General Comment

This study investigates the heterogeneous freezing temperature increase at negative pressure with the mW and MLmW water models. Simulations have been carried out at negative pressures of -500 and -1000 atm with water that was in contact with a hydrophilic substrate that promotes ice nucleation. These simulations showed an approximately linear increase in heterogeneous ice nucleation temperature with decreasing pressure. Moreover, water freezing was simulated in water capillary bridges of heights from 3.0 to 1.8 nm. Here, an approximately linear relationship between the capillary bridge width and the heterogeneous ice nucleation temperature was found for unconfined water and water capillary bridges of 3 and 2.4 nm. For capillary bridges of 1.8 nm, an even increased nucleation rate was simulated. Based on these results, a linear relationship between pressure and heterogeneous freezing temperature was derived. This linear relationship was proposed to serve as a basis to estimate the pressure effect on heterogeneous freezing. Moreover, the simulations were used to investigate the location of ice nucleation. It was found that heterogeneous ice nucleation does not occur in the regions within 1.0 nm of the air-water interface.

These are interesting results that are worth publishing in ACP. However, there are weaknesses in the discussion of the results. The ability of the mW and the MLmW water models to describe the pressure dependence of homogeneous and heterogeneous ice nucleation has not been assessed properly. Nevertheless, a parameterization derived from the simulation results was proposed to predict the pressure dependence of freezing temperatures at negative pressure. However, such a recommendation is only justified when the MLmW model is able to describe the pressure dependence of ice nucleation correctly. The comparison to experimental data (Kanno, 1975) reveals that the proposed pressure dependence underpredicts the freezing temperature depression at positive pressure (see specific comments). It should be explained why the proposed pressure dependence should be accurate at negative pressure when the model is not able to describe the pressure dependence at positive pressure correctly. Similarly, the increased nucleation rate in the water capillary bridge is not critically reviewed in view of experiments that show the opposite trend (see e.g. Marcolli, 2014, for a compilation of experiments).

Specific comments

Lines 14–16: “and shows a preference for nucleation in the region just beyond 10 Å”: do you refer here to the distance from the air-water interface or the distance from the substrate? This should be clarified.

Lines 52–55: Here, it is stated that the slope of the freezing temperature as a function of pressure is parallel to the slope of the melting line. However, inspection of Fig. 1 shows that this is not the case. A parallel relationship would only be fulfilled if the enthalpy of fusion and the molar volume difference were independent of temperature.

Figure 1: in Panels c and d, the substrate is only shown below the water bridge. Is this for clarity or is there no substrate above the water bridge? This should be clarified in the figure caption.

Lines 172–175: The surface area of the substrate and the rate at which the system is cooled do not influence J_het it is formulated as a function of surface area and time. It just influences the time it takes to freeze in the simulation. This needs to be clarified.

Lines 201–202: The data shows indeed a slightly non-linear trend. This sentence should be formulated more carefully.

Line 206–208: the values are still within the uncertainty bounds, but the slope is not strong enough. This weakness in the simulation should be commented.

Lines 211–212: “While the linear nature of ΔT/ΔP” is apparent in our results”. This is an exaggeration. The results are in agreement with a linear relationship given the uncertainty bounds. This sentence needs to be adjusted in this sense.

Lines 213–214: Do you refer here to the values given in Table 1 (last line)? If yes, a reference to Table 1 could be given here.

Lines 219–220: Here, it is hypothesized that the thermodynamic properties of mW water are less influenced near the substrate compared to the MLmW model. Couldn’t this be found out by inspecting the simulation?

Lines 221–225: This paragraph is written as if the MLmW model could correctly predict the dependence of freezing temperature as a function of pressure. This assumption needs to be tested by simulating ice nucleation in the positive pressure range and comparing the results to measurements. Such a comparison can be done for homogeneous ice nucleation. See also general comment.

Figure 3: It should be stated whether the dotted line is a fit line or based on the pressure values given in Table 1.

Lines 249–253: The calculation of the Laplace pressure by estimating the contact angle from the simulation is indirect. What is relevant for the Laplace pressure is the radius of the meniscus, which could be directly determined from the simulation. Could this still be done to validate the assumed tension within the capillary bridge?

Figure 5: Reading the figure caption and the text, it seems that Panels a and b show the same simulation viewed in different 2D projections. Yet, the colour scale in the panels are different: in Panel a, it is from 231–234 K and in Panel b, it is from 231–238 K. Is this a mistake? Please explain.

Figure 5b: the air-water interface (red shaded stripes) seems to be too narrow. It should be broader in the projection because the interface is curved. How was the distance from the air-water interface evaluated? Based on the projection or was the actual distance to the interface taken?

Lines 303–305: A higher nucleation rate for pores narrower than 2 nm is in contradiction with DSC experiments performed on slurries of mesoporous silica materials with pores in this size range, for which no freezing peak at all was observed (see e.g. Marcolli, 2014, for a compilation). This should be commented.

Lines 323–325: Here, the simulation results should be critically reviewed in view of the experimental evidence.

Lines 323–327: Here, it is written: “Therefore, the linear approximation can serve as the basis for a straightforward parameterization of the pressure effect.” And: “Essentially, the temperature increase for heterogeneous freezing is determined in large part by the volume difference between liquid and ice.” These two sentences together imply a linear dependence of the volume difference on pressure. Do the authors really want to imply such a linear pressure dependence? It would be interesting to know whether the simulations support such a linear pressure dependence.

Line 328: If the proposed dependence of freezing temperature on pressure is extrapolated to positive pressure, a freezing point depression of 7.3 K would be expected at 1000 atm. Yet, experimental data by Kanno et al. (1975) show that the freezing point depression is already 7 K at 500 atm and increases to 17 K at 1000 atm. Is there any evidence that the simulations are better in predicting pressure dependence for negative than for positive pressure?

Lines 340–341: “Our findings provide additional perspectives to those of Lintunen et al. (2013), who showed a tendency for suppression of ice nucleation in the xylem of vascular plants”. What is meant by this sentence?

Lines 342–343: what is meant here by "significant"? In the order of kPa or in the order of MPa? The order of magnitude is decisive for the impact negative pressure has on the ice nucleation rate and should be mentioned.

Technical comments

Table captions should be above the tables.

References: Journal titles are not abbreviated according to the journal’s guidelines. Also, they are not consistently formatted: Some are with and some without DOIs; some use capital letters in article titles while others do not.

Line 6: There are two ”from”. One should be deleted.

Line 116: “feasibly be achieved”: either just “feasible” or just “be achieved”.

Line 125: the abbreviation“NVT” should be explained.

Line 139– 41: this sentence should be improved.

Line 179: “comparison with Rosky et al.” instead of “comparison from Rosky et al.”

Line 196:  Do you mean Equation (2) instead of Equation (1)?  Moreover, in most parameterizations, the pre-factor “A” is different for homogeneous and heterogeneous ice nucleation.

Lines 210–211: this sentence is incomplete.

Line 276: “a capillary bridge” or “capillary bridges”.

Figure 4: Panel b of this figure is explained only after Fig. 5. The manuscript should be reorganized in a way that the figures are explained in the right sequence.   

Figure 5: The legend and axis numbers and the colour scale numbers are two small and should be increased.

Line 389: “adobpting”: remove the “b”

Line 460: the paper title is not correctly displayed.

References

Kanno, H., Speedy, R. J., and Angell, C. A.: Supercooling of water to 􀀀92_ C under pressure, Science, 189, 880–881, https://doi.org/10.1126/science.189.4206.880, 1975.

Marcolli, C.: Deposition nucleation viewed as homogeneous or immersion freezing in pores and cavities, Atmos. Chem. Phys., 14, 2071–2104, https://doi.org/10.5194/acp-14-2071-2014, 2014.

This manuscript undertakes an investigation into the impact of negative pressure on the heterogeneous nucleation of ice. This study employs molecular simulations with two coarse-grained models of water, mW and ML-mW, in contact with model graphitic surfaces with varying hydrophilicities, yet comparable ice nucleation efficiencies. To this end, the authors present simulations of ice nucleation that apply negative pressures by two distinct means, namely a barostat on a system without a vapor phase and capillary pressure on a liquid-vapor system. The authors observe that the results are consistent within the uncertainty of the simulations. The findings of this study indicate that the pressure dependence of the heterogeneous nucleation temperature at a given nucleation rate is almost the same as that for the homogenous temperature in the same model. The authors explain this coincidence in the slopes through classical nucleation theory, assuming that the only property dependent on temperature and pressure is the chemical potential. In this regard, the interpretation of this study is based on water activity and employs approximations concerning the temperature and pressure dependence, which may not accurately elucidate the positive pressure side of the freezing line.

The topic addressed in this paper is of significant importance. However, I have observed that the conditions of the simulations are not consistently and adequately defined, and the discussion and conclusions contain unwarranted generalizations. Consequently, I am of the opinion that a revised manuscript could significantly enhance the presentation, analysis, and discussion, and result in an excellent paper. Thus, I recommend that the authors address the questions and issues raised in what follows. I have addressed them in the order they appear in the text.

• I would like to bring to the attention of the authors that the use of the term "density anomaly" by them to describe the negative slope of the melting line, dTm/dp)coexistence, is not appropriate. The density anomaly of water pertains to the non-monotonic relationship between the density of the liquid and temperature. Thus, it would be more appropriate for the authors to refer to dTm/dp)coexistence < 0 as the negative slope of the melting line.
• Equation 1 shows that Thom and Tmelt are parallel, but it is important to acknowledge in the introduction and discussion of the paper that this is not generally the case in experiments or simulations. The narrow range of validity of equation 1 is evident in the steepest slope of Thom(p) compared to Tm(p) at positive pressures in both experiments (Kanno et al., 1975) and simulations for mW (Lu et al., 2016), anTIP4P/Ice (Bianco et al., 2021) and ML-BOP (Dhabal et al., 2022). The authors should clarify in the manuscript that equation 1 is not applicable across all pressure ranges. This is due to the approximations employed to derive equation 1, which should be explicitly discussed in the paper. Importantly, equation 1 assumes that pressure and temperature only impact the chemical potential. The approximation that the ice-liquid surface tension is independent of pressure is reasonable for negative pressures, but not valid at positive pressures (Montero de Hijes et al., 2023). It should be noted that even the heat of fusion and the change in volume upon melting are dependent on pressure (Dhabal et al., 2022). The authors may alleviate the issues they encounter in Section 3.1, where the predicted and computed slopes of deltaT/deltap do not match, by incorporating this dependence.
• The authors appear to be unaware that the melting and homogeneous nucleation lines of mW at pressures ranging from under -2000 atm to over 10000 atm were previously reported and discussed in Lu et al. (2016) “Relationship between the line of density anomaly and the lines of melting, crystallization, cavitation, and liquid spinodal in coarse-grained water models.” The results for mW demonstrate that upon increasing pressure, the slope of Thom is steeper than that of Tm - consistent with the experimental results of Kanno et al (1975). The paper by Lu et al. should be cited when referencing previous simulations of the pressure dependence of freezing and melting in simulations and mW in particular. Additionally, the authors should be aware that equation 1 is not valid for all pressures.
• In line 68, the contact angle of mW water on the graphite surface of this study is reported as 86°. It may be more appropriate to refer to these surfaces as "ice nucleating" rather than as "hydrophilic substrates." If the hydrophilicity of the substrate plays a role in obtaining negative pressures in the capillary configuration, it is unclear why the authors chose a surface with a contact angle of almost 90°.
• It should be noted that the correct name of the ML-mW model contains a dash between "ML" and "mW," and this should be corrected throughout the text.
• The methods section of the manuscript lacks important information and is difficult to follow. The following points should be addressed:

i. In Figure 1, the authors label (a) as "unconfined" and (b) as "confined." However, since both scenarios are periodic, they appear to be the same slab of liquid in contact with IN surfaces on the two boundaries of the slab. The authors should clarify how they handle the periodic boundary conditions for these cells to explain why they are different.

ii. The pressure for the supercooling referred to in line 83 and the cooling simulations should be explicitly stated.

iii. The procedure to identify ice using OP seems to be the same as in Rosky et al. 2022, where about a third of the water molecules are identified as ice before crystallization. However, this data is not provided in the current manuscript, and the authors should clarify the identification process and provide the data.

iv. The procedure to determine the freezing temperature from the q6(T) of Rosky et al. 2022 corresponds to the nucleation and growth, not just nucleation. The authors should clarify this because the growth rate of ice is expected to decrease with extension, as the liquid is more tetrahedral.

v .The authors use the range of the interaction potential to explain the small size of the cell, but they should also consider the length scale of the structural correlations in the liquid. These correlations decay in about 1 nm, suggesting that water in cells with a liquid column of 2 nm or less is dominated by interfacial phenomena and should not be a good representation of larger systems. The authors should discuss the implications of these small sizes and consider adding a simulation of a larger system.

vi Regarding the change in slope of the melting line, Lu et al. JPC 2016 show that for mW cavitation is reached before the extension that makes the liquid less dense than ice.

vii. The manuscript is confusing and inaccurate in describing the ensemble of the simulations and the way pressure and temperature are controlled. The manuscript states that the simulations are done in the NPH ensemble with a Nose-Hoover thermostat to make it NPT, but the input file indicates that the thermostat used is the one from the canonical ensemble by velocity rescaling of Bussi et al. 2007, and the barostat is Berendsen's for equilibration and then Nose-Hoover for the collection run:

fix             2 water nve

fix             3 water temp/csvr ${TEMP} ${TEMP} 500.0 ${SEED}

fix             4 water press/berendsen iso ${PRES} ${PRES} 1000.0 modulus 20000

fix             2 water nph iso ${PRES} ${PRES} ${PCOUPL}

fix             3 water temp/csvr ${TEMP} ${END_TEMP} ${TCOUPL} ${SEED}

The authors should correctly describe the ensemble (NPT), and what are the actual thermostat and barostat they used and their damping constants. The use of isotropic control of the pressure may bias the growth of ice they are using to determine the freezing temperature and result in the relatively large dispersion of the freezing temperatures observed in this work (it may also result in hindrance of complete crystallization at low temperatures, as seen in Rosky et al 2022).  

viii. What cooling rate was used in the simulations? Was it the same for both models?

ix. Line 97 states that "the substrate molecules are held fixed with zero velocity". However, the authors should be aware that when the cell expands isotropically at negative pressure, the substrate will expand concomitantly (there are no forces keeping the substrate atoms together), resulting in a change of the ice nucleation properties of the surface. To avoid these issues, the authors should ensure that the graphite surface is rigid, not fixed (although LAMMPS does not like to evolve rigid periodic bodies!) or that they change the pressure by removing water molecules at constant volume rather than changing the dimensions of the cell.

x. Could the authors please explain how they achieved the same water-substrate area, given that it depends on the contact angle of water on the surface and the height of the water capillary? Did they tune the height of the cell or add/remove water molecules?

xi. Why was an ice cluster size of 25 molecules selected for sampling their positions? Is this the expected size of the critical nuclei at the conditions of the simulations?

xii. Lines 134-137 indicate that squares and diamonds will be used for the two types of configurations, but Figure 2 only shows circles. What type of simulation cells were used for Figure 2? This information is not included in the caption.

xiii. Can the authors explain why the uncertainties in Thet are much larger for ML-mW than for mW?

xiv. Line 143 states again that the carbon of Lupi et al. is hydrophilic to mW, when it is essentially neutral (contact angle 86, which is not indicated until line 166). The contact angle should be indicated in this line 143 so that readers can judge how hydrophilic it is. Why was the carbon surface tuned to have a much lower contact angle of ~50o with ML-mW?

Results and discussion

• Line 174 “larger substrate area … would decrease the observed intensive heterogeneous nucleation rate” is probably wrong, as the nucleation rate is already normalized by the area.
• Lines 183-185 “Most significantly, we observe that the increase in temperature as a function of pressure for jhet is linear to within the sampling uncertainty, indicating that the use of a linear approximation for ∆T /∆P is appropriate for heterogeneous ice nucleation.” This conclusion is not in agreement with experiments of pressure dependence of heterogeneous nucleation. For example, it has been shown that the pressure dependence of ice nucleation on many potent organic crystals IN is milder than for the melting line, resulting in a merging of the melting and freezing line at high pressures [Evans 1967]. The authors should refrain from generalizing about pressure dependence of heterogeneous and homogeneous nucleation from the small range of pressures and nucleating surfaces covered in their simulations. It would be more appropriate to discuss which factors may explain that the heterogeneous nucleation line is parallel to the homogeneous and melting lines at negative pressures in the simulations, and to which extent it can be expected that these results hold for ice nucleation with other substrates.
• Line 189, again improper use of “water density anomaly” replace by “negative slope of the melting line” or “higher density of the liquid respect to ice”
• Lines 212-222, the argument that the values of Tm, enthalpy of fusion and change in molar volume are ambiguous for heterogeneous nucleation does not make sense to me. In the framework of CNT used in this manuscript, these values are those of the bulk phase and the role of the interface becomes apparent only in the surface tensions and their temperature and pressure dependence. Those derivatives, dg/dT and dg/dp are the ones that the authors should focus on when addressing why the analyses that assume them to be zero do not provide a quatitative agreement with the data. The temperature dependence of the various surface tensions involved in the nucleation of ice at the mW-graphite interface have been discussed in Qiu et al. JPC B 2018 wonder whether the differences they see for mW and ML-mW are not rooted on the difference in hydrophilicity of the carbon-like surfaces used in the two sets of simulations. The results and discussion in this Qiu and Molinero 2018 paper may help address that issue.
• Last paragraph of section 3.1, regarding the changes in enthalpy of fusion and difference in molar volume, it is important that the authors first perform the correction of these values with p and T [in experiment, as well as in ML-BOP and TIP4P/2005 these quantities have considerable slope, see figure 3 of Dhabal et al. JPC B 2022 op cit above], and if that does not explain the results consider the change in the surface free energies, which is where all the effect of the surfaces is in the formalism they adopted.
• Line 235, eq 3 and eq 1 do not consider heterogeneous ice nucleation, why would their combination in eq. 4 account for heterogeneous nucleation?
• Line 238 “given the previous conclusion that terms sigma_lv and theta do not change significantly with pressure”: that was not a conclusion but an assumption, because there was not data presented for either of these quantities as a function of pressure. The sentence must be edited to reflect that it is not a conclusion but an assumption or inference. It is known, however, that the surface tensions change with temperature [Qiu et al. JPC B 2018 presents data for mW] and the authors could account for that instead of using values at 298 K.
• When reporting that the 18 angstrom capillary setup has a considerable increase in the nucleation rate as a result of the confined geometry
• A central finding in this study is that the heterogeneous nucleation temperature is rather insensitive to pressure in the range of negative pressures (probably because the surface tension is also relatively insensitive to pressure in this range).  
• The first paragraph of section 3.3: when preparing the water-filled cells with height 1.8, 2.4 and 3 nm, what are the pressures at which they are evolved? The Laplace pressure that you deduce for the same height capillaries in the previous simulations? This is not clear in the text, please add detail.
• Line 266: “unconfined” configuration does not seem to be less confined than the other slabs – please explain clearly where is the lack of confinement in that cell; I do not see it.
• I understand the increase in ice nucleation for the 1.8 nm water slab cell is due to concurrent help of the nucleation surfaces, as explained in Hussain, Sarwar, and Amir Haji-Akbari. "Role of nanoscale interfacial proximity in contact freezing in water." Journal of the American Chemical Society 143.5 (2021): 2272-2284. I recommend the authors to cite that manuscript if that is the phenomenon they are observing.
• End of section 3.3 “Other research (Elliott, 2021) supports that capillary theory can extend to the nano-scale used in our simulations, which our results corroborate. Meanwhile, our results are also consistent with Almeida et al. (2021), who indicate that the capillary theory breaks down with separations less than ≈ 20” . I do not see where you corroborate the validity of capillary theory to the nanoscale nor where do you show that capillary theory breaks down below 2 nm (ice nucleation in confinement does not defy capillary theory). Please make explicit your evidences and arguments in this discussion.
• Lines 284-5: aren’t the capillaries too small to conclude that there is a statistically significance preference for ice nucleation between 2 and 2.5 nm from the air-water interface? Please clarify what are the sizes of the capillaries you analyze to reach that conclusion, as I do not find it justified. They seem to be influenced by finite size effects.
• In discussing whether ice forms or not at the air-water interface, the authors may want to take into account that premelting of water at the ice-vapor interface rules out the existence of heterogeneous nucleation of ice at the water-vapor interface (because premelting and heterogeneous nucleation require the opposite sign of ice binding free energies, as discussed in Qiu Y, Molinero V. Why is it so difficult to identify the onset of ice premelting?. The journal of physical chemistry letters. 2018 Aug 27;9(17):5179-82.
• In the conclusions section, make sure you do not generalize your results as a pressure parameterization beyond the regime that you measure, and I suggest incorporating into the discussion the role of the change in surface tension with pressure (at least the one for water-ice, reported recently for TIP4P/2005 by Montero de Hijes et al. JCP 2023), as otherwise you run against an experimental body of evidence that shows that the temperature of heterogeneous nucleation is not necessarily parallel to either the melting or homogeneous nucleation lines [see the papers by Evans cited above].
• The changes in freezing temperature upon extension seem quite modest to me. Considering that water at negative pressure is doubly metastable with respect to ice and vapor, then to which extent the extension of supercooled water is able to promote nucleation in time scales that are short compared to cavitation?
• Lines 345-346 “Conversely, imposing isochoric conditions has been shown to greatly increase the stability of supercooled water so that it can be used for cryopreservation (Powell-Palm et al., 2020) – That paper refers to the stability with respect to cavitation, not crystallization. I do not see the relevance of this sentence regarding stability against cavitation in the context of what is being discussed in that paragraph… but if you think it is important, clarify that it refers to stability with respect to cavitation.
• Finally, the model that the authors use for the analysis is based on the dependence of the excess chemical potential of water with respect to ice as a function of pressure and temperature, expressed in the equations of CNT. That has similarities to the water activity approaches, such as the one of Knopf and Alpert cited in the manuscript. It would be important the the authors elaborate on the connection of theirs and Knopf and Alpert approach, adn whether they are equivalent.  

References not listed fully above (and not in the manuscript I am reviewing):

Bianco et al. PRL 2021 cited in the manuscript

Dhabal D, Sankaranarayanan SK, Molinero V. Stability and Metastability of Liquid water in a Machine-learned Coarse-grained Model with Short-range Interactions. The Journal of Physical Chemistry B. 2022 126(47):9881-92].

Evans LF. Two-dimensional nucleation of ice. Nature. 1967 Jan 28;213(5074):384-5;

Evans LF. Ice nucleation under pressure and in salt solution. Transactions of the Faraday Society. 1967;63:3060-71].

Kanno, H., Speedy, R.J. and Angell, C.A., 1975. Supercooling of water to-92 C under pressure. Science, 189(4206), pp.880-881)

Lu, J., Chakravarty, C. and Molinero, V., 2016. Relationship between the line of density anomaly and the lines of melting, crystallization, cavitation, and liquid spinodal in coarse-grained water models. The Journal of Chemical Physics, 144(23), p.234507], anTIP4P/Ice

Qiu Y, Lupi L, Molinero V. Is water at the graphite interface vapor-like or ice-like?. The Journal of Physical Chemistry B. 2018 Jan 3;122(13):3626-34.