Peer review of: Deglacial water-table decline in Southern California recorded by noble gas isotopes (2019)

Reviewers' comments: 
 
Reviewer #1 (Remarks to the Author): 
 
Review by Werner Aeschbach 
 
Summary 
 
The authors presents a comprehensive study of the potential of high-precision noble gas isotope 
measurements in groundwater for the reconstruction of past water-table depths. This to my 
knowledge completely new isotope tool has become available after a recent, highly impressive 
analytical progress achieved by some of the authors (Seltzer et al., 2019, Ref. 6). The current 
manuscript now presents the logical follow-up, exploring and demonstrating the use of such 
measurements to determine groundwater table depths. 
The study goes far beyond a first feasibility test, as it includes a large number of samples from 
three different sites. The data are of exquisite quality and their interpretation reaches a depth that 
only leading experts in the field could achieve. Indeed, the author group combines leading 
researchers in noble gas analysis and application to groundwater. The biggest difficulty with the 
manuscript appears to be the complexity and novelty of the method, leading to the necessity to 
back up the general story of the main text (that should remain understandable to non-experts) 
with detailed methodological explanations in the supplement (that peers will need to follow up all 
the arguments). This is generally well-done, but I have some comments in this context. 
In summary, the manuscript definitely deserves publication in a high-level journal such as Nature 
Communications. It is highly innovative and potentially opens up a completely new field for noble 
gas studies in groundwater and paleoclimate research. However, some moderate revisions may 
help to clarify certain points and to make the paper more accessible for a wide range of readers. 
 
 
Detailed comments 
 
1. Both in the abstract and at the end of the introduction, reference is made to a hydroclimatic 
shift from a wetter glacial period to a more arid Holocene. I found this astonishing, as generally I 
would rather expect the opposite. Only later (lines 176 - 180) it becomes clear that this finding is 
in agreement with other studies and due to a regional shift in storm tracks. I suggest to give the 
reader a bit more information already at the end of the introduction, e.g. by adding a statement 
such as “presumably due to a northward shift of storm tracks” or so. 
 
2. It should be made clear in the main text (as opposed to only the supplement) that the 
calculations of the effect of excess air assume that the entrapped air is soil air, affected by the 
gravitational settling fractionation, not atmospheric air. This is not explicit in the discussion of 
equation (1), but otherwise eps_EA would probably be quite large. It becomes more problematic in 
the discussion of Fig. 2, when on line 112 the authors speak of “complete dissolution of entrapped 
air” and in the caption (somewhat imprecise) of “complete dissolution of unfractionated excess 
air”, which seems to suggest that unfractionated atmospheric air is added to the dissolved phase. 
In my understanding, however, it is gravitationally fractionated soil air from the depth of the water 
table, which is entrapped and (partly or completely) dissolved. My recommendation is to speak of 
“soil air” rather than just air, or “entrapped bubbles of soil air”, on lines 87 and 112, and to avoid 
the term “unfractionated” altogether. 
 
3. When discussing the effect of oxygen depletion (which I consider to be quite likely), I find it 
somewhat unclear to speak of a 0.5 or 5 % difference in the sum of O2 + CO2, because this could 
mean a relative change (5 % of the mole fraction of ~0.21) or an absolute change in the mole 
fraction expressed in percent (i.e., from 21 % to 16 %). I don’t really have a clear solution to this 
problem. In the supplement, introducing the change in mole fraction DX_O2 and giving these 
values makes it clear, but in the main text it remains ambiguous. 

Further confusion may come from first talking of an 0.5 % difference, referring to the inset in Fig. 
2, and then of a 5 % effect, referring to the correction shown for the samples. This can be 
understood as soon as one realizes that the scale of the inset is heavily magnified compared to the 
scale of the main part of Fig. 2. Maybe it would help readers if this was explicitly stated in the 
caption of Fig. 2. 
 
4. It is a bit of a pity that the noble gas temperature reconstruction for the SD case study remains 
quite low-key, with the respective figure hidden in the supplement (Fig. S8). Maybe the difficulties 
with too high NGTs of some samples, which are discussed mainly in the supplementary Materials 
(around Fig. S9), which indeed are difficult to explain, are a consideration in this decision. And of 
course, the focus is on the water table reconstruction, which is a new method and requires 
detailed explanations. 
In general, this manuscript is very dense, with lots of interesting and important information (e.g., 
about the inverse model for WTD determination, the study areas, the groundwater dating, the 
NGTs, and special effects/problems seen in some samples) outsourced to the supplement. I 
understand and appreciate the authors’ aim to present a comprehensive study, but I have the 
impression that there is material for at least two papers in this manuscript. This probably can and 
should not be changed at this stage, but may be a consideration for how to proceed with the 
presented and future material. The method (or rather set of methods) is quite complex and may 
need a few further studies before the community becomes acquainted with it. 
 
5. The main result of the manuscript is the water table shift shown in Fig. 4. While this finding is 
quite impressive, there is one point that at least from the main text is not sufficiently clear to me. 
The method reconstructs absolute water table depths (WTDs) below ground surface at the time of 
recharge. While changes in WTD at one site over time are climatic signals (in the absence of direct 
human impact), the variability in WTD between different places may mainly be due to local 
topographic features. This is discussed in section 4 of the supplement and the solution to arrive at 
representative regional mean WTD appears to lie in using a groundwater model to estimate the 
modern mean WTD. Somehow, I am not entirely satisfied here. How well do the sampled wells and 
results from the Holocene and late Pleistocene represent regional mean WTDs? As the sampled 
wells are clustered in six multi-depth well sites, can the WTD results from each well site but 
different ages be directly compared? At least, a short consideration of the effect of topographic 
variability on the result shown in Fig. 4 should be added to the main text. 
 
6. It would be interesting to see how excess air amounts are related to WTD changes, as seen in 
Fig. 4. Literature about relationships between excess air and WTD (changes) is not mentioned in 
the main text, only in the Supplementary Materials. Maybe the current data are not sufficient to 
look at this in more detail, especially since Ne concentrations are missing, but experts in the field 
may wonder about such links. Maybe a statement could be made in the main text. 
With regard to the discussion about possible excess air influences on Ar and Kr concentrations in 
the Supplementary Materials (discussion of Fig. S9), I wonder whether this question cannot be 
answered based on the excess air parameters (A, F) obtained from the coupled inverse modeling 
undertaken in this study. Certainly, additional Ne concentrations would help to pin this down, but 
in principle the available data may suffice to constrain the excess air. As far as I can see, Ne was 
not available for the SD samples discussed here. However, in the Fresno case study, possibly Ne 
was measured in the context of the 3H-3He dating? Would including this information not improve 
the parameter estimations? 
By the way, there are several more papers that address the relationship between excess air and 
water table fluctuations / humidity, summarized in section 4.2 of the review by Aeschbach-Hertig 
and Solomon, 2013 (Noble gas thermometry in groundwater hydrology. In: Burnard, P. (Ed.), The 
Noble Gases as Geochemical Tracers. Springer, pp.81-122). 
 
7. Supplementary Materials, equations (S4) and (S5): I don’t understand why the mass 
differences for the different isotope ratios do not enter in these equations. Comparing with the 
equations (3) and (4) in Seltzer et al., 2019, there seem to be corresponding factors in the 
denominator terms missing. 
 
 
Minor corrections 
 
Line 65: “Isotope ratios of … *are* more strongly affected by …”. 
 
Line 181: “… indicative of *a* shift …” 
 
Line 214 (caption Fig. 4): Delete “be” 
 
Line 260: evacuat*ed* 
 
Supplementary Materials, line before eq. (S7): “Extension *of* S6 …” 
 
Supplementary Materials, bottom of p. 8: “Piston flow age distributions f*ro*m each age tracer …”. 
 
Supplementary Materials, top line of p. 9: Delete “Kip”. 
 
Supplementary Materials, caption of Fig. S11: “brin*g*ing several uncorrected values …”. 
 
 
Reviewer #2 (Remarks to the Author): 
 
Please see attached files for the recommendation to the editors and general comments on the 
manuscript as well as the minor comments in form of annotated comments in the original pdf files 
of the Main Text and Supplementary Materials.