Summary:

This manuscript provides describes a series of collocations between three different ambient formaldehyde instruments, including the Picarro G2307 cavity ringdown spectrometer and two different models (the Pico and the Ultra) of the Aeris Technologies MIRA formaldehyde analyzer. Comparisons between different formaldehyde measurement methods are common and typically have shown mixed results, suggesting that issues still need to be resolved in making accurate and comparable measurements of formaldehyde at ambient air concentrations. However, this manuscript compares three different commercially available, easy-to-operate platforms and compares it to the standard EPA Method TO-11A. Therefore, there is likely some additional value in this work beyond previous studies, which often used instrumentation that is more resource intensive or was research-grade and less easy to run in a routine situation. I had some general and specific concerns about this manuscript that I suggest the authors consider (and possibly address) prior to publication. I recommend moderate revisions (between major and minor) before acceptance.

General Comments:

I had several general concerns with this paper.

The first has to do with how the calibrations were performed. The Picarro was calibrated at 100x to 1000x higher concentrations than the range measured in the field, and was also calibrated in a different matrix gas (N2 vs Air). The authors did point out that they assume linearity, but they do not provide strong evidence for linearity from single-point calibrations, and certainly not linearity over 3 orders of magnitude. The Aeris instruments either weren’t calibrated (Ultra) or were post-corrected based on comparison with the Picarro (Pico). Therefore, the slope and intercept in Figure 7 are essentially a test of how good the Aeris calibration is. Given the 15+ months from manufacturing to use, the strong comparison is impressive but perhaps not very useful. Given the importance of appropriate calibrations for making these measurements, I recommend the authors spend additional time discussing recommendations for how to calibrate the instruments. Even suggestions based on experience (if presented as such) would be better than completely ignoring the issue.

The second major concern is with the suggestion that the Picarro G2307 be run with a DNPH scrubber for regular zeros. I would make sure to mention that doing this would likely (and probably should) void the manufacturer’s warranty and/or any maintenance or service agreements and could also reduce the lifetime of the instrument. The LpDNPH S10L cartridges are made by coating silica gel with 2,4-dinitrophenylhydrazine in an acidified solvent solution. As a result, the LpDNPH S10L cartridges will emit small amounts of solvents (possibly acetonitrile or methanol), acid gases (e.g., HCl or H2SO4), and possibly volatilized byproducts of the DNPH reactions. It is not immediately clear what impact those might have on the cell or mirrors in the G2307, or whether any of those compound might contribute to spectral interferences in the formaldehyde retrievals in the 5626 cm^-1 region. This should also be considered when discussing the ~0.5 ppbv offset difference between the DR / DR+MS baseline and the DNPH baseline for the Picarro instrument. Although the DNPH cartridge makes sense for doing humidity-matched baseline corrections, it appears (Figure 3) that the Picarro is plumed such that the zeros are performed from indoor air passing through the DNPH scrubber. In this configuration the instrument loses the ability to perform humidity-matched zeros, which seems to negate the major reason for using DNPH over a different scrubber (e.g., humidified zero air or just dry zero air). A zero air cylinder would last longer than a DNPH cartridge, not have the potential concerns about acid / solvent off-gassing, and could last indefinitely with an appropriate zero air generator.

Nowhere in the manuscript is the issue of the actual accuracy of the Aeris or Picarro instruments addressed. Given the large discrepancy between the Picarro G2307 and the TO-11A, there are clearly accuracy issues with one or both methods. In addition, the discrepancies observed here are larger than those observed in many other studies comparing DNPH to spectroscopic measurements. I also have concerns about the 0.5 ppbv difference in baseline using the DNPH versus DR and whether that could contribute to the 1 ug/m3 intercept in the Picarro vs DNPH comparison. Nowhere do the authors make a convincing argument that the DNPH zero is a “true zero” versus the DR or other zero / scrubber mechanism.

General Suggestions:

PLEASE use consistent units when talking about formaldehyde concentrations. Choose either ppbv or µg·m^-3 and don’t keep switching back and forth in different parts of the text and different figures. Conversion from one unit set to the other is straightforward, but it’s very difficult as written to compare concentration ranges in different sections because the units are not consistent.

Specific Comments and Suggestions:

Line 36: Recommend “Because HCHO photolysis / oxidation is a source of …” instead of just “HCHO is a source of”

Line 44: Recommend “the standard EPA approach” rather than “EPA-standard”

Lines 45-46: Please cite the 1999 version of EPA Method TO-11A. You cite Riggin, 1984, which is before the TO-11A “Method” existed. (https://www.epa.gov/sites/default/files/2019-11/documents/to-11ar.pdf)

Line 46: I believe it should be “Sample collection and analysis are” instead of “is”

Line 47: “…long sampling times” is very ambiguous. TO-11A is generally used for 1 hour to 24 hour sampling in ambient air – it is not effective if the time is too short (not enough HCHO collected) or too long (you get breakthrough).

Line 47-48: “EPA Method TO-11A measurements in the PAMS and NATTS networks are 8 or 24 h …”

Technically TO-11A measurements can be any length – you are specifically talking about current PAMS and NATTS required sampling frequency / duration.

Line 51: “the method…” here seems to refer to the “previous approaches” in the sentence prior rather than “Method TO-11A” (which I believe is the intended target for “the method”).

Line 51: Perhaps mention “the DNPH method…” because Method TO-11A specifically addresses the O3 interference (which was actually a large impetus for publication of TO-11A versus staying with TO-11).

Lines 57 – 61: There are a number of datasets with about 1 month or longer of continuous spectroscopic formaldehyde measurements at ground level, generally using TDLAS. See, for example, Coggon et al. (2021) (https://doi.org/10.1073/pnas.2026653118, Figure S20) or Spinei et al. (2018) (https://doi.org/10.5194/amt-11-4943-2018, Figure 3).

Line 63: “A more suitable long-term HCHO monitoring instrument…” – more suitable than what? And suitable for what purpose? I recommend rewriting this entire sentence – it’s a bit confusing as written.

Line 77: “relies on the HDO line” – which HDO line? Either specify a line or say “a HDO line”

Line 88-89: “This updated algorithm…” – are you referring to the algorithm used in Glowania et al. (2021) or the post-Glowania algorithm update to resolve the issues reported in Glowania et al. (2021).

Line 91: Technically, the Picarro G2307 does not “rely” on periodic instrument baseline zeroing. Once calibrated, it should be stable for months without needing to zero. Regular zeroing is recommended for the highest (sub 1 ppbv) precision (e.g., minimize baseline drift).

Line 92 – 94: A commonly used scrubber for HCHO-free air is a heated catalytic hydrocarbon scrubber. This is often used in cases where humidity-matched zeros are necessary. See, e.g., Herndon et al. (2007) (https://doi.org/10.1029/2006JD007600). I believe it is also used by Fried et al. on various aircraft studies. This is also used in commercial zero air generator systems to produce HCHO-free air.

Lines 150 – 160: It’s odd for the authors to calibrate the HCHO at > 1 ppmv but make most of their measurements in the 1 – 10 ppbv range. This is a 3 order of magnitude difference between the calibrated range and the measured range. Linearity across 3+ orders of magnitude is a major assumption, especially given the potential influence of peak shape on formaldehyde retrievals at different concentrations over a 3 order of magnitude range. Because these are single-point calibrations, the authors do not even test the linearity of the instrument across any range.

In addition, the calibrations were done in an N2 bath gas, whereas the zero and measurements were done with a N2/O2 mix (air). In an ideal situation, calibration matrix would match the measurement matrix as closely as possible, especially considering the high potential for matrix effects in a high-reflectivity cell with > 1 km effective pathlength. Given the 50% discrepancies observed versus DNPH, I recommend some of the assumptions made during the calibration be reconsidered (or at least discussed more thoroughly).

Lines 150 – 160: The concentration of HCHO in reference gas cylinders typically decrease over time at a pseudo-linear rate. It would be helpful to know when the gas cylinders were certified by Apel-Riemer / Airgas versus when they were used to perform the calibration checks.

Line 166: The manufacturer’s literature / spec sheets describe a 13 m pathlength for the instruments. I recommend you check whether 1.3 m or 13 m is the correct pathlength.

Line 178 / 179: Figure 2 is a map. I believe the authors intend to refer to Fig 3a / Fig 3b in these lines. Figures should also, in general, be added to the manuscript in the order they are referred to in the text, which would make Fig 3 the first figure (Fig 1).

Lines 177 – 179: The “Scrubbing ambient air rather than indoor air…” part is confusing, since indoor air also has sufficient water vapor to maintain a laser line lock (and, in fact, Aeris markets their instruments for indoor air measurements of HCHO as well). Scrubbing ambient air will provide humidity-matched (or very close to humidity matched) background versus sample gases, whereas scrubbing indoor air would produce a near constant humidity for the zeros but a varying humidity for the sample gases.

Line 179: It is not clear why authors choose to sample ambient air for 180 s and scrubbed air for 30 s, versus the scheduling used by Shutter et al. or recommended by the manufacturer.

Line 216-217: Please provide the correct (1999) reference for EPA Method TO-11A

Lines 219 – 221: What was the temperature of the heated inlet? What type of ozone denuder? I’m assuming based on the ATEC sampler that the ozone denuder was a KI-coated copper tube heated to 50 °C, but this is important to mention. Particularly as there are concerns with some types of ozone scrubbers in sampling formaldehyde (see, e.g., Ho et al. 2013, https://doi.org/10.4209/aaqr.2012.11.0313).

Lines 220 – 221: Please provide additional details about the cartridge (e.g., sorbent, DNPH loading, bed size, etc.). Supelco DNPH-C-18 is not a standard item – their standard DNPH cartridges use silica gel, not C-18. This seems to be an unusual / custom cartridge type.

Lines 230 – 234: The 12% uncertainty seems very low. Estimated collection efficiencies are generally about 70 – 100% (see, e.g., https://projects.erg.com/conferences/ambientair/conf18/MacGregor_Ian_AirToxics_8-15_800_SalonE_POST_508.pdf) for HCHO. In addition, there is likely to be a negative bias in the DNPH because of breakthrough of HCHO, reverse derivatization reactions, degradation of hyrdozone, etc. In contrast, for a good chromatographic program (that resolves the NO2 artifacts) there should not be a positive bias in the measurements.

Figure 9: It is very challenging to see the difference between the three symbol types in this figure. I recommend choosing a different presentation if you want to clearly distinguish between the Picarro and two Aeris by the symbol style.

Section 5:

If I understand this correctly, the Aeris Ultra essentially used the manufacturer’s calibration, the Picarro was calibrated at 1 ppmv in N2, and the Aeris Pico was corrected based on the Picarro. Therefore, the comparability of the Aeris Pico, Aeris Ultra, and Picarro G2307 (especially the slope and intercept) seem to be a test of how comparable the Ultra calibration is to the Picarro calibration. Essentially, this section seems to be a test of the Aeris Technologies calibration more than actual instrument-versus-instrument comparability.

 It might be more interesting to look more closely at:

• When the disagreement between methods occurred (e.g., is there any pattern that could suggest a reason for the disagreement beyond just random noise)?
• How large was the “scatter” around the regression line – was it in line with what would be expected from the precision / allan variance measurements reported earlier, or is there additional uncertainty factors from measuring in ambient air? If the latter, could you quantify how large that additional uncertainty is and suggest possible causes?

GENERAL COMMENTS



Mouat et al performs an intercomparison between Aeris MIRA instruments (Pico and Ultra) and Picarro CRDS G2307 in order to evaluate how robust these instruments are for long-term HCHO monitoring. Comparison is also made to the standard EPA Method TO-11A. The authors compare instruments against each other to determine relative biases and offsets. Additionally, they also evaluate how well HCHO is removed by DNPH, Hopcalite (HO), Drierite (DR), and Drierite+Molecular Sieves (DR+MS), and found that DNPH was best suited for all instruments to generate HCHO-free air.



The authors also present a multi-month HCHO dataset taken at two locations in the Atlanta metro area and show that HCHO has decreased by ~50% over two decades by comparing recent measurements in 2022 with those in 1999. The level of analysis for this last section of the paper is appropriate for AMT.



In addition to usual revisions and minor technical corrections, this paper contains several major revisions and corrections that I describe more fully below which the authors need to address. Broadly speaking, the major revisions encompass how the authors are calculating instrument performance and how they compare the instruments against each other.



This paper fully falls within the scope of AMT and would be of interest to its readership. I would recommend publication but only after proper and full attention has been paid to the following revisions. 





MAJOR REVISIONS:





- Line 179: "We sample ambient air for 180 s and scrubbed air for 30 s": The default settings of the Aeris MIRA instruments used to be sampling ambient air for 15 s followed by scrubbed air for 15 s, yet the authors have dramatically changed the timing of the cycle without providing substantial justification as to why their new cycle is better (other than maybe extending DNPH lifetime). The instrument's use case is for ambient monitoring (not fluxes), so more frequent sampling of the scrubbed air line is fine. What characterizations were done to justify this new cycle? The new cycle chosen by the authors looks problematic when I look at Fig 5 and see a multi-ppbv spread (6 ppbv HCHO for Ultra and nearly 20 ppbv for Pico) in the HCHO mixing ratio over several days when just sampling scrubbed air (that presumably has 0 ppbv HCHO). That spread is large enough to severely affect the accuracy of measured HCHO mixing ratios measured in the field.



To help address this concern, the authors need to explain how their new cycle timing was derived and show data to see how it performs against whatever is the default cycle timing used by Aeris. Another zero should be performed and an Allen-Werle curve derived using the default cycle timing and plotted against their new cycle timing since this now falls within the scope of their paper.



- Line 201: "significant deviation in sensitivity had occurred since its [Pico] last factory calibration": As denoted by the title, this is in part an instrument evaluation/comparison paper, so it's concerning when there's comparison of instrument accuracies against each other (Fig 7 and elsewhere), but there's also probable cause that the factory calibration for one of the instruments (i.e., Pico) was no longer even valid. When reading about the high 30-40% bias in the Pico, readers will be confused (and misled) as to whether this is a real instrument bias, or if it is simply because the authors are using an instrument with an expired factory calibration. In other words, how generalizable is this bias since someone just reading the abstract (Line 19) or conclusion (Lines 566-577) may not realize there are very significant caveats to this quantitative statement?



To help address this concern, the authors could verify that the Aeris Pico has the correct calibration/sensitivity (just like they did for the G2307 before doing subsequent comparisons) and then compare against the other instruments. Alternatively, the Aeris Ultra factory calibration seemed valid (Line 210-211), so maybe just do the instrument comparison between the Ultra and G2307 (would need to fix Fig 7 appropriately and correct corresponding text throughout paper).



- Section 4.1: Instrument drift: The authors state multiple times that they drift corrected the data (e.g., Line 295, Line 305), but never specify (1) how this drift correction was derived and (2) how generalizable is this drift correction (i.e., can it be applied to subsequent data collected by the instrument?). This should be rectified. Additionally, the authors don't explicitly mention whether or not they drift-corrected their multi-month HCHO dataset. Should that be drift-corrected too?



At one point (Line 324), the fastest Pico drift rate was 1.67 ppbv HCHO h-1, which is not acceptable for ambient monitoring. However, that drift rate seems highly variable (i.e., time-dependent) since it doesn't seem to always be changing at that rate as shown by Fig 5. Plus, the sign of the drift (either positive or negative) changes with time too.



Stating that an instrument is drifting is a very serious claim since when sampling ambient air, folks won't know if the change in HCHO mixing ratio is due to some underlying instrument baseline drift or a real change in mixing ratio.



- Fig 4 and surrounding text: I don't trust how this figure was derived since the whole purpose of an Allen-Werle curve is to help identify the integration time at which instrument drift becomes an issue. By correcting out instrument drift beforehand, the resultant Allen-Werle curve of course looks better, but it tells the reader nothing about the instrument's precision and long-term variability. Also, when I look at the large multi-ppbv changes in variability in Fig 5 for both the Ultra and Pico, I don't see how that corresponds to <100 pptv 1-sigma precisions for 20 min integration times and higher as indicated by Fig 4.



To help address this concern, the authors should derive Allen-Werle curves using *unaltered and uncorrected* HCHO mixing ratio data as reported directly from the instruments. Reporting this gives a better indication of instrument precision and provides better comparison back to what was reported in prior work. Based on my previous comment, I'm still left wondering whether this drift correction is generalizable since can it be consistently applied to ambient data when 0 ppbv HCHO air isn't being flowed into the instruments?



If the magnitude of these new 1-sigma precisions are on the order of a few 100 pptv HCHO, how would this impact your analysis comparing HCHO removal from DR, DR+MS, HO, and DNPH? Were the differences in baselines large enough to not be encompassed by the instrument's LOD?





REVISIONS:





- Lines 14-15: "Baseline drifts over a 1-week period of ambient sampling of 1 ppb, 4 ppb, and 20 ppb": You're technically reporting the spread of values as opposed to a time-dependent trend, so please state that.



- Lines 156: "measured concentrations were consistently 7% lower than expected": This also falls within the uncertainty reported for the Airgas HCHO gas cylinder standard (10%), so isn't it possible that the lower readings were simply due to the gas cylinder standard having lower HCHO than reported (which is definitely a possibility for HCHO gas cylinder standards)? Also, how long was HCHO allowed to flow through the MFC before calibrations were done? Generally speaking, several hours are necessary to passivate the MFC surfaces, and having a low flow is helpful to not waste calibration gas. 



- Line 150 - 160: Another concern when calibrating at such high mixing ratios (i.e., >1000 ppbv HCHO) to derive sensitivities is assuming linearity over three orders of magnitude (from 1 to 1000 ppbv HCHO). The authors state linearity is observed between 1-10 ppbv (Line 155), but if using a sensitivity derived at ~1000 ppbv HCHO, was it checked that linearity is observed between 10 and 1000 ppbv HCHO?



- Line 277: "two mass flow controllers": Are the MFCs were being used as valves in this setup (either fully open or fully closed) to go between the DNPH and HO lines?



- Line 291: "instrument baselines measured while sampling through a DNPH-coated cartridge": At this point in the text, the authors should explicitly say they are scrubbing HCHO from ambient air to derive their Allen-Werle curves.



- Fig 5: Not sure what is going on during the evening of September 6 between all three instruments, but if some part of the sampling apparatus was changed at that time, then this data should be removed since the setup was altered.



- Line 345: "differential concentrations in the range of -2.0 to -1.0 ppb HCHO for ambient air": Why are the magnitudes of ambient HCHO in air lower than when sampling scrubbed HCHO air? What are you trying to convey here?



- Fig 7: The Aeris Ultra and Picarro G2307 should just be directly compared if the Pico's calibration isn't trustworthy.



- Fig 9: It was hard for me to see when and where the Pico was sampling. Also, please make this a vector graphic since it becomes blurry and hard to read when rasterized.



- Line 538-539: Two more reasons that should be mentioned include (1) these are online measurements and (2) don't require special handling/storage of samples or use of hazardous chemicals.



- Line 563: Authors are making an incorrect comparison between 3-sigma (i.e., LOD) and 1-sigma values.





TECHNICAL CORRECTIONS:





- Lines 16-18: The authors appear to be incorrectly reporting the 3-sigma LOD since the numbers cited are for 1-sigma based on what is presented in Fig 4.



- Line 135: Do you mean Fig 3a (not Fig 2a)? This happens elsewhere in the manuscript too when I think you mean to reference Fig 3.



- Line 278: "the sample flow alternated between scrubbers in 40 s intervals": That's not what Fig 3c depicts.



- Line 417: Replace "This technique" with "This linear regression"



- Line 536: Replace "long-term" with "multi-month"



- Fig 3 caption: Be more explicit by defining abbreviations in caption and defining 1 (sample line) and 0 (zero line).