Review of “Lagrangian particle-based simulation of aerosol-dependent vertical variation of cloud microphysics in a laboratory convection cloud chamber”

This paper presents a computational investigation of cloud droplet formation and growth in a 2-meter-tall convection chamber. A unique aspect of the work is the use of Lagrangian microphysics, which allows the time history of droplets to be investigated. Some of the results are intriguing and overall the work appears to be rigorous and technically correct (with one exception described below). The connections to atmospheric processes are somewhat tenuous, so it seems the paper would be more suitable for AMT than for ACP. To be published in ACP those connections should be strengthened.

The main criticism is regarding the way some of the results are discussed and interpreted. In multiple places in the manuscript the wording suggests that supersaturation builds up during ascent. This has the potential to be very confusing because some readers may associate this with the familiar increase of supersaturation with height in a convective cloud. For example, the explanation of increasing q_c with height being attributed to “active droplet activation and condensational growth during ascent” (lines 198-199) does not make sense. Symmetry suggests that the same argument should work for plumes descending from the top surface. A cold plume mixed into a warm background has nearly the same potential to generate supersaturation as a warm plume mixed into a cold background (see multiple previous papers showing calculations and simulation results for convection-cloud chambers… usually the supersaturation profile is nearly constant with height, showing no significant bias toward the bottom or top surface). In contrast, arguments that appear later in the paper (such as on lines 380-382) make much more sense in light of the results shown. I would encourage the authors to revise the language in other parts of the paper that give the potentially misleading impression that droplet growth is tied to vertical ascent. The peak near normalized vertical displacement of negative 0.25, suggests that plumes that are efficiently mixed produce the strongest supersaturation (as opposed to a plume that simply travels upward without strong mixing). Supersaturation generation in a convection-cloud chamber is the result of mixing, not of ascent. That mixing may have a link to plume propagation distance and therefore to distance from the top or bottom boundaries, but it is not the ascent itself that is the source of supersaturation.

Other important points to be addressed are:

What is the fundamental problem statement or hypothesis underlying the investigation? For example, on lines 58-60 the direction of this investigation is stated, but it is not clear why this topic would be of interest to explore.

A “free-slip” boundary condition at the top and bottom surfaces (line 106) is unphysical and may fundamentally alter the nature of the flow. Can this be justified as having negligible effect on the microphysical problem investigated in this study? If so, please provide clear evidence. If not, please clearly state this limitation in the abstract and provide a discussion of how the conclusions will change.

In multiple places in the manuscript it is pointed out that mean and fluctuations of supersaturation are reduced as cloud droplet concentration is increased. Suppression of supersaturation for shorter phase relaxation time has a clear theoretical interpretation; for example, see Equations 12 and 13 in Chandrakar et al. (Journal of the Atmospheric Sciences, 2018, “Influence of Turbulent Fluctuations on Cloud Droplet Size Dispersion and Aerosol Indirect Effects”; note that  in that paper is the phase relaxation time).

There are also multiple places in the manuscript that would be more clearly interpreted in terms of the quasi-steady supersaturation. For example, on line 322, the statement that condensation causes “rapid vapor depletion… before S can develop” does not make sense. Without supersaturation, there is no vapor depletion. I suppose what is meant is the analog to quasi-steady supersaturation, which is the result of two rates: the rate at which supersaturation is produced versus the rate at which it is consumed. So the low supersaturation observed is simply a result of faster consumption by droplet growth (due to shorter phase relaxation time) for an unchanged rate of production. This is not a surprising result. Another example is lines 218-219: There the concept could be made clearer by drawing an analogy with the quasi-steady supersaturation in a convective cloud. For equivalent forcing, such as updraft strength, smaller phase relaxation time leads to lower quasi-steady supersaturation.

Figure 5 shows large oscillations in the mean supersaturation with height near the top and bottom boundaries. What is the source of this numerical instability? The concern is that the oscillations could strongly influence the correlation with vertical air speed, which is an important focus point in this investigation. This needs to be addressed and its influence on the w’-s’ correlation needs to be checked.

Specific comments

Lines 102-105: In one sentence the “sidewall temperatures” are stated, but in the next line it is stated that the model is configured with “periodic lateral boundaries”.

Lines 112-114: How significant are droplet losses to the sidewalls compared to the bottom surface?

Lines 157-158: What is the reason for the arbitrary use of 1 micrometer as a cutoff between haze and cloud droplets? For the broad aerosol size distributions used in this study, this can be very different than the true activation radii. An advantage of Lagrangian microphysics is that the aerosol properties are known for each super-droplet, so the boundary between haze and cloud can be determined for each super-droplet. Please explain whether this simplification has any significant consequences for the interpretation of results.

Line 188: It’s not incorrect, but it seems a little strange to use “altitude” instead of “height”.

Line 194: It isn’t clear to me whether these refer to averages over horizontal planes at 0.3 m and 1.7 m, or to averages over layers (e.g., from 0 to 0.3 m and from 1.7 to 2.0 m). Also, is there any particular reason for choosing the value of 30 cm?

Figure 3 caption: For the benefit of those reading the paper quickly, it would be helpful to provide a qualitative description of  within the caption.

Line 229: It is not clear what is meant by the “largest aerosol mode”.

Figure 5 caption: Clarify that the vertical profiles are for the horizontally-averaged supersaturation. Also, are the histograms for supersaturations within the full volume, or a subset of the chamber volume?

Line 265: Should be “high aerosol concentration”.

Line 267: Should be “The physical explanation…”.

Lines 281-283: The “rapid equilibration” argument makes sense, if by that it means that the supersaturation is rapidly depleted. It is unclear what is meant by “droplets complete their growth before experiencing the full extent of vertical S variability”. Does it mean that the supersaturation is depleted after relatively short ascent, such that droplet growth ceases above some level? As written, this argument is too vague.

Line 314: The definition “the timescale over which S environment evolves” is ambiguous. One could also say that the phase relaxation time is the characteristic time for the supersaturation to evolve (due to droplet growth). I assume what is meant is that it is the timescale on which the supersaturation varies due to turbulent mixing.

Line 316: The units are for a velocity standard deviation, not a velocity variance. Please correct either the wording or the units.

Line 359: The statement that “sustained upward motion enhances droplet growth by exposing SDs to regions of higher s” is inconsistent with the results shown. For most of the simulated cases, a peak occurs at a negative value of normalized vertical displacement, which suggests the opposite of what is stated. Only in the two cleanest cases is the mean growth associated with positive vertical displacement.

Line 388: Should be “confinement of the S production zone”.

Lines 403-406: The two statements that “activation fraction generally increases with normalized vertical displacement” and “it peaks around a normalized displacement of approximately -0.25” are inconsistent. There is an initial increase, but over most of the range of normalized vertical displacement the activation fraction decreases or is only weakly changing.

Lines 408-414: This discussion is not clear.

Figure 14: Wouldn’t it be more insightful to show the spatial locations of where activation occurred, rather than the locations of droplets that were activated within the last 20 seconds, which is sufficient time that they can be transported over the maximum dimension of the chamber? This seems like a missed opportunity to gain deeper understanding of what processes are controlling activation.

Lines 456 and 463: After reading the paper and looking at the evidence, I disagree with the statements that “droplets experienced sustained condensational growth during ascent” and “droplet growth (dr) and activation strongly correlated with upward displacement”.

The manuscript examines how aerosol loading and vertical transport jointly shape cloud microphysical structure in a turbulent convection chamber. The simulations are conducted using large-eddy simulations coupled with a Lagrangian super-droplet model, and the main findings focus on mean vertical profiles of liquid water content within the chamber. The results indicate that cloud water generally increases with height due to continued droplet activation and growth during ascent. However, this vertical gradient weakens substantially under polluted conditions, where enhanced competition for water vapor suppresses supersaturation variability and leads to more vertically uniform cloud water profiles. These findings underscore the role of aerosol loading in controlling vertical cloud microphysics and emphasize the coupled effects of vapor competition and turbulent vertical dynamics, with potential implications for aerosol–cloud interaction parameterizations in both laboratory and atmospheric contexts.

While the topic of the manuscript is highly interesting and detailed modeling is indeed required to understand the processes governing droplet formation in cloud chambers, I have significant reservations regarding both the content and the conclusions drawn. Consequently, I cannot recommend acceptance of the manuscript in its current form. The analysis is highly technical and limited to a single experimental configuration intended to mimic a specific chamber setup. However, I do not find sufficient scientific novelty in the results when compared to previous studies using the same modeling framework or to the established understanding of how aerosol concentration controls supersaturation. In this respect, the manuscript may be more suitable for a journal with an instrumental or methodological focus, such as Atmospheric Measurement Techniques or a similar outlet.

I also agree with the first reviewer regarding issues with terminology. Although I am not an expert in cloud chamber experiments, I find the discussion of updrafts to be potentially misleading. The manuscript explicitly states that “the positive correlation between supersaturation (S) and vertical velocity (W) in the chamber arises not from adiabatic cooling driven by the updraft itself, but rather from the mixing of air volumes with different thermodynamic properties originating from the lower and upper boundaries.” Given that the dynamical processes in the chamber differ substantially from those in real atmospheric clouds, the interpretation of droplet activation in terms of updrafts at different altitudes appears questionable. If activation is primarily driven by mixing, one would expect similar effects to occur in downdrafts as well, which is not addressed in the discussion

Some specific comments:

Lines 194–195: “The denominator is the mean of qc at both levels, where active cloud formation occurs during the quasi-equilibrium period.” Is droplet activation assumed to occur only near the top and bottom of the chamber? If so, what is the physical justification for this assumption? Given the turbulent nature of the chamber, mixing should occur throughout the domain, and activation would therefore not be limited to only two vertical levels.

Lines 216–218: “…the number of droplets increases, leading to stronger competition for available water vapor. As a result, each droplet grows more quickly, consuming vapor rapidly… This rapid vapor depletion suppresses the buildup of S during ascent, thereby limiting the vertical increase in qc.” This description appears inconsistent. Individual droplets should grow more slowly when supersaturation is reduced, even though the total condensational growth rate (and thus qc) may increase due to a higher number of droplets. Please rephrase to clearly distinguish between individual droplet growth and bulk condensational growth.

Figure 3: How do the mean droplet size and droplet number concentration vary with height in the chamber? Is it possible that the more vertically uniform qc profiles arise from changes in supersaturation as a function of height and its interaction with the aerosol distribution? Because the chamber top is colder, condensation rates should be reduced, potentially facilitating more efficient activation and higher droplet number concentrations. As aerosol concentration increases, critical supersaturation increases and small variations in become less important, which may naturally lead to weaker vertical gradients in qc.

Figure 5: The manuscript repeatedly states that supersaturation fluctuations are maintained by mixing of air parcels. However, from basic thermodynamics, mixing two supersaturated air parcels at different temperatures should still yield supersaturated air. Since all boundaries in the model domain are supersaturated with respect to water, what mechanism produces negative supersaturation values in the simulation? Additionally, what causes the strong fluctuations in mean S near the top and bottom boundaries?

Lines 231–232: “In contrast, because our size distribution spans multiple modes, s̅ does not collapse exactly to one number but instead asymptotes to a narrow range just above the largest-mode critical S (∼0.02%).” This explanation is difficult to justify physically. The close correspondence between s̅ and the largest-mode critical supersaturation may be coincidental rather than mechanistically constrained.

Lines 234–236: Can this hypothesis be tested by explicitly accounting for water uptake in the aerosol phase? What role does water availability from the chamber walls play, and could it contribute to the apparent stagnation behavior?

Lines 264–265: “Downward motions near the upper boundary carry cooler and drier air down into the chamber, generating negative S perturbations.” According to the model setup, the upper boundary is at 100% relative humidity. If mixing is the dominant process affecting temperature and moisture, why do negative supersaturation values form?

Figure 10 and related analysis: The main message of this figure is unclear. Please explain more explicitly how this analysis supports the manuscript’s conclusions. Why is the analysis restricted to particles initially located near the bottom of the chamber rather than applied to all particles?

Lines 363–364: “Suggesting that condensational growth becomes increasingly decoupled from vertical motion due to limited S variability under polluted conditions.” Or simply because there is more particles to use the same amount of water that is limited by the transport rate from the walls, and that’s why the relative growth is less.