the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 03 Aug 2026
Evaluating N2O Analyzers for Urban Monitoring: Evidence for Underestimated Emissions
Abstract. Nitrous oxide (N2O) is a potent greenhouse gas and ozone-depleting substance. Approximately 42 % of anthropogenic N2O emissions are thought to be emitted from urban areas. We tested three N2O analyzers for their suitability to measure N2O in urban areas from tower and mobile platforms. All three analyzers (Aerodyne SuperDUAL, Aeris MIRA Ultra, and LI-COR LI-7820) have sufficient precision for urban measurements but require different amounts of calibration and attention for best results. Using these analyzers, we observed tower-level enhancements at least 3 times larger than predicted from the best available inventory for the NYC region. Co-measurement of carbon monoxide (available on all but the LI-7820) were used to identify combustion-related enhancements of N2O. Mobile driving confirmed that traffic related emissions for NYC are captured by the inventory and that wastewater treatment is the most likely source for the missing N2O emissions.
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Status: open (until 03 Oct 2026)
- CC1: 'Comment on egusphere-2026-3919', Andrew Whitehill, 09 Aug 2026 reply
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RC1: 'Comment on egusphere-2026-3919', Anonymous Referee #1, 30 Aug 2026
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General comments
This manuscript compares three commercial laser-based N₂O analyzers (Aerodyne SuperDUAL, Aeris MIRA Ultra, and LI-COR LI-7820) and applies them to tower and mobile measurements in the New York City region. The authors conclude that EDGARv2024 underestimates regional N₂O emissions by about a factor of three. The topic is well suited to AMT, and several of the operational findings are the kind of practical knowledge that is difficult to obtain and rarely published. These include the Aeris line-locking failure mode, the interaction between the Aerodyne etalon fit and the water-vapour correction, and the LI-7820 humidity response and mid-deployment calibration jump. I therefore recommend a major revision before the manuscript can be accepted by this journal.
My main concern is that the manuscript still lacks interpretive and quantitative analysis. Observations are reported, but they are frequently not analysed enough. One of the examples is Sect. 3.1.4: three analyzers sampled a common inlet for three weeks (L132–133), which is the single most valuable dataset in the paper. However, the entire ambient intercomparison is presented in only four lines and one statistic, "the R² between each of the analyzer pairs was above 0.94" (L225). Apart from this R² value, the data allow much more analysis. For example, the authors could report the bias, RMSE, and drift between analyzer pairs at several averaging intervals, present a difference-versus-mean plot, and state whether any analyzer meets the WMO/GAW compatibility goal, and under which calibration regime. Almost all of this can be produced from data the authors already have.
The methods section is also too brief to make the study reproducible, particularly for the analyzer testing (Sect. 2.2) and the sampling set-up (Sect. 2.3–2.4). More detail would be welcome.
Detailed comments are provided below.
Introduction and motivation
The introduction does not clearly state what gap this evaluation fills. All three analyzers have already been used in published work, which the authors themselves cite, so a reader may reasonably ask why a further evaluation is needed. Please state the gap explicitly: what is not yet known, rather than what has already been done.
Methods
Sect. 2.1 (L58). Please add a brief explanation of why these three analyzers were selected for comparison before describing their features and parameters.
L79. Please verify this citation. Tong et al. (2023, 2025) did not use the Aerodyne SuperDUAL for flask sampling, so the attribution appears to be incorrect.
L94. Please specify how the configuration was performed and what was configured.
Sect. 2.2, Analyzer Testing. This section needs substantially more detail before the tests can be reproduced. For the humidity test in particular, how was water vapour introduced? As written (L114–118), dry cylinder air is passed through a Nafion dryer with the same dry cylinder gas as counterflow, which cannot generate the 0–2.3 % H₂O range shown in Fig. 1B. Please state how humidity was generated and varied, the exact humidity levels or the range and rate of change, whether the sequence was wetting, drying, or both, the duration, and the sample temperature.
L115. The phrase "vary the humidity of the analyzers" is imprecise, because the humidity of the sample gas was varied, not that of the analyzers. I would suggest "vary the humidity of the sample gas delivered to the analyzers".
L125. The phrase "in the same manner as we calibrated the ambient data" is not clear at this point in the text, because the ambient calibration procedure has not yet been described. Please describe how the ambient air was calibrated, or move this text after Sect. 2.3.
L133. Please provide more detail on the sampling set-up: inlet material, length and internal diameter, flow rate and residence time, filters, whether the line was heated, whether the sample was dried, and how the three analyzers shared the inlet. These details are essential for interpreting the intercomparison in Sect. 3.1.4.
L134. The phrase "corrected according to the results of the humidity correction described below" is a forward reference. Please describe the correction briefly where it first appears.
L146. I understand that the detail is in the Supplement, but a brief description of the mobile survey design and the plume identification method should appear here so that readers can follow the argument without turning to the SI.
L149. Were plumes identified using CO enhancements for every source? If so, sources that emit N₂O but no CO, such as wastewater treatment, sewers, fertilised urban green space, would not trigger the detection criterion at all. The Wards Island results suggest that N₂O-only enhancements were in fact identified somehow, so please describe how non-combustion plumes were detected.
Deployment summary table. Please add a table to the methods summarising when and where each source was sampled, with which analyzer, and under which calibration regime. The deployments are currently scattered through the text, and a reader cannot easily reconstruct which measurement came from which platform. This would also make the site-to-site comparison in Sect. 3.2.3 far easier to follow.
Results and discussion
Sect. 3.1.1, Fig. 1A. Why do the Allan–Werle curves for the Aeris MIRA Ultra and the LI-7820 fall sharply and then rise again at long integration times?
Sect. 3.1.4, structure. Consider presenting the tower and mobile deployment results in a separate section. The methods treat the tower and mobile deployments separately, and neither belongs under "analyzer testing", so the parallel structure would be clearer. If there is not enough material for a separate section, the content could be moved into the urban observations section, since those results are derived from the same deployments.
L225. By "cell size", do you mean the sample cell volume, the optical path length, or both?
L235. "The majority of vehicles in NYC do not use urea-based catalysts", is there literature or fleet-composition data to support this? The inference also seems stronger than the observation allows: vehicular N₂O is produced both by three-way catalysts on gasoline vehicles, particularly when the catalyst is cold, and by SCR systems on diesel vehicles, so a low N₂O/CO plume fraction is also consistent with fleet composition, driving mode, or the detection threshold used.
Sect. 3.2.3, cross-check with CO and CH₄. CO is measured at the same inlet, and published observed-versus-predicted analyses exist for CO and CH₄ at this site (Schiferl et al., 2024, 2025). Running the same analysis for CO and CH₄ over the same hours and footprints would test whether the discrepancy arises from the N₂O inventory or from transport and background errors common to all species. At L269–271, this argument is asserted rather than demonstrated, and demonstrating it would require no new data.
L280 and source attribution. The discussion of alternative sources is too brief given that the conclusion rests on it. Three candidates absent from EDGAR are not considered: recreational N₂O use, which the authors themselves cite three times in the introduction (L23–24) and at L247–248 but never revisit; medical and anaesthetic N₂O, given the hospital density of New York City; and sewer networks, which the authors themselves reference through Fries et al. (2018). All three are non-combustion, carry no CO signature, and are missing from the inventory by construction.
Sect. 3.2.2, quantification. No estimate of the Wards Island source strength is attempted, so it is not established that wastewater treatment could actually close the gap. Even an approximate mass-balance or Gaussian-plume estimate from the mobile transects, compared against the roughly 4000 t yr⁻¹ of missing regional emission implied by the scaling, would turn this discussion from a suggestion into a test.
Figures
Fig. 2A. These are two example plumes selected from the many observed during the campaign, is that correct? Please say so in the caption, and state how representative they are.
Fig. 3A. The small enhancements cannot be distinguished because every point is rendered in the same green. The colour scale appears to be set for the maximum in panel B (450 ppbv), which saturates panel A into a single colour and removes all of its information. Please use a separate scale for panel A, or a logarithmic scale.
Fig. 4A. The colour bar label "kg box⁻¹ hr⁻¹" uses an undefined unit, and grid-cell area varies with latitude. Please use kg km⁻² hr⁻¹ or define "box".
Fig. 4B. The panel is clipped: the legend is cut off mid-word
Conclusions
Some of the material in the conclusions is not a result of this study. For example, "The LI-7820 has an internal battery that makes it ideal for portable applications or mobile sampling but it does not measure carbon monoxide (CO), which can distinguish between different sources of N₂O in urban environments" is a manufacturer specification, available from the product documentation, rather than a finding of the work. Such information would be better placed in a summary table of analyzer characteristics, which the paper currently lacks and would benefit from, so that the conclusions can focus on what the authors have actually shown.
Technical corrections
L30 versus L305–306. The introduction states that Harris et al. (2017) found Zurich consistent with inventory estimates, while the conclusions cite the same work as showing a smaller underestimate. Please make these consistent.
L130 versus L272. The CUNY deployment is given as August 2024 to May 2026, which is 22 months, but L272 refers to 32 months. I assume these are site-months summed across the three sites; please clarify.
Units. The manuscript mixes ppbv, pptv and ppb. Please adopt one convention throughout, including figure axes.
Citation: https://doi.org/10.5194/egusphere-2026-3919-RC1
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- 1
The manuscript "Evaluating N2O Analyzers for Urban Monitoring: Evidence for Underestimated Emissions" by Andrew Hallward-Driemeier et al. evaluates and compares three commercial nitrous oxide (N2O) monitoring instruments (Aeris Technologies, Aerodyne Research, and LI-COR Environmental) under a variety of conditions and provides recommendations to improve data quality from them. The manuscript also provides an analysis of tower-measurements compared to inventories and mobile measurements of traffic emissions and wastewater treatment emissions. The paper is framed as two loosely-connected narratives (the instrument evaluation and comparison, the measurement campaign and inventory evaluation) – I will comment mostly on the first, as it is within my area of expertise. This is not meant to be a comprehensive review of this manuscript.
This is a very useful manuscript with helpful data for the community (on both methods as well as N2O sources and inventories) and is within the scope of Atmospheric Measurement Techniques. I believe several improvements could be made to make the manuscript stronger prior to publication, which I outline below.
General Comments
Lack of quantitative results and uncertainties
The biggest issue with the methodological sections of this paper is the lack of quantitative results and associated uncertainties. Similar AMT manuscripts (e.g. Commane et al. 2023) generally report more numerical results (in the text or tables), with uncertainties where possible. The main text should have actual numerical results (with uncertainty bounds) rather than general comments or rankings ("All three analyzers outperformed their reported 1-second precision in our tests.", L183; " None of the analyzers showed a significant change…", L207, etc.). The abstract is also written vaguely (e.g. "sufficient precision for urban measurements…"). I recommend the authors be more precise and quantitative when describing their data and results. Almost all measured / modeled values and statistical results are assumed to be exact (reported without uncertainties).
Methodological descriptions could use improvement
Additional description of the methods (flow paths, part numbers, assumptions, etc.) for the experimental sections would make this manuscript much stronger. Additional descriptions of the modeling and associated assumptions would improve the manuscript as well.
Aerodyne water vapor correction
The authors apply a literature-derived water broadening coefficient from Kostinek et al. (2019) to their Aerodyne data. However, they do not provide any details or equations about how they implement this correction. Kostinek et al. (2019) use JFIT software rather than TDLWintel (Aerodyne standard software) and derive specific water vapor corrections (dilution and pressure broadening) applied using specific equations using their specific analysis stack. If the authors of this manuscript drop the Kostinek et al. (2019) broadening coefficients directly into TDLWintel software without proper modification then they are artificially introducing a water vapor bias in their N2O spectral retrieval algorithm. This is very clearly seen in Figure 1B, where there is a significant linear water vapor dependence of the Aerodyne that is indicative of a poorly-chosen water vapor broadening coefficient. Authors need to provide additional justification for the choices they made here. At a minimum, they should describe how they applied the water broadening corrections (assumptions, equations, etc.), why they were necessary (e.g. demonstrate with data that they are superior to the default parameters), and justify their choice of Kostinek et al. (2019) parameters even when using a different fitting code with different assumptions. If authors want to apply appropriate water vapor corrections they should really characterize the broadening for their specific system, software retrieval, and instrument / cell conditions and apply that rather than just applying literature values.
Specific Comments and Suggestions:
L4-L6: Suggest authors include quantitative estimates of precision instead of ambiguous statements like "sufficient precision"
L6-L7: Suggest authors include quantitative values for comparison of tower-level enhancements versus NYC inventories. Also recommend the authors specify which inventory they are using – "best available inventory" is ambiguous.
L19-L25: Authors make lots of claims about budgets and estimates (including numerical values) but do not include uncertainties. One of the core arguments of the papers is that emissions inventories underestimate emissions – it is important to include uncertainties in the emissions estimates and budgets to be able to assess the validity of the argument and the degree of under-estimation.
L32-L34: This implies N2O / CO correlations only occur from fossil fuel combustion. However, biomass burning and other non-fossil combustion sources also co-emit N2O and CO
L51-L52: The Aerodyne SuperDUAL QCL/ICL uses direct or differential infrared absorption spectroscopy in a Herriott multipass absorption cell (see L79). This is not a cavity-enhanced technique – it does not rely on an optical cavity or typical physics employed by cavity-enhanced techniques (CEAS, CRDS, etc.).
L85-L89: See General Comments…
Section 2.1.2.: Authors need to provide additional information about how they set up and configured their Aerodyne sampling. What frequency did they perform spectral backgrounds (e.g. hourly with N2 as in Commane et al., 2023, every 5-10 minutes as in Kostinek et al, 2019)? What frequency did they perform calibrations? The use of regular calibrations or spectral backgrounds is a critical factor affecting the performance of Aerodyne systems and authors do not provide any details about this.
L109-L110: Authors should provide additional details into how they performed their Allan-Werle variance experiments – was it done in a laboratory environment (temperature stability is critical for most of these measurements), what flow rates (cylinder depletion effects relate to flow rate), flow path, etc. Were all instruments measured at the same time? What N2O concentration was the Allan Variance performed at?
L110: It is interesting for authors to apply a specific method (Allan-Werle variance) without citing any of the core papers describing the method (e.g. Werle et al., 1993, etc.).
L117: Minor point, but the degree and magnitude of CO2 leakage across Nafion membranes is an important parameter that has been disagreed upon in the literature (but generally agreed to be relatively small). If the authors note significant CO2 leakage that could be important beyond the scope of the paper, or could indicate an issue with their Nafion membrane. Additional details (e.g. membrane type, leak rate across membrane, or even just CO2 leakage magnitude) would be useful here but not critical.
L134 – L139: The traceability is good (NOAA-2006A) but authors should provide values for the concentrations of their primary calibration cylinders – what range did their calibrations span compared to their measurements?
L183: Authors should include a table here with numerical results (reported 1-s precision, measured 1-s precision, etc.) rather than just a figure. See, e.g. Table 3 of Commane et al. (2023) as an example.
Section 3.1.3:
Authors should include quantitative results here (or in an associated table) instead of general descriptions of the pattern.
Section 3.1.4:
Authors should quantitatively define the "limits sufficient to capture urban N2O variability" as well as report quantitatively the "noise of all three analyzers"
R2 shows strong (but not great) correlation but nothing about the relative accuracy of the analyzers after calibration. I recommend something like a histogram of absolute or relative differences in the measurements between instruments. Given the different response times, this is probably best done on some time-average (5-minute, 1-hour) versus 1 Hz data (or done after applying appropriate time shifts and smoothing to account for instrument response time).
Given differences in flow rates, cell size, and instrument response the 1 Hz data is not expected to agree between instruments, yet it was the chosen interval for inter-instrument comparison. There is also no discussion of time-correction / time-alignment / clock synchronization between instruments, which would be critical for 1-s data comparison.
L224-L225: "The different cell sizes of the analyzers and instrumental noise account for any remaining discrepancies"
This is stated with minimal explanation or justification. Although it is likely correct, authors should show (at least qualitatively) why the discrepancies make sense given their knowledge of cell sizes, flow rates, and noise (which they know for each instrument).
Section 3.2.3: A more thorough wind-direction analysis (or even a few wind rose plots showing the relationship between wind direction and N2O enhancement) or footprint analysis would make the source argument much stronger and more quantitative than the current general observations. Comparing estimated sources with land-use (where is the WWTP compared to the air sources during the peaks? Are there also other potential sources – parkland, industrial sources, transportation hubs, etc. – in similar directions?).
Comparing N2O and CH4 data might also significantly strengthen the WWTP hypothesis (see, e.g., Gålfalk and Bastviken, 2025). According to the manuscript, CH4 was also measured, so why not use it to support your argument?
Figure 1: Why is σ2 in units of ppbv and not ppbv2? Does not σ have units of ppbv?
Datasets:
These should be reviewed and cleaned-up. A brief (non-comprehensive) overview revealed several issues:
allan_variance.csv
The columns seem to be incorrectly labeled here. CO_qcls increases monotonically throughout the test and N2O_aeris is around 15 ppbv and N2O_licor is around 180 ppbv.
humidity_test.csv
Possibly column mislabeling? H2O_aeris seems to be constant around 250 through the entire series, whereas H2O_qcls and H2O_licor vary.
calibration_data.csv
Random N2O jumps to 1540 ppbv (e.g. 03/06/2025) versus 370.26 is not well explained