Enhanced Photocatalytic and Antibacterial Performance of ZnO Nanoparticles Prepared by an Efficient Thermolysis Method

Round 1

Reviewer 1 Report

Hanif et al. have developed a thermal method to produce Zinc Oxide nanoparticles (ZnO-NPs). Authors have assessed particle crystal structure, morphology and size by XRD, FE-SEM and TEM. At the same time the manuscript explores the photocatalytic activity, of such nanoparticles, degrading methylene blue followed by UV-Visible absorbance. Finally, authors have determined the minimal inhibitory concentration for the ZnO-NPs using a Gram-negative model strain.

Authors present their results in a coherent manner showing that nanoparticles produced with their method present higher antibacterial activities (against E. coli) compared with similar nanoparticles from other published works (References 15 and 32), these results are very encouraging indeed and worth pursuing such nanoparticles to tackle infection. However authors do not study the safety of their Zinc Oxide nanoparticles (ZnO-NPs) for humans. In my opinion the article would highly improve from including (a) cytotoxic assay(s) evaluating the toxic effect on human/mammalian model cell lines.

Figure 1 display clearly the XDR patterns for the samples characterized in this experiment. However, is difficult to discern the scale between the different experiments (a, b and c) as no units are shown in the y axis.

In figure 2, authors show representative micrographs showing the ZnO-NPs morphology. Authors should mention either in the result and discussion or experimental sections the number of images taken in order to confidently determine ZnO-NPs morphology. Additionally, scale bars are difficult to see.

Similarly, authors should clearly state how many micrographs and particles were assessed in order to determine particle size in Figure 3. Particle distribution in Figure 3 (a) is difficult to see and should be clearly highlighted; and in panel (e) y axis units are not specified.

Regarding the methylene blue (MB) decomposition experiments performed by UV-Visible absorbance there is a control missing. Authors have not shown the decomposition rate of MB when incubated in absence of ZnO and ZnO-NPs under UV irradiation. Additionally, in Figure 5 panel (d) authors do not show any deviation or standard errors for the points measured. Authors should state the number of replicates performed for these experiments.

For the antibacterial screening authors present their results Figure 8 and Table 2 but again results don’t show any deviation or standard errors; authors should clearly state the number of biological and experimental replicates carried out. Authors should specify the colony forming units and/or optical density used for the experiment and if the MIC values were evaluated by absorbance or naked eye visual inspection. Additionally, Figure 8 shows microbial and non-microbial growth labelling opposite as described in the text and shown in Figure.

The manuscript is clearly written and easy to understand, however a careful revision of English language would improve the current manuscript. Additionally, authors should properly introduce all abbreviations in the manuscript.

Author Response

Please see the attached file.

Author Response File: Author Response.pdf

Reviewer 2 Report

The authors present their work on preparation, photocatalytic and antibacterial properties of ZnO nanoparticles, which is an appropriate topic for the chosen special issue.

The prepared ZnO-NPs are compared with so called “pure ZnO”, which is commercially available product. As can be seen on Fig. 5(d) the photocatalytic performance of both materials (as-prepared ZnO-NPs and pure ZnO) is very close. The difference in the degradation efficiency is approx 5 % which is negligible and it is not significant for evaluation of the ZnO-NPs as material with “enhanced photocatalytic performance”. In this aspect, it is doubtful whether the method reported is really “efficient method”. Therefore, my first question is what is the novelty of the paper?

Apart from this, I would comment some figures and interpretations in the text:

1. Figure 4. The UV-vis spectrum looks unusual: the shape of the peak at 383 nm is not typical UV-vis band and the curve from 400 to 600 nm is almost linear which is not characteristic for UV-vis spectra. I recommend the authors to prepare a new graph as reconsider axis, scale and etc.

2. In line 145 is given the band gap of ZnO to be 3.23 eV. It will be better if the authors confirm the calculated value by Tauc’s plot of UV-vis data. It will be in conjunction with the UV-vis spectrum.

3. in line 138: What is “original absorption peak”? It is better to give references and cite other authors.

4. In line 139 “adsorption” should be replace with absorption.

4. I suppose a mistake in figure 8. Check it, please.

5. I recommend figure 9 to be shifted in Supporting information.

6. In lines 317 – 322 is given the probable reaction mechanism. Do the authors rely on some evidence for the proposed mechanism? What is the compound ZnO4(CH3COO)6? Is it possible such mechanism? What are chemical processes behind the reaction steps?

7. I recommend a TG/DTA analysis for thermal decomposition of zinc acetate as a precursor in the reported method.

In conclusion, the experimental data reported in this paper are scarce and discussion is based on general information much more than on new findings. In order to attract the reader’s attention this paper should be generally rewritten and reconsidered.

Author Response

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Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

The authors have made a great effort to address the different suggestions raised by the reviewers.

Authors specify both in Introduction (lines 69-70) and Experimental methods (lines 382-383) that several pathogenic E. coli strains were used for the antibacterial MIC assays.

Authors should include in results (or supplemental) and Experimental methods these experiments for each strain. All strains had the same MIC values?

They should clearly state which strains were used and if those were clinical isolates and how their pathogenicity was assessed.

Author Response

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Author Response File: Author Response.pdf

Reviewer 2 Report

The presented revised manuscript was significantly improved in terms of results, interpretation and writing. It is much more understandable for the readers then the first version, and it would be a good contribution for the journal.

I have a few comments on the text:

1. line 142 – replace adsorption peak with absorption peak

2. lines 161 – 164 – the words repetition in two successive sentences gives misunderstanding. Please, edit the text

3. line 162 – “to’ is missing. From room temperature to 110 C

4. in the paragraph (lines 157-168) the TG/DTA analysis is presented and in lines 352-355 the decomposition mechanism is shown. Can you make a logical connection between both parts?

5. lines 207-208: “The rate constants were obtained from the absorbance vs time curves (Figure 7b).” Do you mean: the rate constant was determined by the linear plot ln(Co/C) against time, which is fig. 7b

6. line 215-218: The equation gives the relationship between ln(Co/C) and time, not absorption and time. Please, revise the text

7. in Fig 8 the band gap is given as 3.26 eV but in the text it is 3.23 eV

8. line 278: The decomposition of MB goes through several steps up to CO2 and H2O. It is better to point out that final products are CO2 and H2O.

9. line 338: introduce the reagent noted as ZAD with its chemical name and formula

Author Response

Please see the attached file.

Author Response File: Author Response.pdf