We sincerely apologize for the significant delay in submitting our point-by-point response to the reviewers’ comments.. In order to address the reviewer’s concerns as carefully and comprehensively as possible, we undertook substantial additional work during the revision period to improve the manuscript and to reassess several parts of the analysis. We are deeply grateful to the reviewer for the careful reading of our manuscript and for the constructive, thoughtful, and insightful comments. We fully acknowledge that the original version did not adequately satisfy the reviewer’s specific concerns. Accordingly, in the revised manuscript, we have focused on clarifying key definitions, strengthening the treatment of measurement uncertainty and its relation to the reported model accuracy, adding a sensitivity analysis of the dynamic formulation, clarifying the validation strategy and error definition, improving the physical explanation of the dynamic–thermal coupling assumption, and revising the relevant figures, captions, and parameter descriptions for greater clarity and rigor. Our point-by-point responses are provided below.

General comment 1

Comment:The derivation of Eq. (8) does not include a quantitative uncertainty analysis of either the measurements or the resulting model output. Given that the reported prediction accuracy is better than 3.5%, it is important to assess whether this level of accuracy is meaningful relative to the underlying uncertainties. It would be great if an estimate of measurement uncertainties (e.g., on size, velocity, collision angle) could be provided and if possible, a propagation of these into the model results.

I know that particularly the propagation can be very challenging or impossible. However, at minimum, it would be great to visualize how the fit parameters in Eq. (8) were obtained by showing the underlying dataset together with the fitted curve to get an idea on the data spread. It then can including uncertainty estimates (e.g. confidence intervals or covariance information).

Response: Thank you for pointing out this important issue. We agree that the key point is not simply the wording of the 3.5% value, but whether this value is meaningful relative to the uncertainty of the input measurements. We therefore addressed this comment by adding a quantitative uncertainty discussion focused on the three directly measured quantities used in the model, namely droplet diameter, impact velocity, and collision angle. In the revised manuscript, we now report the estimated measurement uncertainties of these quantities and describe how their uncertainties affect the predicted sticking efficiency through the dynamic and thermal formulations.

Regarding the suggestion of a calibration figure for Eq. (8), we understand that this was proposed as a minimum fallback if a propagation analysis could not be provided. Because we were able to address the primary issue through measurement-uncertainty estimation and propagation, and because a separate multi-parameter fit-surface figure would be difficult to interpret without the full covariance structure of the ternary fit, we chose not to add an under-explained calibration plot. Instead, we clarified in the text  how the uncertainty of the measured inputs affects the model output. We believe this revision addresses the reviewer’s main concern more directly while avoiding the addition of a figure that would not substantially improve the scientific clarity.

General comment 2

Comment:It remains unclear which input parameters in the dynamic formulation dominate the attachment probability. Here, a sensitivity analysis would be very helpful to identify the most influential parameters, assess the model robustness, and may allow for further generalization if dependencies are negligible.

Response: Following this suggestion, we added a local sensitivity analysis for the dynamic-stage attachment probability. The analysis was carried out directly from Eqs. (7)–(9): for representative operating points in the transition regime, droplet diameter d, impact velocity vd, and collision angle θ were perturbed one at a time by ±10% while the other variables were kept fixed, and the corresponding change in the dynamic attachment probability Ps was evaluated. We then computed the normalized sensitivity coefficient Sx = (ΔPs/Ps)/(Δx/x) for each variable. To avoid drawing conclusions from a single operating point, the calculation was repeated for several representative cases spanning different sticking regimes. The resulting sensitivity analysis has now been added to the revised manuscript and is also summarized in supplement. The analysis shows that impact velocity is the dominant control on Ps in the dynamic formulation, droplet diameter is the second most important variable, and collision angle becomes particularly influential in the oblique-impact transition regime where tangential stripping competes strongly with normal-impact retention.

General comment 3

Comment:The validation strategy of the model requires further clarification. In particular, to me it is unclear if the model parameters are derived from the same dataset that is used for validation. In that case, the comparison to the other three models (Jones, Makkonen, Mundo) would be slightly unfair as the proposed model would have been tuned to the validation data set.

It is further unclear if the three other models were applied in their respective parameter range and what the input parameters have not been described.

In the validation against real world icing the derivation of the true sticking efficiency “ηtrue” is said to be measured (line 243). How is this value measured? This is a critical point as the main claim of the paper being accurate below 3.5% relies on it. In Figures 9 to 11 it would  be great to not only show the errors but also the real values for each case. Further, please state which kind of error is shown here. 

Response: We appreciate this comment and have revised the validation section substantially.

First, we now state explicitly that the empirical coefficients in Eq. (8) were calibrated from the laboratory impact dataset. For this reason, the laboratory comparison is no longer described as a fully independent blind validation. Instead, in the revised manuscript it is described more precisely as a within-dataset benchmark comparison against the Jones, Makkonen, and Mundo formulations under the same laboratory conditions. This wording better reflects the actual role of the laboratory data.

Second, we now clarify how the comparison models were applied. In the revised validation subsection, we specify that the same measured environmental and droplet input conditions were used for all models as far as permitted by each formulation, and that each reference model was applied within the scope of its own input structure. This makes the comparison procedure clearer and more transparent.

Third, we revised the wording around ηtrue for the field cases. The reviewer is correct that the original manuscript did not explain clearly enough how ηtrue was obtained. In the revised version, we clarify that ηtrue for the three field icing cases is not obtained by direct droplet-by-droplet counting. Instead, it is derived by inverse analysis from the observed icing response of the transmission line together with the estimated incident supercooled-water flux under the recorded meteorological conditions. We retain the symbol ηtrue, but we now explain explicitly what it means operationally in the field-validation context.

General comment 4

Comment:Please elaborate more on the assumption of that freezing and dynamic processes are independent (lines 257ff). Is that a valid assumption and are these fully independent? Doesn't the contact time also depends on the dynamical features. Same for the freezing process itself i.e., the spreading / contact area depend on droplet size and impact velocity etc. 

Response: Thank you for this important comment. We agree that the wording in the original manuscript was too brief and could be misunderstood as claiming strict physical independence. That is not what we intended. In the revised manuscript, we now explain the modeling logic more explicitly.

The two-stage formulation is used as a sequential engineering decomposition of the sticking process. The dynamic stage determines whether the droplet remains on the surface after impact long enough for freezing to become relevant, while the thermal stage evaluates whether the retained liquid can freeze within the effective contact time. In this sense, Eq. (13) is not meant to assert that the two mechanisms are fully uncoupled. On the contrary, part of the coupling is already carried into the thermal stage through the kinematically dependent contact time tc in Eq. (10), and through the angle- and impact-dependent correction terms Ac and beta vn^2 in Eq. (11). We have therefore revised the manuscript to describe Eq. (13) as a first-order conditional product approximation for engineering prediction, rather than as a claim of strict physical independence.

Minor comment 1

Comment: Generally: Please make figure captions more descriptive and clear. Figures captions should allow to understand the figure fully without the need to search in the main text.

Response: Revised as suggested. All figure captions have been rewritten to be more self-contained and clearer.

Minor comment 2

Comment: Line 45: "exhibit errors exceeding 30%": Please specify compared to what.

Response: Thank you. We agree that the original sentence was too categorical. The "exceeding 30%" statement was intended as a literature-based order-of-magnitude summary of deviations reported for existing icing models under complex operating conditions, rather than as a value derived from one standardized benchmark dataset. To avoid overstating the point, we revised the sentence so that it now refers more cautiously to errors on the order of several tens of percent reported in previous studies under complex icing conditions, and we clarified that this statement is literature-based.

Minor comment 3

Comment: Line 49:  What is meant with that statement: "This technology is not limited by particle shape."?

Response: We clarified this sentence. The revised manuscript now states that digital holography does not require a priori spherical-particle assumptions in the reconstruction step and can therefore be applied to droplets or fragments with non-spherical or evolving shapes.

Minor comment 4

Comment: Line 58ff: "[...] is successfully reduced to within 3.5%." Also here specify what the error is referenced to? Training data, in-situ measurements etc.

Response: We revised this statement and now specify exactly what this error refers to. In the revised manuscript, the reported value is defined as the absolute relative difference between the model prediction and the corresponding laboratory or field reference sticking efficiency used in the validation subsection. We also now state more explicitly that the relevant uncertainty sources include the holographic retrieval of droplet diameter, impact velocity, and collision angle, the repeatability of the impact experiments, and, for the field cases, the inverse derivation of ηtrue  from icing observations.

Minor comment 5

Comment:Line 89: Latent heat of fusion should be per unit mass, not volume. Otherwise units do not cancel out to yield seconds

Response: Corrected. L is now defined as the latent heat of fusion per unit mass, and the associated wording around Eq. (2) has been revised for dimensional consistency.

Minor comment 6

Comment: Line 101: How do "n particles" come into play in Eq. 3?

Response: We clarified this directly after Eq. (3). The revised text now states that the reconstructed wave field is the superposed contribution of the n particles contained in the sampled measurement volume.

Minor comment 7

Comment: Line 127: Which three experiments? Please specify what is meant here.

Response: Thank you. This was a wording error in the original manuscript. The sentence did not refer to three different experiments; it was intended to describe the optical measurement principle used in the experiment. We have corrected the wording accordingly so that it now refers to the experimental principle rather than to "three experiments."

Minor comment 8

Comment: Line 138: What about the droplet size as variable? Or are the produces droplets mono-disperse? Fig.2 shows a broad size distribution.

Response: We clarified this point in the revised manuscript. The spray generator does not produce perfectly monodisperse droplets. Different nozzles were used to target different droplet-size ranges, but the actual diameter of the impacting droplets was determined from the holographic reconstruction and then grouped for analysis. We now state this more explicitly in the experimental section.

Minor comment 9

Comment: Line 172: How is the splashing probability defined here?

Response: We apologize for the ambiguity. In this part of the manuscript, "splashing probability" was intended to represent the mass fraction of the incident droplet that is lost by splash after impact, i.e.

Psp = msplash / m0,

where msplash is the splashed liquid mass and m0 is the total pre-impact droplet mass for the impact event. It does not refer to the number fraction of droplets that splash. We now define this quantity explicitly at first use and distinguish it clearly from the sticking efficiency discussed elsewhere in the manuscript.

Minor comment 10

Comment: Fig 5 to 7 right panels: Do the plots show the final sticking efficiency according to Eq. 13 or splashing probability. If they show the sticking efficiency following Eq. 13 it must be somehow explained earlier in the manuscript.

Response: We clarified this in both the main text and the figure captions. The right panels of Figs. 5-7 show the experimentally measured sticking efficiency under the corresponding experimental conditions; they do not show the splashing probability and they are not direct plots of Eq. (13) alone. The text has been revised to prevent these quantities from being conflated.

Minor comment 11

Comment: Lines 183-184: "Experimental analysis [...] roughly 10%, hence λ ≈ 0.1". This statement requires further clarification on how it is derived.

Response: We revised this statement to make the derivation clearer. In the revised manuscript, lambda is described explicitly as an empirical oblique-impact correction coefficient introduced to represent the additional shear effect under non-normal impact. The value lambda ≈ 0.1 was obtained by fitting the shift in the experimentally observed transition between retention and splash under oblique impact, relative to the near-normal case, within the present dataset. We no longer present the 10% value as a universal physical constant.

Minor comment 12

Comment: Lines 199-200: Do the constants A, B, C have a physical meaning? A and B lack units.

Response: We clarified this point after Eq. (8). In the revised manuscript, C is described as the baseline scale of the critical Weber-number threshold, while A and B are empirical scaling coefficients introduced through the nonlinear fit. Their dimensions depend on the units adopted in the fitting procedure: with droplet diameter expressed in mm and velocity in m s^-1, A has units of mm^-1 and B has units of (m s^-1)^(-delta). We now state this explicitly so that the dimensional consistency of Eq. (8) is clear.

Minor comment 13

Comment: Eq 9: Where do the factors 0.3 and 0.7 come from?

Response: We now explain this explicitly. The value 0.3 is the lower boundary of the transition interval for the ratio Weeff / Wecr below which sticking is taken as effectively complete in the present engineering formulation. The value 0.7 is the width of the linear transition interval between 0.3 and 1.0, used to interpolate the sticking probability from 1 to 0 as the effective Weber number approaches the critical value. In the revised manuscript, these are described as empirical transition parameters introduced to match the observed gradual change between complete sticking and non-sticking.

Minor comment 14

Comment: Eq. 11: How are the correction terms Ac and β established? Where does the 0.8 come from? How was β measured and derived?

Response: We revised the explanation of Eq. (11). In the revised manuscript, Ac = 1 + 0.8 sin(theta) is presented as an empirical correction for the increase in effective spreading/contact area with collision angle, and the coefficient 0.8 is stated to come from fitting the observed angle-dependent spreading behavior in the impact images. The coefficient beta is described as an empirical enhancement factor introduced to represent the increase in effective interfacial heat transfer caused by impact-induced thinning of the air layer and increased liquid-solid contact. Its value was obtained by fitting the freezing-time correction term to the present impact/freezing dataset. We now state clearly that both Ac and beta are empirical calibration terms within the present model.

Minor comment 15

Comment: Line 234-235: What is meant with: "[...] inverse analysis of actual transmission line icing data, [...]"

Response: We clarified this in the validation section. In the revised manuscript, "inverse analysis" is defined as the back-calculation of ηtrue from the observed ice accretion response of the transmission line and the estimated incident supercooled-water flux under the corresponding meteorological conditions.

Minor comment 16

Comment: Eq.12: Why was a exponential behavior selected?

Response: We now explain this modeling choice more clearly. The exponential form was selected as a bounded and monotonic engineering closure for incomplete freezing when tc < tf. It ensures Pf = 1 when the effective contact time reaches the freezing time and produces a smooth decrease in freezing probability as the available contact time becomes shorter than the required freezing time. The revised manuscript makes clear that this is an engineering parameterization rather than a uniquely derived fundamental law.

Technical correction 1

Comment: Introduction: please apply proper use of citation style including the years (see \citep vs. \citet)

Response: The citation style has been checked and revised throughout the manuscript so that narrative and parenthetical citations are used consistently.

Technical correction 2

Comment: Line 38ff: Is the citation Snaiki et al or Lamali et al?

Response: This inconsistency has been corrected to “Snaiki et al.” in the revised manuscript, consistent with the reference list.

Technical correction 3

Comment: Line 102: math mode issue $(u,v)$

Response: This formatting issue has been corrected.

Technical correction 4

Comment: Caption figure 4: Check for several missing blank spaces and unit after time

Response: The caption of Fig. 4 has been reformatted and rewritten for clarity, including the missing spaces and consistent unit presentation.

Technical correction 5

Comment: Eq. (6): Be consistent using vd and vn throughout the manuscript--> adapt v in (1) and (5) to vd

Response: We agree and have revised the notation accordingly. The impact velocity is now denoted consistently as vd, and the normal component as vn, throughout the relevant equations and text.

Technical correction 6

Comment: Line 245: add suffix to vd also for case 2 and 3

Response: This notation has been corrected in the revised validation section.

We sincerely apologize for the significant delay in submitting our point-by-point response to the reviewers’ comments. During the revision period, we carried out substantial additional work to improve the completeness and clarity of the manuscript and to address the reviewer’s concerns in a thorough manner. We sincerely thank the reviewer for the careful evaluation of our work and for the constructive and highly insightful comments. We fully recognize that the original manuscript did not sufficiently meet the reviewer’s specific expectations. Therefore, in the revised manuscript, we have focused on strengthening the analysis in Sections 3 and 4, expanding the physical interpretation of the observed trends and the comparison with existing models, clarifying the definitions and physical meaning of key fitted parameters, improving the discussion of uncertainty and reproducibility, revising the Introduction to better define sticking efficiency and distinguish it from collection efficiency, and refining the graphical abstract, figure captions, notation, citations, and overall presentation throughout the manuscript. Our detailed point-by-point responses are given below.

Major Comment 1:

Comment: The main concern is that the core results are not analyzed in sufficient detail. Section 3 mainly describes the experimental setup and selected example cases, but does not provide a systematic analysis of the measured droplet properties. Section 4 focuses on model development and validation, but the discussion remains largely descriptive. The relationships between key variables (e.g., droplet size, velocity, and collision angle) and sticking efficiency are shown in figures, but the physical interpretation is limited. In addition, the comparison with existing models lacks depth. The manuscript would benefit from a clearer explanation of why the observed trends occur and how they relate to existing theories and models.

Response: Thank you. We agree that the original Sections 3 and 4 were too concise. In the revised manuscript, we retained the original overall structure but substantially strengthened the interpretation of the results. In Section 3, we now explain more clearly why Fig. 4 is presented, namely as a representative three-dimensional reconstruction example illustrating the retrieval of droplet trajectory, diameter, impact velocity, and collision angle, rather than as the sole evidential basis of the study. In Section 4, we expanded the discussion of the observed trends in Figs. 5-7 so that the physical reasons behind the dependence on collision angle, impact velocity, and droplet size are explained explicitly in terms of normal-impact inertia, tangential shear, splash/breakup, and freezing-time effects. We also deepened the discussion of the comparison with the Jones, Makkonen, and Mundo models by clarifying the structural differences between those formulations and the present two-stage model.

Major comment 2

Comment: The proposed model consists of a dynamic phase and a thermal phase. While the formulation is generally clear, the definitions of key parameters, the citations of appropriate references, and the physical interpretation need further clarification. Several modified or fitted parameters (e.g., the modified critical Weber number) are introduced, but the underlying assumptions and their physical meaning are not sufficiently justified. These aspects should be explained more clearly.

Response: We agree and revised the manuscript accordingly. The model is now described consistently as a two-stage coupled model. The effective Weber number, the modified critical Weber number, the transition parameters in Eq. (9), and the correction terms in Eq. (11) are now each identified more clearly as either physically motivated approximations or empirical calibration terms. We also added references where important parameters or physical concepts are introduced and improved the surrounding explanations so that the assumptions behind the model are more transparent.

Major comment 3

Comment: The manuscript reports that the prediction error is within 3.5% under various conditions. This is a strong claim. However, there is no clear description of uncertainty sources in either the measurements or the model. Moreover, uncertainties in droplet size, velocity retrieval from holography, and experimental repeatability are not quantified. A proper uncertainty analysis and robustness assessment are needed to support the reported model performance.

Response: We agree that this issue required a more direct treatment. In the revised manuscript, we added an uncertainty-focused discussion that identifies the main uncertainty sources in the study: holographic retrieval of droplet diameter, impact velocity, and collision angle; experimental repeatability; and the derivation of ηtrue for the field cases. We also added a first-order propagation analysis of the measured-input uncertainty through the model and now discuss the reported < 3.5% prediction error in that context. The revised wording no longer treats 3.5% as a universal model guarantee; instead, it is presented explicitly as the absolute relative prediction error obtained for the validation cases considered in this study.

Major comment 4

Comment: Several parts of the manuscript require substantial revision in terms of clarity, structure, and formatting. In the Introduction, the presentation lacks clarity and logical flow. The background section mainly consists of a list of references without sufficient synthesis or discussion. More importantly, the key concept of sticking efficiency, which is central to the manuscript, is not clearly introduced or defined. The relationship and distinction between sticking efficiency and collection efficiency should be explicitly clarified. In addition, many references are missing where they are needed, and some citations are not formatted properly (e.g., “Jiang et al.” in Line 31). There are numerous similar issues throughout the manuscript, and a thorough check is required.

Response: We agree and revised the Introduction substantially while preserving the original topic and flow as much as possible. In the revised version, sticking efficiency is defined explicitly near the beginning of the Introduction as the fraction of supercooled droplets that remain attached after impact. Its relationship to collection efficiency is also clarified: collection efficiency is the broader interception/retention concept, while sticking efficiency in this work refers specifically to the post-impact retention behavior at the droplet scale. We also reorganized the literature review so that it is less list-like and more focused on the specific limitations of previous methods, and we checked and corrected the citation formatting throughout the manuscript.

Specific comment 1

Comment: The manuscript refers to the proposed framework as a “multi-stage coupled model”, while it is consistently described and implemented as a two-stage model (dynamic and thermal phases). The use of “multi-stage” is potentially misleading and should be corrected throughout the manuscript.

Response: Corrected throughout the manuscript.

Specific comment 2

Comment: Graphical abstract (left panel): The meaning of the icons (e.g., histogram icon, arrow icon) inside the text boxes is unclear. They resemble prompt-style elements rather than scientific annotations. The arrows on both sides of the text boxes are also not clearly explained.

Response: The graphical abstract has been revised accordingly. The icon-like elements were replaced with explicit scientific labels for droplet size, three-dimensional velocity, and collision angle, and the workflow arrows were simplified.

Specific comment 3

Comment: Graphical abstract (right panel): It would be more effective to redesign this panel based on the experimental figures (e.g., Figs. 5-7) to better reflect the content of the study.

Response: The right-hand panel has been revised so that it reflects the experimentally observed sticking-efficiency trends more directly and is better aligned with the actual content of the study.

Specific comment 4

Comment: Lines 68-70: Important parameters should be supported by appropriate references when they are defined and introduced. Similar issues occur elsewhere in the manuscript.

Response: Additional references have been added at the relevant points, and similar omissions have been corrected elsewhere in the manuscript.

Specific comment 5

Comment: Lines 72, 89, 104: “Where…” should not be capitalized, as it follows a comma.

Response: Corrected throughout the manuscript.

Specific comment 6

Comment: Line 139: At least five repeated experiments are mentioned, but only representative data are shown. The reproducibility of these experiments is not discussed. The uncertainty and representativeness of the selected results should be clarified.

Response: We clarified this point in the experimental section. The revised manuscript now states explicitly that repeated runs were used to confirm the reproducibility of the observed trends under each tested condition, whereas the examples shown in the figures are representative cases selected for concise presentation.

Specific comment 7

Comment: Figure captions: All figure captions require further clarification. They currently show trends but lack sufficient detail about the experimental conditions.

Response: Revised as suggested. All figure captions are now more detailed and self-contained.

Specific comment 8

Comment: Lines 146-150: The criteria used to evaluate the validity, reliability, and uncertainty of the measured and reconstructed results are not clearly described. It is also unclear why only one example (Fig. 4) is presented.

Response: We revised the corresponding paragraph to explain more clearly that Fig. 4 is included as a representative demonstration of the reconstruction and trajectory-extraction capability of the digital holography system, whereas the broader conclusions are based on repeated measurements over the full parameter space described in the validation section.

Specific comment 9

Comment: Fig. 5: Please add panel labels for the right panel.

Response: Added in the revised figure.

Specific comment 10

Comment: Figs. 5-7: Please include uncertainty ranges or confidential intervals for the sticking efficiency under different experimental conditions.

Response: We agree that uncertainty information is important. In the revised manuscript, rather than adding partially supported confidence intervals to all curves without a full per-condition statistical treatment, we strengthened the quantitative uncertainty discussion in the text, clarified the repeatability basis of the plotted trends, and added the propagation-based uncertainty assessment described in the response to Reviewer #1 General Comment 1. We believe this addresses the reviewer’s concern more directly while keeping the graphical presentation scientifically defensible.