the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 14 Aug 2025
Sensitivity of tunable infrared laser spectroscopic measurements of ∆’17O in CO2 to analytical conditions
Abstract. Triple oxygen isotope (∆’17O) measurements of CO2 are increasingly used in paleoenvironmental and atmospheric sciences, in part due to the emergence of tunable infrared laser direct absorption spectroscopy (TILDAS) as a cost- and time-effective method for quantifying rare isotopologues in CO2. This study aims to provide users with a clear understanding of how the stability of analytical conditions — such as optical cell temperature, pressure, and CO2 concentration — affects measurement quality. Using data from two laboratories equipped with TILDAS instruments (University of Göttingen and University of Cape Town), both operating in high-precision dual-inlet mode, we demonstrate how variations in these parameters influence measurement repeatability and long-term stability. The most significant factor affecting short-term repeatability of ∆’17O is a mismatch in CO2 concentration between sample and working standard. The resulting scale-offset effect can amount to several ppm per 1 µmol mol mismatch, depending on instrumental parameters. We show that empirical corrections for such offsets, arising from variable pCO2 of the analyte across measurements, significantly improve reproducibility. In contrast, the dominant influence on long-term stability is drift in optical cell temperature and pressure. In air monitoring studies, unrecognized instrumental drift due to variations in optical cell temperature, pressure, and CO2 concentrations can be misinterpreted as genuine seasonal variations in ∆’17O. We conclude with practical recommendations for achieving the highest possible precision with TILDAS, emphasizing that continuous monitoring and reporting of analytical conditions is essential.
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- RC1: 'Comment on egusphere-2025-3040', David Nelson, 01 Sep 2025
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RC2: 'Comment on egusphere-2025-3040', Mathieu Daëron, 29 Sep 2025
This kind of study, although perhaps non-glamorous, is extremely useful in the early days of a novel analytical technique. Virtually all groups already using optical methods to target cap-deltas in CO2 (or about to do so) will benefit from the observations reported here. Below, I list a number of comments/suggestions intending to improve and clarify the text.
* terms like "repeatability" "reproducibility" and "long-term stability" should be defined explicitly, early in the text. When using notions such as "standard deviation", it must be clear what "one observation" means (e.g., a single injection of an aliquot of CO2, the average of several injections, a one-second-long average optical measurement, etc). This is usually obvious to the authors but not to the readers, who may follow different conventions.
* l. 43: Petersen et al. (2019) does not seem to be directly relevant here.
* l. 48: Technically correct but somewhat misleading: the "precise" measurements reported by Adnew et al. (2019) come at the cost of prohibitively long integration times (20 h integration for 14 ppm internal SE).
* l. 60 "most apply to the technique in general": you may want to specify if "the technique" refers here to TILDAS of infrared spectroscopy in general. I am of course biased, but VCOF-CRDS as implemented by Chaillot et al. (2025) is not sensitive to analyte pressure, for example.
* l. 153-154 "This indicates that the correction is independent of the isotopic composition of the sample analyte": what is the difference in δ13C, δ18O values between IAEA-603-derived CO2 and the working reference gas?
* l. 156-157 "This suggests that the correction slope varies slightly between sessions": in practice, this means that one must determine lab-and-session-specific correction parameter(s) based on repeated analyses of some known CO2. These estimates for correction parameter(s) will have uncertainties, and it would seem useful to investigate/quantify the final contribution to analytical uncertainties from this source of error.
* l. 169 "eliminating the need for such a correction": to the authors' discretion, it might be relevant to note that this was tested and verified experimentally.
* l. 176-182: Regarding the data shown in figure 5, it is not entirely clear if these measurements were corrected by repeated bracketing by a working standard, as reported in section 3.1. The next paragraph is quite confusing IMHO because of this: if the figure 5 data is reference-bracket-corrected, the δ18O and Δ17O variability seems enormous; if not, then what do these data look like after reference-bracket-correction? And if the corresponding reference gas measurements were not performed, how could the authors compute their "mismatch parameter"?
* figure 6: How is "internal Δ'17O error" defined?
* l. 187-188 "The internal error of a single replicate analysis, i.e., the
repeatability of approximately 10 sample cycles within a bracketing measurement": This is good exemple of ambiguity introduced by using undefined terms. Is the "internal error" not the standard error but the standard deviation of ~10 non-independent but separate bracket-corrected measurements? The answers to this question may be obvious for the authors, but not for most readers.
* l. 211-213 "This suggests that a temperature stability of ±1 mK, a pressure stability of ±10 Pa, and a χ’626 stability of ±1 µmol/mol are sufficient during a replicate measurements to prevent any systematic impact on internal repeatability.": I suggest quantifying this statement by adding "[any systematic impact on internal repeatability] beyond +/- X ppm on Δ’17O."
* l. 220-221 "In this context, drift in compression directly affects the accuracy of the final ∆’17O values.": This is surprising. One would expect that drift in compression would be effectively corrected by a two-anchor standardization approach. Is this not the case here?
* l. 243-249: Here the authors make an important point, too often unacknowledged. Kudos for stating it succintly and clearly.
* l. 250-257: I would suggest adding recommendations about what to do in such cases. Is it feasable to inspect the fit residuals to look for a signature of such matrix effects? Would other approaches work better? Would labs using the exact same methods but different collision gases still get consistent results after two-point standardization?
* Regarding the monitoring of long-term drifts in analytical conditions, does this imply that things like temperature sensors should be peridoically recalibrated to avoid drifts in true T (despite logged T being constant)?Citation: https://doi.org/10.5194/egusphere-2025-3040-RC2
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This is an excellent paper and the content is appropriate for this journal. It should certainly be published with a few minor revisions as described below.
Comments
The meaning of short term and long term in the abstract (and throughout the paper) are not well defined. The authors should define the time scale that they mean by long term drift. Also it seems to me that pressure variation is also a short term drift. Since the pressure in the optical cell changes each time the cell is filled, it generally varies more rapidly than sample concentration. Hence, it would seem that pressure variation should also be categorized as a short term effect just as the authors do with variation in sample concentration. Both concentration mismatch and pressure mismatch are drivers of instrumental measurement error. However, both are precisely quantified scalars whose effects can be quantified and corrected. The effects of temperature drift are much more complex beginning with the observation that there is not just one temperature. Many relevant temperatures are drifting simultaneously and continuously: cell temperature, laser temperature, the temperatures of various key electronic components, etc...
At line 113, I would suggest rephrasing to something like: “mixtures … are used to create optimal spectral line broadening due to collisional broadening at pressures between 30 and 40 Torr.”
In Section 3.2 the authors seem to give the impression that concentration dependence arises from the inability to measure all isotopologues of CO2. I don’t think this is correct. The root causes of concentration dependence are subtle and still being studied. But major factors seem to include systematic errors in the non-linear spectral retrievals and non-linearity in the infrared detector response function. Whatever the cause of concentration dependence, the empirical first order correction adopted by the authors (x=a*x’ + b) is appropriate.
At line 255 perhaps it should be explicitly stated that the reference gas matrix must be selected to match the sample gas matrix.
At line 269 the authors state “Long-term drifts in analytical conditions — such as a gradual temperature change of 0.5 K over the course of a year”. In some laboratories, temperature drifts of 0.5 K can occur within a few hours. There is a need to differentiate time drift versus temperature drift. Do the authors have data that isolate the effect of temperature on scale compression? That would be interesting to see. It seems that a key question is: how frequently does a two point calibration need to be performed? Or, perhaps, how much do such calibrations depend on ambient temperature? The answer may depend on the range of 18O isotopic composition in the samples and standards being measured.