The manuscript addresses a relevant and interesting question about the role of solute diffusion into the rock matrix during fracture flow. In this work, the authors present a "unified" parameter to assess the relevance of matrix diffusion and a correction term to the analytical solution of solute transport in a single fracture that mimics the effect of matrix diffusion without the need to explicitly model matrix diffusion, thus reducing the computational burden.

I have several comments to improve the manuscript:

1) The manuscript remains descriptive in several places where quantitative limits and criteria would benefit the text. These include: 

* l131: "shows extremely small concentrations". I believe values would give the reader a better understanding.

* l132: "R is approaching a maximum value". What specific value? The definition of R does not seem to approach an analytical limit, since the value depends on the number of data points (see comment below).

* l145: "an almost linear relationship". Can a R^2 or any other fit quality parameter be provided to assess the quality of the linear fit? Is there any systematic deviation from the linear trend?

* l171: "shows the largest correlation coefficient". I believe providing Pearson correlation coefficients explicitly in the text would benefit the readers ability to form their own opinion.

* l184: "has a negligible effect". What do the authors consider negligible? Is it possible to give a quantitative limit.

* l261: "gives the best result". How was this concluded? Can you provide a quantitative measure from which this statement can be understood? 

* l353: "remains a reasonable criterion". Similar to above: What quantitative measure was used to make this determination?

2) The theoretical basis of the paper is sometimes unclear to me, partly because of potentially imprecise formulations

* l37: "the underlying uncertainties". Uncertainties about what? Which relevant parameters are considered uncertain in which situation and to what degree?

* Eq. 2: I think the derivation should be in terms of z, not x in the diffusion part, to be consistent with the original sources, such as Graf & Simmons (2009). If the authors derive from the original source, this needs considerable attention and explanation.

* Eq. 4: The symbol \xi is missing an explanation * l113f: The order for C_f and C_mf should be "fracture-only and fracture-matrix coupled models, respectively", I guess.

* Eq. 6: The definition of R in its discrete form is irritating for me. Should it not follow an integral form related to a tracer recovery form or similar? In its current form, R seems to depend on the number of data points chosen in the breakthrough curves (BTCs), which could be an arbitrary number or at least depends on the spatial discretization, and makes comparison between BTCs difficult, as I assume the same N must be used. I think this has a major impact on the analysis presented here. The chosen form, if it remains in the revision, should be justified and critically discussed to improve the readers understanding of this result.

* Table 1: The given values are not justified. Why were these values chosen? What kind of host rock/fracture system and application do the authors have in mind for their analysis?

* Section 2.2: Why do the authors focus on the linear part of the relationships? Isn't the nonlinear part the much more interesting relationship? 

* l175: The proposed unified parameter is never derived or motivated. Its physical interpretation is not given. This makes it very difficult for the reader to assess its full potential as the parameter seems rather arbitrary in its present form. How did the authors arrive at this parameter? Especially with the results in l194 and l220f, an interpretation of the unified parameter would be very helpful for the reader.

* Section 3: The numerical model lacks a detailed methodological description. What equations have been solved? With which software? Has the code been benchmarked? Initial conditions? Boundary conditions? Compared to other models? ...

* l265: "the fracture-only model overestimates solute transport". What is the result for the unified parameter derived earlier? Does this parameter also indicate that matrix diffusion is relevant?

3) The structure of the manuscript needs to be improved.

* The introduction could more clearly state the computational burden. Currently it only seems to be an additional parameter to be guessed with a simple diffusion equation, which seems not very computationally cumbersome these days. Especially as the  authors focus on a solution for a single fracture and not fracture networks.

* l67: smaller apertures lead to higher flow velocities. Hence, it remains unclear how "smaller fracture apertures and flow velocities" should result in the same effect regarding matrix diffusion.

* l86: The introduction would benefit from a concise discussion of the other five unified and dimensionless parameters from literature, their underlying assumptions and derivations.

* Fig4: Based on the occurrence in the text, the placement and order of Figs 4 & 5 should be reconsidered.

* Section 4.1 reads very much like a repetition from the introduction and a summary of previous results but does not present a critical discussion of the obtained results.

* Sections 4.3 and 4.4 seem to be rather results than a discussion.

* A critical discussion of the results, especially adressing limitations of the unified number and the correction term are needed to provide the reader with a critical assessment of the acomplishments achieved by the authors.

4) The data availability statement seems incomplete and partly imprecise.

Which BTCs are calculated with analytical solutions? I assume section 3 is not based on analytical solutions but computer models/codes are not mentioned in the statement. It should be more clearly stated that the field and lab data is a summary of literature results to avoid confusion.

General Comments

The authors propose a new unified parameter for quantifying matrix diffusion effects, which is incorporated into an analytical fracture-only model to effectively reduce computational cost. Overall, the manuscript presents a solid discussion with a clearly defined research objective. The comparison between the proposed model and the fracture–matrix model, as shown in Figure 4a, further supports the credibility of the approach. However, the manuscript does not quantitatively address how the proposed model improves computational efficiency and predictive accuracy compared to existing methods. Additionally, some explanations are unclear, and it is difficult to correlate them with the referenced figures. Addressing these issues would significantly strengthen the overall contribution of the study.

Specific Comments

1. Line 121. Please provide citations and justify the wide range of each parameter, demonstrating that these values fall within realistic and commonly observed limits in relevant experimental or field studies.
2. Line 123. Please explain the Latin hypercube sampling (LHS) approach and provide the original citation where the method was first introduced.
3. Figure 3. Please add panel labels such as (a), (b), and (c), and refer to these labels when discussing specific parts of the figure in the text.
4. Line 176-178. The previously reported correlation coefficient of 0.96 already indicates a strong relationship. Please clarify whether the 0.03 improvement represents a meaningful difference that justifies the claim that the newly proposed method is better.
5. Line 193-195 & 288-289. Please provide a detailed explanation for why cases with values beyond 0.01 are identified as having negligible matrix diffusion, and why a threshold of 5 s¹ᐟ² is considered a reasonable criterion.
6. Line 204-206. Could you quantify the additional computational cost associated with using a fracture–matrix model relative to a fracture-only model that approximates matrix diffusion?
7. Lines 242 and 255: What is the rationale for introducing the 2D fracture-only model? Please clarify its purpose and how it contributes to the overall analysis.
8. Line 251-253. Please explain what causes the discrepancy between the 3D model and the proposed unified term shown in the sixth panel of Figure 3.
9. Lines 264–267: Figure 4b presents results from the 3D case, while Figures 6b and 6c correspond to 2D cases. It is unclear why the 3D case is being compared with 2D cases, which may be confusing for readers. Additionally, the explanation of the 3D case shown in Figure 6a appears to be missing or unclear.
10. Figure 6: Why does the concentration around the well become fainter over time? Please clarify the physical or modeling reasons behind this trend.
11. Line 318-319. Does the sorptive solute model only account for retardation, without considering the potential release (desorption) of sorbed solutes back into the fracture?
12. Line 345-346. Could you please explain the role of the degradation coefficient in solute transport, and clarify the basis on which the range of this parameter was selected?
13. Rearranging the figures and paragraphs could improve the clarity and readability of the manuscript.
    • It may be clearer to switch the order of Figures 4 and 5. Alternatively, relocating Figure 5 and the corresponding first paragraph to the methodology section could improve the logical flow of the manuscript.
    • Sections 4.1 and 4.2 contain overlapping content. It would be more concise and effective to combine these sections into a single, streamlined discussion.
    • A parallel discussion of the conservative, sorptive (Section 4.3), and degradative (Section 4.4) solutes in the results section would benefit readers. Currently, Figure 4c presents the sorptive case, but this case is not discussed earlier in the text, which may cause confusion.

Technical Corrections

1. Figure 4 contains boundary lines. Please remove them if they are unnecessary.