General points / major revisions

In their manuscript, Abramov et al studied the process of Microbial Induced Calcite Precipitation (MICP) in arid soils stimulated by the addition of urea. Their main aims were to characterize the native microbial community and their ureolytic efficiency and study the effect of the biostimulation (urea addition) on microbial diversity. Due to the expected heterogeneity in soil microbial community, they collected samples from three different sites and three different depths (surface, 50 cm and 100 cm). They estimated ureolysis rate by periodic measuring of the urea concentration and used it as the proxy for the MICP potential.

As I got familiar with the MICP topic, I found the method exciting and was particularly impressed by its promising application in ground improvement. I was intrigued by the author’s novel attempt to characterize native soil community and the impact that the MICP-stimulating urea would have on it.

The writing of the manuscript was generally fluent and precise, and the related work was to my knowledge properly credited and referenced. The abstract provided a concise summary of the manuscript. The title, however, gave me a wrong expectation of the scientific approach, which I elaborate on further below. I found methodology not entirely clearly outlined, which I write about in more details in Minor remarks. Some figures could be enhanced or clarified, which I also mention in more details in Minor remarks.

A major weakness of this manuscript is, in my opinion, the experimental setup, which I find flawed in aspects described below:

1. The authors aim to compare the non-biostimulated and biostimulated native soil microbial communities. I therefore expected the authors to have administered a low volume of urea-containing solution on soil and compared the microbial community before and after the application. However, as described in the manuscript, the authors actually compared native soil microbial community to a soil slurry they generated by suspending 10 g of (arid) soil in 100 mL of urea medium for 20 days. As expected, exposing the microbial community from arid, nutrient-poor soil to water and high concentrations of urea (and other nutrients contained in the yeast extract) resulted in a completely different community. This outcome can, however, no longer be ascribed to single effect (urea), but is instead very likely the result of overall drastically changed environmental conditions. This flaw in the experimental design is not mentioned in the manuscript.
2. This experimental setup leads to several flawed conclusions. As the native microbiome is subjected to drastically different incubation conditions, the alpha diversity of the microbial community declines. Even though it cannot be ascribed solely to urea addition, the authors clearly relate this decline to biostimulation and make it an important point both in the discussion and in the conclusions.
3. Another flawed conclusion concerns the characterization of ureolysis-related environmental changes. The outcome of the biostimulation experiment is a drastic increase of pH. In the discussion, the authors suggest a similarity between the measured increase in pH in soil slurry and potential pH increase in MICP-treated soil pore fluids. I find the conditions in the described soil slurry incomparable to conditions, geochemical properties and natural buffering capacities of soil. Due to this reason, I consider drawing parallels between the two systems inappropriate.
4. Throughout the manuscript, I found no mention of a control treatment. If the authors choose to drastically change the environment of the soil microbiome by generating a soil slurry, I suggest adding a treatment in form of a soil slurry where urea is omitted from the nutrient medium. By comparing the control treatment to the native soil, the authors could disentangle the influence of incubation conditions compared to the influence of urea on the native community.

Due to described concerns, I consider the author’s approach not appropriate to support the interpretation and conclusions.  

Minor remarks:

Introduction

59 – Is the citation on the importance of cyanobacteria a bit too general? The reference is a book titled “Biological soil crusts: structure, function and management” from 2003. Wouldn’t it be better  to find a source which directly claims that cyanobacteria (and not for example lichens or algae) constitute a key group in arid biocrusts? According to descriptions in “What is a biocrust? …”, in hyperarid regions, biocrusts consist of cyanobacteria and / or algae, while in arid regions, they are generally dominated by cyanobacteria or lichens, with patches of bryophytes commonly found in wetter microsites. In the manuscript, there is a strong accent on cyanobacteria – why is the significance of algae or lichens not discussed? Is it because they cannot be characterized by 16S sequencing?  A photograph of sampling area, where studied biocrust are visible, would be helpful as part of the Supplementary Data.

67 – typographic error; I assume the authors meant “drought” (a shortage of rainfall) and not “draught” (a cold burst of wind).

86 – one of the references for archaea becoming more abundant in deeper soil horizons may not apply; from my understanding, the paper by Sokol et al. 2022 is nowhere stating that archaea are more abundant in deeper soil horizons.

Materials and Methods

122 – from this sentence, it seems like biostimulation experiments were only performed on soils from 3^rd site. The 3^rd, disturbed site is not clearly described – how was it disturbed? Were upper soil layers placed on the bottom and vice-versa? A photo in Supplementary Data would also be helpful.

123 – “disturbance approximately 20 before this study” – I guess 20 years?

125 – I am guessing that overall, 12 samples representing Negev soil mean only Site 1 and Site 2, because the math otherwise does not add up (3 sites x 3 depths x 2 replicates = 18 sites; 2 sites x 3 depths x 2 replicates = 12 sites).

138 – here it seems again like only samples from Site 1 and Site 2 were biostimulated, as the number of biostimulated samples is 12? Then how come the biostimulation effect is later also described for the 3^rd, disturbed site?

150 – If possible, I would advise not to use NanoDrop spectrophotometers for DNA extracted from environmental samples; a fluorimetry-based assay, such as Qubit, is more reliable for measuring DNA concentration. Spectrophotometry-based quantification is often reported to overestimate DNA concentrations and is strongly influenced by other proteins and contaminants, which would in case of DNA extracted from soil include humic acids.

152 – I would expect more details for the library preparation: which exact region of the 16S rRNA gene was amplified, which primers were used (including references where primer design is described), how long was the expected PCR product, details about the PCR program (steps, temperatures, number of cycles).

Results and discussion

213 (figure 1) – the green and blue line look very similar; it’s sometimes hard to distinguish between them.

227 (figure 2) – in this figure, there are samples which strongly separate on the PC1 axis from the rest of the samples (these are on the left side) – I think a reader would like to know what are these samples. The colors are very similar, especially in case of the PCA graph, it’s hard to spot the difference under certain light conditions.

305 (figure 5) – the colors close on the spectrum are very similar; it’s very hard to see on the graphs which colors correspond to which taxa.

451 – there is an error in the reference; ;Asce, S.M and Asce, M. are not author names.

The authors study the impact of ureolytic biostimulation on the soil microbiome in Aridisols. The approach of the authors is scientifically sound and the results are worth to be published. The manuscript is well-written and shows only minor slips. In addition, the manuscript is structured in a comprehensible and clear way. However, it is not totally clear why the authors took samples from three sites, but in large parts only refer to two (undisturbed) sites and did not treat the samples from all three sites in the same way - this needs to be explained. The authors should also - at least shortly - discuss the reasons why soil depths has an impact on microbial communities (litter input, soil moisture...). And while the authors mention that they analyzed the chemical and physical properties of the soils, this is completely neglected in the Results/Discussion. The authors should therefore include in their Discussion other factors that could have had an impact on the microbial communities.   

Overall, the authors should tighten their manuscript, some parts are repetitive. Especially the last part of the Results/Discussion section should be tightened and focus more on the authors' results. The authors should also stick to basic rules of writing: Do not start a sentence with an abbreviation, write numbers up to ten as words etc.  

  

Please see my detailed comments below:

Title:

The title could be more precise: What are the responses? How do they change with depth? 

Abstract:

l. 25 I suggest to replace "possess" by "fulfill", "play" or something similar. 

l. 44 Do you mean that members of the Planococcaceae family replaced Paenibacillaceae and Bacillaceae as most prevalent Firmicutes? 

Introduction

l. 62-62 I suggest to rephrase this sentence or delete it.

l. 63 This reference (Zuazo and Pleguezuelo, 2009) is not in your list of references.  

l. 62-69 In this passage, the connection between the relevance of biological soil crusts and the role of MICP should be made clearer.

l. 83-92 You should at least shortly indicate why soil depth has such an impact on microbial communities - litter input, temperature, moisture regime in the soil...

l. 106 What do you mean by "microbiology of MICP"? Why is knowledge "particularly lacking" in the Negev? You stated before that it is widely lacking.

Materials and methods

l. 119 Please include a reference for the soil classification (USDA soil taxonomy). 

l. 123 20 what prior to your study? 

l. 123-124 Please indicate cleary from which depths you took samples - what do you mean by surface? 0-5 cm? 0-10 cm? You should give the precise range, especially as you refer to "soil layers" later.  

l. 125 Why n=12 samples? You have three sites and samples from three depth per layer in duplicates? Should be n=18? 

l. 126 Why did you not include site 3 here? 

l. 127 You do not need "refridgerated" here. 

l. 131 Please include a short description and not only a reference to another publication.

l. 131-132 How do you explain the huge standard deviation and why do you add this information here and not in the Results section? 

l. 149 At which temperature?

Results and discussion

l. 178-181 You do not need that additional introductory part here.

l. 183-184 The first sentence is also not needed here. 

l. 189 It should be "...than in the topsoil..."

l. 198 Why do you use passive here ("...has yet to be recovered.")?

l. 200-202 How do you know that the decisive factor is the disturbance? You do not present the results of the chemical and physical characterization of the soils, so it is not clear if there are differences that could also have an impact. 

l. 224 I suggest to rephrase this part and write something like "...and hosted similar communities..." instead of "...and did not host distinct communities...".

l. 234-235 Please rephrase this sentence. 

Figure 3 Why did you put the panels in this order? I suggest to start with the surface on the left and end with the 100 cm depth on the right. 

l. 253-254 You do not have to announce what you are going to discuss later. 

Figure 4 Please take care that your labels are consistent. Here, you use "hndred cm" and "fifty cm", while you use "100 cm" and "50 cm" everywhere else. 

l. 319 What do you mean by "it" here? ("...we found it had a more prominent influence...")

Conclusions

Please take care that your Conclusions are coherent, at the moment some sentences seem not be related to the sentences before and after them.