Review of “The global ocean mixed layer depth derived from an energy approach” by Moreles et al.

Review by Brandon Reichl

Summary

In this manuscript the authors propose to define ocean surface mixed layer depth by computing the work required to move a water parcel from the mixed layer depth against gravity (buoyancy work, or WB in the manuscript).  The authors argue that this WB approach is advantageous to a density threshold method because it links to physical quantities and dynamical forces in the ocean boundary layer.  This work then proposes a value for the integrated buoyancy work that it argues yields accurate estimates of the MLD throughout the Pacific Ocean.  The resulting MLD from WB is then compared to a subset of other existing MLD estimates in certain (“challenging”) regions, and finally a new MLD climatology is analyzed and discussed.

The MLD is not an objective quantity, it requires defining timescales and spatial scales since the ocean surface boundary layer is under consistent and variable external forcing.  Furthermore, identifying a mixed layer invokes some qualitative analysis to quantify what is meant by “mixed”.  This ambiguity makes the present goal of deriving a “global ocean” mixed layer depth challenging, and I acknowledge the efforts the authors have devoted to this matter.  I find the proposed WB method for estimating MLD is potentially interesting, but the paper presently relies heavily on ad-hoc and empirical arguments.  This limitation makes it difficult to judge the value of the WB approach versus other approaches.  The study would therefore benefit significantly if it can identify quantifiable metrics to bolster its claims.

The desire for a MLD metric led to proposing PE anomaly in the Reichl et al. (2022) analysis of MLDs, as it quantifies the energetic distance of a column of sea water from being well mixed.  This naturally leads to the PE anomaly as a possible basis for identifying the MLD, but it is not obvious that the same energetic distance should define the MLD in all regions or on all timescales.  WB itself may provide another interesting metric for quantifying mixed layers, but it differs in important ways from the PE anomaly.  WB provides an integrated measure of stratification of the column by considering the displacement of a particle from the mixed layer base.  This yields some insight into the stratification, but less information than if you evaluated the buoyancy work associated with displacement of all particles within the mixed layer.  It is also not obvious that a single WB quantity should define the MLD at all locations and on all timescales.

The WB method may offer some physical insights into when and why different MLD methods differ, and it is closely related to the threshold method (see my 2nd comment under "Other Comments") such that it may better ground the threshold values used in present studies.   My overall opinion of this article is that there is potential to provide an interesting perspective on MLD identification in the ocean based on these methods, but presently the gaps in metrics and presentation are significant, as detailed below. 

Major concerns

1. The WB method for estimating MLD has merit over a density threshold method since it invokes a dynamical quantity.  However, I am unsure that this dynamical quantity truly addresses two main shortcomings of the threshold method.  It would help if this paper better identified what it does and doesn’t improve upon other methods.
   • WB does not offer any physical guidance for choosing a threshold value, so the threshold remains ad-hoc.  The paper argues that 20 J/m3 is a universally applicable value, but this was derived empirically based on arguments about its vertical gradient over limited regions of the ocean.  There is no physical significance offered for the integrated buoyancy work of 20 J/m3, which would justify it from first principles for identifying the upper ocean mixed layer in all seasons and locations.
   • The new method is still sensitive to the details of the choice of the threshold value and the reference depth.  Interestingly though, some of this sensitivity is reduced since WB is an integrated quantity and therefore less responsive to noise in a profile.
2. I did not agree with the claim in the text: “There is a correspondence between our methodology and that of Reichl et al. (2022), suggesting that our energy-based methodology is consistent with the turbulence approach of the mixed layer formation”.  I do not find the correspondence between the WB and PE anomaly to be obvious, other than both using energy based criteria. PE anomaly is a column integrated energy value that quantifies the distance of the column from being perfectly homogenous, hence it has units of J/m2.  WB only considers the energetics of a single parcel advected through the column, hence it has units of J/m3.  One could construct different idealized profiles that give the same WB MLD yet have different PE anomalies, which was identified as a shortcoming of other MLD methods in Reichl et al. 2022.  Perhaps the WB method has less PE anomaly sensitivity than other methods, but an evaluation of WB in terms of PE anomaly was not attempted in this paper.  These important differences from the PE anomaly do not support the statement that this method connects to boundary layer turbulence in the same way as argued for PE anomaly.
3. The article claims the WB MLD with an energy value of 20 J/m3 is “accurate, robust, and of global applicability”.  This claim is based on looking at “challenging regions”, which are defined where a suite of existing methods disagree with each other in MLD magnitude.  One issue is that this approach appears to weight the analysis to deep MLD regions (usually convective regions), but this appears to deemphasize shallow MLD regions (e.g., the Arctic Ocean (more on this below) and summer time mixed layers in biologically productive regions) that are just as valuable.  Furthermore, I did not find a convincing and quantitative argument in section 3.2.2 for why the WB method estimates a better and/or more consistent MLD than other methods in these regions; it mostly relies on ad-hoc arguments.
4. I found the analysis of the climatology lacked a significant new/novel result that advances beyond previous work on mixed layer climatologies.  It would be useful if issues in previous climatologies could be identified and to discuss why the WB method was able to provide a more meaningful estimate of a MLD climatology (or for what contexts it may be more meaningful).
5. The article states that it offers globally applicable mixed layer depths and provides a mixed layer depth climatology.  Constructing a gridded mixed layer depth climatology requires many decisions, and little technical detail on how this is done was provided.  Nor is the resulting climatology data made available, which would severely limit any potential impacts of this work.  The climatology is produced only using Argo data, which neglects a lot of additional oceanic profile data that exists.  This also leads to coastal oceans and the entire Arctic Ocean being absent from this work.

Other Comments

1. What reference pressure is used to define the potential density in equation 3?  Can a fixed reference pressure be used as a suitable approximation?
2. One can rewrite the WB criteria (equation 3, by rewriting the 2nd terms RHS w/ H defined as the MLD and _Hmean defined as the depth integral mean of potential density over the MLD):  WB =  g*H*[_Hmean - rho_ref], which is now expressed similarly to the threshold method: delta = [rho(z) - rho_ref].  This makes two notable differences of WB from the threshold method more apparent:  (1) the density difference is now from the average of the density over the column instead of at the MLD, and (2) the density difference is effectively weighted by the MLD (and gravity).  These have some interesting implications: (1) integrating the potential density makes the MLD less sensitive to noise in the profile, and (2) weighting the threshold by the MLD reduces the depth of deeper MLDs with the same energy value.  The first effect seems advantageous for practical use.  The second effect makes sense from the perspective that it takes more energy to raise a parcel from a deeper depth, but since deeper MLDs often experience more turbulence and mixing, it is not straightforward to me that the second effect is obviously “better” for MLD identification.  The ocean does not experience uniform levels of energy inputs to turbulence.  (This is a main reason I am not convinced there should be a single universal energy value for either the WB method or the PE anomaly method.)  Furthermore, the 2nd point above about MLD weighting also offers an interpretation of why shallower depths are associated with larger density differences, e.g. Figure 7.
3. L336:  “It is also easy to implement numerically.” < Easy compared to what?

Review of “The global ocean mixed layer depth derived from an energy approach” by Moreles et al.

The mixed layer is an important oceanographic parameter, playing a significant role in understanding upper-ocean dynamics and air-sea interactions. Therefore, accurately calculating the mixed layer depth (MLD) is crucial. Over time, many researchers have proposed various methods to estimate the MLD, which can generally be categorized into three types: threshold methods, energy-based methods, and geometric shape methods. However, due to the very nature of the mixed layer, there is no perfect method. How can we quantitatively define "mixing"? It always requires some reference values, and the use of such reference values inherently leads to spatial or temporal dependence in the applicability of different methods.

This work approaches the problem from an energy perspective, proposing a new method for calculating MLD based on the amount of buoyancy work. The authors demonstrate through practical applications that this method performs reasonably well. Overall, I find this to be a very interesting study. It not only helps us better understand the mixed layer, but also provides an additional option for calculating its depth. However, I have several comments as follows:

• I believe the authors may have overstated the performance of their proposed method. In the abstract, they claim that this method provides “a robust criterion based on physical principles.” However, it should be noted that: 1) The authors still use a threshold value (20 J/m³) as the criterion for defining the mixed layer. This value is derived only from a few observational sections, and whether it is applicable globally remains questionable. 2) The authors’ evaluation of “good” or “bad” performance seems to focus on regions where traditional methods do not perform well. Is this method better across all seasons and global ocean regions? In areas where density profiles change gradually, the MLD itself is inherently ambiguous—how should a “good” standard be defined in such cases? 3) The authors mention in the introduction that “in regions with vertically compensated layers, the density threshold may overestimate the MLD.” Can the proposed method in this paper avoid this issue? Considering that the method is still based on density, it seems unlikely that this problem can be completely avoided.
• Although the authors express the buoyancy work integral in the form of Equation 3, in essence, this equation is the depth integration of density anomalies. This means the method still heavily depends on the choice of threshold value—especially in summer with shallow mixed layers when density increases slowly with depth. In such cases, different thresholds could lead to significantly different results. I recommend the authors conduct a deeper discussion and analysis of the limitations of their method, rather than focusing solely on its advantages.
• Although there is no universally accepted standard method for determining MLD, there is a parameter that can reflect the effectiveness of a given method to some extent—the Quality Index (https://doi.org/10.1029/2003JC002157). I suggest the authors consider using this parameter to evaluate the performance of their method.