Review of “Diurnal, seasonal, and interannual variations in δ(¹⁸O) of atmospheric O₂ and its application to evaluate changes in oxygen, carbon, and water cycles” by Ishidoya et al., 2024

General:

The manuscript presents a study of highest relevance for the linkages among the carbon, oxygen and water cycles. For the first time, a research group has analysed long-term measurements of the atmospheric oxygen isotope ratio (18O/16O) intending to see the impact of natural (biospheric fluxes) and anthropogenic (fossil fuel combustion). It is a fascinating manuscript to read and I would like to congratulate them for their long-term measurement effort as well as their in-depth analyses.

The manuscript is nicely written and organized and can be considered for publication with minor changes outlined below. 

Major points:

(1) As already estimated in former studies, the expected signal in the atmospheric δ(¹⁸O) by the above mentioned isotope fluxes is minimal. This requires high precision measurements over an extended period in order to see such a small signal as the single uncertainty is about 10 times larger. The required precision and accuracy, especially important for trend analysis, can only be achieved by averaging over many measurements as shown in the manuscript.

I am not sure whether the mass spectrometer was dedicated only to these measurements and whether it was run day and night autonomously. Controlling the long-term stability only every month is quite rare because the mass spectrometers behavior can change suddenly due to maintenance (filament change, ion source tuning etc). Can you please comment on these points and maybe add an additional short section about it.

(2) Regarding the long-term estimated change in d18O(O2), the authors assume a constant increase rate of the GPP per year. For me, this does not make sense as there are many studies out there discussing the CO2 fertilization effect. Therefore, I would rather assume a scaling based on the excess CO2 level (CO2actual – CO2 preindustrial). Even though this will most probably not affect their results significantly (Fig. 8), but it still better than use a constant increase rate. In particular as the authors have used a CO2-dependent photorespiration rate (eq. 5).

Minor points:

Title:           Diurnal, seasonal, and interannual variations in δ(18O) of atmospheric O2 and its application to evaluate changes in oxygen, carbon, and water cycles.

What kind of changes do you mean here? Changes in trend, seasonality, fossil fuel influence, natural changes?

L15-16        the amplitude is very small, how about its uncertainty? Because it is a mean of about 11 seasons, the seasonality could be smoothed.

L18             The secular increase is even more delicate to determine, which requires an extreme stability of the instrument and the standard gas measurements. What about the influence of filament changes, power interruptions, ion source tunings, inlet system, gas flow regime. I am amazed about the stability that is required. Isotope ratio may be less prone to changes but elemental ratios as O2/N2 or Ar/N2 are generally more dependent on such changes. Can you comment on these. Thank you.

L26-28        consider rewording to:

The 18O/16O ratio of atmospheric O2, datm(18O), is about 24 ‰ higher than that of ocean water (per definition 0 ‰ on the Vienna-Standard Mean Ocean Water (V-SMOW)) due to various processes in the global oxygen and water cycle (e.g. Craig, 1961; Barkan and Luz, 2005)

L35-36        Please give corresponding references. There are many more than given here

L37             ..of present air, ...

L37             ….and that variations of the DME from the average are ±0.2 ‰. This addition is not clear, please be more specific here.

L45             Which value is now used? You may write...and have obtained a range of 22.4 to 23.3 for DME.

L63-65        This is a very interesting statement.

L82-83        Switch sentence structure, 2nd part first and vice versa.

For the continuous measurements of stable isotopic ratios of O2, N2, and Ar (datm(18O), datm(15N), and datm(40Ar)) as well as the O2/N2 ratio and amount fraction of CO2, we repeatedly conducted alternate analyses of the sample and reference air.

L84             how come to determine a trend of 0.22 permeg or a seasonality of 2 permeg with a standard deviation of 20 permeg. This requires an well-defined long-term stability.

L86             …calculated by ...Keeling…

L88-89        For this purpose, the measured values of the datm(18O) for the same air sample needed to not show any temporal drift, at least during the averaging period.

not clear what you want to say here, maybe you combine it with the previous sentence to

This averaging results theoretically in a standard error of the observed datm(18O) of less than 0.6 per meg assuming no temporal drift during the averaging period.

L106           …an uncertainty of ±0.13 per meg a–1….how was this calculated?

L113-114    As seen in Figure 3a, datm(18O) increased linearly with increasing amount fractions of CO2.

Why, what are the reasons? There is  no isobaric interference. Has it to do with isotope exchange between CO2 and O2? Have you done CO2 additions with O2 labelling?

L120-121    reword to …....in our earlier flask studies in 2013.

L135-136    RTS and RST denote the ratios of the annual fluxes of O2 between the troposphere and stratosphere, respectively.

to what? It is a ratio.

L140           …the amount fraction of O2 calculated by the 140 box model was converted to d(O2/N2).

how? Assuming a norm atmosphere or using the measurements to do it correctly. I ask this because of dilution effects.

L152-153    Here, eST was set to –4 per meg so that the diminution of datm(18O) at equilibrium was –0.4 ‰.

How come?

L161-162    This uncertainty complicates the problem of inter-annual datm(18O) change and suggests that gravitational separation may be involved in small fluctuations in the DME.

One needs to look into O3 and 14C variations at high altitudes, ideally close to the tropopause.

L204-205    …and artificial inlet fractionation induced by radiative heating of an air intake (e.g., 205 Blaine et al., 2006).

You mentioned that thermal diffusion is not affecting the measurements due to the high flow rate.

L234           1.46 ….in graph 1.45

L239           why only to terrestrial and not to marine biosphere activities?

L243-244    (https://www.enecho.meti.go.jp/statistics/energy_consumption/ec002/results.html#headline2, last access: 28 March 2024, in Japanese) (Ishidoya et al., 2020).

paper in 2020, reference in 2024?

L244-246    The implication is therefore that the isotopic discrimination of O2 during activities of the terrestrial biosphere was the main cause of the observed summertime diurnal datm(18O) and d(O2/N2) cycles, and the isotopic discrimination of O2 during fossil fuel combustion was very small or negligible.

The same conclusion could be drawn by radiocarbon measurements. I guess 14C measurements are being done at your station. Why not use and show it?

L254-256    This method, hereafter referred to as the “datm(18O)-method”, enabled us to remove the impact on d(O2/N2) of not only the activities of the 255 terrestrial biosphere but also the contributions due to the air–sea O2 flux, which is driven mainly by activities in the marine biosphere (e.g., Nevison et al., 2012; Eddebbar et al., 2017), from the estimated dFF(O2/N2).

Not clear as you first make the balance between observed and bio to obtain the FF. By doing this you cannot disentangle the air-sea O2 flux from the terrestrial O2 flux.

L267-268    It is noteworthy that propane (CH3CH2CH3), for which the ORFF is 1.67 for complete combustion, should also be considered as the household gas consumed in the TKB area.

This is very interesting.

L278-281    y. Similar separation has been carried out for CO2 based on the simultaneous analysis of the D(14C) and amount fraction of CO2 (e.g., Basu et al., 280 2020) or based on the simultaneous analysis of d(O2/N2) and the amount fraction of CO2 by assuming an average ORFF based on a statistical assessment (Pickers et al., 2022).

There are more publications available that might be cited!

L291-292    Figure 7a therefore shows 116 and 120 datm(18O) and d(O2/N2) data, respectively.

rewrite

L306-309    Keeling (1995) expected datm(18O) to be lower in summer than in winter by 2 per meg based on the assumption that the 100 per meg seasonal increase of d(O2/N2) was driven by the input of photosynthetic O2, the d(18O) of which is about 20 ‰ lower than datm(18O).

Show how to calculate it!

L316           We found that the box model could reproduce the observed seasonal datm(18O) cycles

You adjusted the corresponding values. Questions are remaining as to whether the used model values fall within known ranges.

L355-357    see major point 2

Fig. 2          The measurements are not equally distributed over time, this influences the uncertainty per year. Have you considered this?

The authors present measurements of the 18O isotopic composition of atmospheric molecular oxygen from air taken at the roof of their building in the greater Tokyo region. They also measured O2/N2 ratios and CO2 concentrations to assess the suitability of delta-18O in O2 to probe the carbon cycle. They analyse the diurnal and seasonal variations as well at the interannual trend with a one-box model.

The observations are pretty exciting. I am not aware of any group that measured the diurnal cycle of delta-18O in atmospheric O2 before. Given the tremendous technical advances over the last years, it seems logical that they succeeded, eventually. They still have to average about 1000 individual measurements so that average diurnal cycles for each season are presented.

I am less convinced by the analysis with the one-box model. The method was not well explained, so that it is possible that I missed some things. I think that the manuscript needs some serious revisions before publication.

• Why are there only the values of Bender et al. (1994) but not the updated figures of Luz and Barkan (2011, doi: 10.1029/2010GB003883)?
• Where is fossil fuel in the box model? It looks like the model comes from Bender et al. (1994) who analysed the last 130,000 years and did not need fossil fuel.
• The method of ignoring terrestrial or marine fluxes was not well explained. Only the terrestrial fluxes had a sinusoidal cycle in the methods. So how does the model calculate a diurnal cycle if terrestrial O2 fluxes are ignored?
• The rationale behind their calculations of the delta-18O_atm-method were not given. Why does the ratio give you delta-18O_bio? Is it because fossil fuel is missing in the box model?
• The box model has a shifted diurnal cycle by about two hours. You would get a strange signal when dividing two sinusoidal signals shifted by some delta. This does not seem the case here and I was wondering why? Is it possible that you get a false diurnal cycle of the biospheric fluxes because of the wrong timing of the box model?
• The ER method is not explained. Where are the numbers 1.1, 1.4-1.7 coming from? I guess nowadays 1.05 is more accepted for photosynthesis.
• How is it possible that in O2 leaf water isotopes are increasing by 9 per meg (Figure 8) when leaf water isotopes of H2O are increasing by nothing until 2000 and then only about 0.2 permil?
• What are the leaf water scenarios in Figure 7? I could not find any explanations. I would be curious how you get a time shift of up to two months from different formulations of leaf water.
• You get an increasing or decreasing secular trend if the right-hand side of Eq. (3) is non-zero. This can have many reasons and you do not have to have increasing GPP or anything. The authors have tweaked so many fluxes in their model that I do not think that we can say anything about the secular trend.
• This reminds me of the literature of delta-18O in atmospheric CO2. There were the same issues: a secular trend due to unbalanced fluxes, a one- to two-month time shift in the seasonal cycle, etc. The authors could learn at lot from that literature but not a single paper is referenced in the manuscript.
• Nobody thinks that GPP increase over the last century comes solely from a decrease of photorespiration. The discussion from page 14 line 397 up to page 15 line 417 is weird regarding the carbon cycle and anything we know about photosynthesis.
• The leaf water from MIROC5-iso looks like source water. Most global models of water isotopes do not calculate leaf water enrichment because they assume steady state so that the transpired water is the same as source water. If not, I would have loved to know how delta-18O of leaf water is calculated in MIROC5-iso.

More minor comments are:

• Why is the 18O in parenthesis in d(18O)? This is a weird notation.
• Given the current notation. It is never clear which molecule is looked at. Sometimes d_LW(18O) is O2 and sometimes H2O. Perhaps making it clearer, e.g. adding the molecule behind such as d18O-O2 or d18O(O2)?
• Lots of references are missing like all the references for the emission ratio method. Or ER = 1.67 for propane?
• I was wondering if MIROC5-iso has no carbon cycle? Most models have nowadays. So why not using these fluxes, or at least its dirunal and seasonal variations, instead of simple sinusoidal fluxes?

Ishidoya et al. have produced a stunning and groundbreaking extension of the well-known millennial-scale variations in atmospheric oxygen isotopes (namely 18O of O2), sometimes known as the Morita-Dole Effect, that are recorded in ice cores.   Their extension brings to the table totally new and fascinating information - namely the first high-quality observations of diurnal and seasonal cycles in 18O of O2.  Their tour-de-force treatment of extremely difficult analytical techniques makes it  possible now to ask totally new questions about the role of the terrestrial biosphere in the last 5 decades of (unplanned) anthropogenic CO2 fertilization due to fossil fuel burning, as just one example among many.

  The quality of their measurements is superb, and unparalleled.  Their deep attention to details, and exploration of potential pitfalls, makes their conclusions robust and convincing.

  One very minor comment I would make is that their box model estimate of ~1500 years for the turnover time of atmospheric O2 may be a little too long.  My ice core work shows that 18O of atmospheric O2 relaxes with a characteristic asymptotic decay curve after abrupt climate change events on a timescale of about ~1000 years, implying that the turnover time of O2 in the atmosphere is about ~1000 years.

 The authors are to be congratulated for a true breakthrough that will no doubt open many doors for future study of the interlinked carbon, oxygen, and argon cycles in Earth's atmosphere.  These studies will no doubt shed light on the ongoing anthropogenic perturbations to the cycles of these gases.