and description of the work do not adequately reflect what is actually being investigated.”

Response 2: We agree that optical methods alone primarily confirm decolorization, and that transparent intermediates could be formed. As addressed in Comment #4, we have introduced Total Organic Carbon (TOC) analysis to the revised manuscript (Section 3.2.5). The new TOC data demonstrates a 54.2% reduction in actual organic carbon mass from the solution (contact time evaluated 180 minutes). This quantitatively confirms that true physical removal of the pollutant is occurring alongside its partial degradation. While we hypothesize that extending the contact time could achieve a higher organic carbon reduction (mineralization), we were constrained by limited access to the TOC analyzer for extended kinetic studies. For that reason, we relied primarily on the optical method to monitor the rapid degradation of the methyl orange azo group. We have updated the manuscript to reflect these new results.

 

Comments 3: “What is the state of the composite before and after sorption? To confirm sorption, it is necessary to provide, for example, IR surface analysis or demonstrate by other means that methyl orange has indeed adsorbed onto the surface. This could be accomplished using XPS, for instance, by detecting the appearance of corresponding elemental states on fractions of the Cu2O/CuO composite separated from the suspension.”

Response 3: We thank the reviewer for their insight. Unfortunately, we do not have access to an XPS machine. Nevertheless, we have conducted an FTIR analysis on our nanocomposite before and after treatment, and multiple new peaks were identified that can be attributed to methyl orange, which in turn could confirm MO adsorption on the nanocomposite. We have revised the manuscript and added a new section 3.1.4 FTIR Spectroscopy along with the FTIR spectra of the nanocomposite before and after adsorption of methyl orange. The added section is shown in manuscript lines 209 to 227.

 

Comments 4: "The absence of new absorption peaks suggests that the predominant mechanism is the effective adsorption of dye molecules onto the surface of the mixed copper oxide, rather than their transformation into intermediate by-products detectable within this range." Indeed, the forming intermediates may not absorb in the examined range. To properly confirm adsorption of the substance, it is necessary to conduct TOC (or COD) analysis of the solution to demonstrate the decrease of this parameter due to removal of the compound from the solution. Without such confirmation (or an equally demonstrative alternative), claims regarding adsorption are meaningless.”

Response 4: We thank the reviewer for their suggestion. We conducted Total Organic Carbon (TOC) analysis as requested. A single experiment was performed using a 40 ppm Methyl Orange (MO) solution and 1.0 mg mL^-1 of the Cu₂O/CuO nanocomposite. After 3 hours, UV-Vis spectrophotometry showed a 97.01% reduction in the primary absorption peak. However, TOC analysis of these exact samples revealed an initial carbon concentration of 23.6 mg L^-1, which decreased to 10.8 mg L^-1 after treatment which corresponds to a 54.2% reduction in total organic carbon from the solution, in the range of time the experiment was carried out. The difference in values between the UV-Vis (97.01%) and the TOC reduction (54.2%) confirms that while total elimination of the MO took place, a significant portion of the remaining dye may have remained as colorless intermediate products. Based on other studies, we believe that further increasing contact time may give these colorless products more room for mineralization and elimination. We have now added a new section 3.2.5. Total Organic Carbon (TOC) analysis, where we discuss these results.

 

Comments 5: “These results indicate that a concentration of 25 mg L favors the highest performance under the conditions studied”. This is the highest value examined and represents the boundary of the investigated range. This means that the indicated value is not truly the maximum within the examined concentration range, but is limited specifically by the scope of the investigation and cannot be cited as a genuinely characteristic value. In this light, the section on concentration effects remains unresolved due to incomplete studies.”

Response 5: We thank the reviewer for their insight. We have conducted new batch experiments over a significantly expanded initial methyl orange concentration range of 10, 20, 40, 60, 80, and 100 mg L⁻¹. To ensure we could properly observe the material's saturation point within this range, we utilized a lower adsorbent dosage of 0.2 mg mL⁻¹. We present the new results in Figure 8 to resolve the MO concentration effect. The removal efficiency initially increased from 53.2% (at 10 mg L⁻¹) to a true maximum of 70.2% at an MO concentration of 40 mg L⁻¹. As the concentration was pushed further, a gradual decline was exhibited in removal efficiency down to 52.3% at the highest tested concentration of 100 mg L⁻¹. The newfound methyl orange concentration (40 mg L^-1) was used for the next experiments.

 

Comments 6: “"access the available active sites on the surface of the nanocomposite" - if the authors use this terminology, what constitutes an active site on the surface in this context?”

Response 6: In the context of our specific nanocomposite adsorption system, the active sites which we refer to, primarily consist protonated surface hydroxyl groups (M-OH₂⁺) as discussed in section 3.2.3, since our optimized working pH (6) is below the nanocomposite’s PZC (8.4) causes surface partial hydration and protonation. These charged groups may act as active sites for the electrostatic capture of the anionic sulfonate groups of MO molecules. 

 

Comments 7: "the adsorption capacity (qe) showed a drastic decrease from 239.20 mg g to 29.50 mg g " - according to the presented data, the "removal" of the pollutant is nearly 100%, indicating that the sorbent is in deficit in this case. The obtained "adsorption capacity" data therefore do not reflect the true properties of the investigated sorbent, as the process is limited by the supply of substance to the surface rather than by the properties of the sorbing surface itself.

Response 7: We agree with the reviewer that at higher nanocomposite dosages the system becomes dye limited. In our revised manuscript, we updated this dosage experiment in section 3.2.2. While the removal efficiency now plateaus at nearly 97.0% rather than reaching near 100%, the system reaches an equilibrium where the remaining MO molecules are insufficient to saturate surplus nanocomposite. Consequently, the calculated q_e mathematically decreases because the mass of the nanocomposite increases while the amount of MO removed remains static. To determine the true characteristic capacity of the sorbing surface, we relied on the adsorption isotherm studies in section 3.4., where the adsorbent dose was kept constant and the adsorbate concentration was varied to properly saturate the surface, yielding a maximum capacity q_max = 254.759 mg g^-1 by the Langmuir-Freundlich model. The corrected paragraph is shown in manuscript lines 273 to 298.

 

Comments 8: “"the PZC was established at 8.39" — given the stated precision of the measurements, the determined value can at best be reported as 8.4, but certainly not with precision to hundredths.”

Response 8: We agree with the reviewer and the changes have been made. The PZC value now reads 8.4 and all occurrences are highlighted in the manuscript.

 

Comments 9: “"Cu2O/CuO system as a viable, stable" — the manuscript presents no data regarding the stability of this composite either over time or after multiple "adsorption-desorption" cycles. Such claims should therefore be considered unsubstantiated.”

Response 9: We have removed the word stable as we have not performed the reusability experiments for this nanocomposite. We believe that performing multiple cycles of adsorption-desorption would drastically increase the time and budget to present our results.

 

Comments 10: “There is confusion regarding the identification of copper oxide phases in Figure 3. In fact, the red color and the peak at 29 degrees correspond to Cu₂O, not CuO as indicated in the figure legend. This misidentification requires correction.”

Response 10: We have corrected the figure, and the legend phases colors now match the XRD diffractogram peaks. Figure 3 has also been renumbered to Figure 2.

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The authors have satisfactorily addressed the comments raised in the previous review by implementing the suggested revisions, conducting additional experiments, and improving the fitting procedure. I appreciate the thoroughness of their responses and believe that the manuscript has been significantly strengthened as a result. Therefore, I recommend its acceptance for publication in its current form.

Author Response

Comment: The authors have satisfactorily addressed the comments raised in the previous review by implementing the suggested revisions, conducting additional experiments, and improving the fitting procedure. I appreciate the thoroughness of their responses and believe that the manuscript has been significantly strengthened as a result. Therefore, I recommend its acceptance for publication in its current form.

Response: We sincerely thank the reviewer for their time, positive evaluation, and recommendation for acceptance. We are deeply grateful for the highly constructive comments and insightful suggestions provided during the previous review stage.

Reviewer 2 Report

Comments and Suggestions for Authors

Accept

Comments on the Quality of English Language

Accept

Author Response

Response: We sincerely thank the reviewer for their positive evaluation of our revised manuscript and for their highly valuable feedback throughout the review process. We completely agree with your observation regarding the language. In response to this comment, the entire manuscript has undergone a rigorous English editing and proofreading process.

Reviewer 3 Report

Comments and Suggestions for Authors

The authors took into account all the comments and did a lot of work to finalize the manuscript. In the current form, I see no global problems in this manuscript, so it can be recommended after minor revision.

• I would like to express my opinion regarding the scale of axis in Figures 8 and 9. If there is a second scale (on the right) in the range from 0 to the maximum value, the left scale, which does not start from 0, may be misleading. I understand that this was done to improve the dynamic range of the display, but nevertheless, it gives the impression of a much larger change in values than it actually is.
• In addition, in Figure 11, the points on the scale correspond to pH values of 6, 9, 10, and 11. Overall, everything is fine. So that I didn't even notice it when I first read it. However, given the sequence of 9, 10, 11, the proximity of 6 and 9 may also give the impression of a stronger relative change in the value than it actually is.

Author Response

Comment: The authors took into account all the comments and did a lot of work to finalize the manuscript. In the current form, I see no global problems in this manuscript, so it can be recommended after minor revision. I would like to express my opinion regarding the scale of axis in Figures 8 and 9. If there is a second scale (on the right) in the range from 0 to the maximum value, the left scale, which does not start from 0, may be misleading. I understand that this was done to improve the dynamic range of the display, but nevertheless, it gives the impression of a much larger change in values than it actually is. In addition, in Figure 11, the points on the scale correspond to pH values of 6, 9, 10, and 11. Overall, everything is fine. So that I didn't even notice it when I first read it. However, given the sequence of 9, 10, 11, the proximity of 6 and 9 may also give the impression of a stronger relative change in the value than it actually is.

Response: We sincerely thank the reviewer for their positive feedback, their recognition of our hard work during the revision process, and for recommending the manuscript. We highly appreciate your keen eye and insightful observations regarding the data visualization; we completely agree that accurate graphical representation is crucial to avoid misleading the reader.

In response to your valuable suggestions, we have made the following corrections:

• Figures 8 and 9: We have replotted both figures, adjusting the left y-axis to start from zero. This ensures that both the left and right scales are visually synchronized and accurately reflect the true magnitude of the variations.
• Figure 11: We have corrected the x-axis scale. It has been replotted using a true linear numerical scale rather than categorical spacing, ensuring that the visual distance between pH 6 and 9 is correctly proportioned relative to the sequence of 9, 10, and 11.

We believe these adjustments have greatly improved the clarity and integrity of our figures. We thank you again for your meticulous review.