The manuscript entitled "Identification of Micro-dynamics Phase Transition processes for Ammonium Sulfate aerosols by Two-dimensional Correlation Spectroscopy" investigates the micro-dynamic mechanisms of ammonium sulfate (AS) aerosol phase transitions using two-dimensional correlation infrared spectroscopy (2D-IR), coupled with relative humidity (RH) control. By employing 2D-IR (including generalized 2D-IR and perturbation-correlation moving window 2D (PCMW2D) spectroscopy), the authors successfully elucidate non-equilibrium micro-dynamic processes during AS efflorescence, revealing four distinct sequential steps at the molecular level. This approach advances beyond conventional methods (e.g., ESEM, H-TDMA) that primarily characterize physical parameters (size, shape), offering unprecedented insights into intermolecular interactions (e.g., hydrogen bond dissociation, ion reconfiguration). The manuscript may be suitable for publication after major revisions and addressing the following concerns.

1. The statement “This study could provide critical insight about redefining atmospheric heterogeneous chemistry.” may be not suitable since little information was provided regarding heterogeneous atmospheric chemistry.
2. How to ensure the accuracy of a 1% RH interval in experiments that is close to the error of a hygrometer?
3. The FTIR measurement is reported to use "a repeat time of 1 scan". This is problematic because FTIR spectroscopy typically requires multiple scans (e.g., 32 or 64) to average out noise and improve SNR. A single scan risks capturing unreliable, noisy spectra, which could distort the identification of subtle spectral changes during phase transitions and may introduce artifacts in the synchronous/asynchronous 2D-IR maps, affecting the precision of transition point determinations.
4. How is the sample particle size determined to be 300nm?
5. The PCMW2D and generalized 2D-IR analyses are central to identifying transition points and molecular sequences, but their reliability is compromised by incomplete data. For instance, the assignment of positive/negative correlation peaks in Fig. 2, references wavenumbers (e.g., 1084 cm⁻¹, 1417 cm⁻¹) that lack contextual spectral data (e.g., how these peaks evolve with RH). Without clear baseline spectra or RH-dependent intensity curves, the interpretation of "convex/concave variations", remains speculative.
6. Is the attribution of infrared peaks based on references? Usually, NH₄⁺ exhibits several infrared absorption peaks around 3000 cm^-1. Why are the NH₄⁺ peaks of the dried sample not obvious around 3000 cm^-1 in this study?
7. How to define complete dryness in experiments? From the infrared spectrum, it appears that there is still a significant amount of H₂O present in the sample.
8. There are many spelling and grammar errors. The issue of capitalization of the first letter. For example, Line 53, Line 57, Line 173, these sentences seem not complete.
9. Line 218: DRH?

The paper proposes a new method for investigating ammonium sulfate (AS) efflorescence using two-dimensional correlation infrared spectroscopy (2D-IR). Coupling this method with FTIR and PCMW2D, the authors attempt to validate the microdynamic mechanisms behind AS efflorescence. Although the method has potential and the topic is timely, the manuscript in its current form falls short of the standards expected for AMT, particularly in terms of methodological detail, validation, and clarity of interpretation. I therefore recommend rejection at this stage. With substantial additional work and restructuring, however, I believe this research could form the basis of a stronger future submission.

First, I want to say that I initially was happy to receive this review, as it is a topic in which I want to deepen my knowledge. The authors would excuse me for the long time I took to properly review their manuscript as I first wanted to be fully familiar with literature. After reading the introduction, I noted the absence of several key references on efflorescence, which makes it difficult for a reader to appreciate the state of the art and the potential contribution of 2D-IR. Including these references and clarifying the recent advances would greatly strengthen the paper. Importantly, because of several vague sentences, the paper often posits ‘old’ state of the art as traditional understanding, without clearly explaining the more recent results. This substantially weakens the introduction. Unlike what is stated, the paper does not provide a kinetic mechanism of AS efflorescence which has been proposed through literature (Onasch 1999, Takahama 2007, Ciobanu 2010, Wang 2017, Xu 2022). This should be clearly stated in introduction. Several sentences are overstated and should be revised for accuracy. For instance: “The traditional understanding assumes that phase transitions are thermodynamically equilibrium,” (L15), “the molecular-scale dynamical processes governing aerosol phase transitions remain hitherto uncharacterized” (L77) should be revised to reflect more accurately the current understanding in the literature. Thus, I would recommend to have an introduction that is in 3 to 4 paragraphs: the first one, presenting the importance of understanding aerosol transition, the 2^nd one on equilibrium and kinetic mechanisms that are currently known, the 3^rd would present the methods that arrive to these conclusions and highlight the current limitation, and a 4^th one could introduce 2D-IR as a promising method that needs to be investigated and validated as done in the paper.

In my opinion, the manuscript oscillates between two positions. Either it is a “method paper”, which aims to demonstrate the value and robustness of an approach (in this case 2D-COS applied to aerosols). Or it is a “process paper”, which seeks to provide new scientific insights into the efflorescence of AS. However, in its current form, it mixes the two approaches without clarifying its angle. Many of the results presented are already known generalities (efflorescence values, qualitative sequence of the process), while the methodological contribution is not sufficiently validated (next point). I recommend that the authors clearly refocus their contribution. In AMT, it seems to me that the methodological contribution is the most relevant: it should therefore be highlighted, demonstrating the reproducibility, validation and advantages of the method compared to existing approaches, rather than claiming to offer a scientific (re)interpretation of efflorescence.

Accordingly, we would expect from a “method paper” to read many details on the method, which currently lacks. In its current format, the paper lacks sufficient detail for reproducibility. To make the method accessible to readers, I suggest considering the following points. But I want to stress that this list is probably not exhaustive, and any detail the authors think would be necessary should be integrated.

1. The paper refers to Wei et al., 2022 for the description of the experimental setup. Where elements of the setup and analysis are literally identical to Wei et al. (2022), a concise reference is acceptable (e.g., ‘atomizer/dryer/DMA layout as in Wei 2022’). However, parameters that are specific to the present study must be reported explicitly here, as they directly affect FTIR intensities, 2D-COS outcomes, and the inferred efflorescence thresholds. For instance, we need details on the 300 nm selection and its distribution, mass/areal loading on ZnSe (and resulting optical thickness), deposition morphology and homogeneity, the exact RH program and dwell strategy during dehumidification
2. No validation tests are presented. It would be important to show, for example, tests on standard salts or blank spectra. Finally, it is absolutely necessary to carry out repeatability tests and to test the method under different conditions. I understand that the comparison with the literature on RH values can be seen as a comparison test, but in my view, this is not sufficient.
3. Regarding section 1.2, the presentation is a little too theoretical and not practical enough. For example, the size and overlap of the window used in PCMW2D are not specified, even though they directly affect the resolution and robustness of the results. Similarly, the description of spectrum pre-processing (baseline correction, noise correction, normalisation) is insufficient to guarantee reproducibility. Finally, no significance criteria are mentioned to distinguish real correlative peaks from noise. These details are necessary if we are to evaluate the robustness of the conclusions drawn from the 2D maps.
4. L146, it is stated that linear baseline corrections and smoothing are performed. Such preprocessing can have major implication on the signal. The paper should clearly state which correction is applied and for which reason. In particular, I think that sensitivity tests should be done to show the impact on the conclusion.

I have some questions regarding the results and discussion. As these sections will likely need to be revised in light of my previous comments, the following comments should not be read as blocking, but rather as points that will likely need to be clarified later on:

1. Section 2.1: The authors restrict their analysis to the regions 1000–1500 and 2500–3550 cm^-1, but do not show the complete spectrum. However, the evolution of other bands (e.g., lattice modes <900 cm^-1, NH4+ bending ≈1680 cm^-1) could provide additional clues about the liquid-solid transition and better support the proposed four-step sequence. I recommend presenting the complete FTIR spectra (before and after pre-treatment) in order to verify the absence of spurious peaks and identify any additional spectral signatures.
2. Typically, one would expect point 5 to be discussed in several sections, including 2.1: for example, does it have an impact on the estimated value of RH? Or when the authors state: ‘Since asynchronous spectra reflect differing rates of spectral changes, the sequence of molecular bond transformations during efflorescence can be deduced as: (1084 cm^-1) > (1097 cm^-1) > (1463 cm^-1) > (1417 cm^-1).’ (L306) How would preprocessing impact this point?

In this way, I would recommend to show the raw and post-processed results.

1. Discussion remains general and mostly hinge on visual observation. The interpretation would benefit from data-based interpretations, using statistical tests, spectrum analysis techniques etc. The values would then be thoroughly compared with literature, allowing for a proper validation of the method
2. I have probably missed one point, but when I look at the Figure 2, I would say that the maximum in correlation occurs at RH = 33 – 34 %. This is below the reported value of (39 ± 0.8) %. Can you clarify this point please? In the same way, I read maxima for the Fig 2B at RH = 32 and 35%. Section 2.2 needs a similar revision.

Finally, I would recommend using more cautious language and not overinterpreting the results. If the method is sufficiently reliable, it should speak for itself, and the overly superlative language disturbed me much more than it convinced me of the method's merits. Here are some examples, but again, it is true for most of the paper.

• “This study could provide critical insight about redefining atmospheric heterogeneous chemistry.” (L87)
• Lines 293-298: "Conversely, three negative cross-peaks […] causing these ions to move closer together." The authors directly interpret the negative cross-peaks as evidence that ammonium and sulphate ions move closer together during water loss. However, in my opinion, a negative cross-peak only indicates that the spectral intensities at the two wavelengths vary in opposite directions with RH. The translation into structural terms (“ions move closer together”) is a plausible hypothesis, but it should be formulated more cautiously and supported by other evidence (e.g., band shifts (section 2.1) or comparison with previous work).
• Similarly, the presentation of the sequence of AS efflorescence (1084 > 1097 > 1463 > 1417 cm^-1) might be too strong. A more appropriate phrasing would be that the spectral variations at 1084 cm^-1 appear earlier in the humidity-driven process than those at 1097 cm^-1, and so on. The physical interpretation of these sequences (e.g. as bond dissociation or ion rearrangements) should remain a hypothesis rather than a demonstrated fact. What the asynchronous 2D-COS actually shows is that spectral variations at 1084 cm^-1 occur earlier in the RH-driven process than those at 1097 cm^-1, and so on. I recommend reformulating in that sense, to avoid over-interpretation.
• Following the latter point, the concluding paragraph of section 2.3 should be revised. The mechanistic details proposed (hydrogen bond dissociation, ions approaching) go beyond what FTIR/2D-COS can directly demonstrate, and should be framed as hypotheses rather than conclusions. The final statement on NH₄⁺ surface enrichment is particularly problematic: this cannot be inferred from the present data and appears to be borrowed from Tian et al. (2011). I recommend the authors either remove this claim or clearly state it as literature context, not as a conclusion of their own work.
• Section 2.4 concludes that the microscopic kinetic evolution of AS efflorescence is elucidated ‘at the molecular level.’ This phrasing is too strong. 2D-COS analysis does reveal sequential spectral changes and can suggest a two-step efflorescence pathway, but it does not directly provide molecular-level kinetics. Such interpretations require careful assumptions and should be stated more cautiously, e.g. as ‘the data are consistent with a multi-step efflorescence mechanism’ rather than as a direct elucidation of molecular dynamics.

More minor mistakes are present along the manuscript such as English wording, capital letters or citation format. Although this is not in itself problematic, these small issues accumulate and could distract readers. Careful proofreading would help improve the overall readability and presentation.

In conclusion, I think this manuscript illustrates the difficulty of writing method-focused papers, which require a careful balance between presenting the technique itself and showing how it is validated. In its present form, the introduction and framing currently do not meet the standards expected for AMT. This, in my view, is less a reflection of the first author’s effort than of the need for closer guidance from the supervisors in positioning the work. With stronger supervision and restructuring, I believe this study could evolve into a much more solid contribution, and I encourage the authors to pursue this line of research.