This study presents a GPP estimate over the conterminous US using TROPOMI SIF calibrated against eddy-covariance sites, with MODIS-based downscaling to 500 m spatial resolution. The methods used here are an extension of the previous work of Turner et al. (2020). This GPP estimate is then employed to examine interannual variations in GPP between 2018 and 2019, finding that differences between years are strongly impacted by four large precipitation-driven climate anomalies. This paper is well written, and I believe that this analysis is a significant scientific contribution and will be of interest to the readership of Biogeosciences. I feel that this paper is suitable for publication after generally minor revisions.

However, as a potential user of this datasets, I feel that the impact of this work would be significantly increased if a comparison with existing (particularly MODIS-based) GPP estimates was presented. Over the past several years, there have been a number of gridded GPP products developed, including the FLUXCOM GPP (Jung et al., 2020) and FluxSat v2 GPP (Joiner et al., 2020) that estimate GPP from MODIS data trained on eddy-covariance observations. A clear advantage of the MODIS-based GPP estimates is that they cover 2001-present, while the advantages of this TROPOMI-based GPP product are less clear. In particular, some questions that I have after reading this manuscript are: (1) Would the MODIS-based GPP estimates similarly find that 2018-2019 differences in GPP to be <4% with 28% of the variations explained by these four events? (2) Do MODIS-based GPP estimates show less IAV for forest ecosystems, as suggested by NIRv? (3) SIF and NIRv may underestimate drought-induced GPP reductions (e.g., He et al., 2020), what are the differences in drought-induced GPP reductions for TROPOMI-based and MODIS-based GPP? I encourage the authors to provide a comparison of the GPP estimated in this analysis with MODIS-based estimates.

The manuscript does not provide much discussion of the uncertainties associated with these GPP estimates, and it is unclear if the GPP product provided with this analysis has associated uncertainties. I encourage the authors to include an uncertainty estimate with the data product and explain these uncertainties in the text. Presumably, an uncertainty estimate could be obtained from the uncertainty in the SIF-GPP regression.

Specific comments

P2 L18-20: Please re-word this sentence. Drought and flooding are drivers of IAV but seasonal redistribution is a response.

P2L19: Check citation format. Many instances where “Author (year)” should be “(Author, year)”

P3L6: “partitioned by the group operating the site”. Is this always nighttime partitioning? Or does it vary between sites?

P3L8: It is not clear what product is being used to define the IGBP product and version number (note that there are large changes in v6 of MODIS product).

P4L4: “small signal” is “small SIF signal”?

P4L7-16: A little bit more detail could be given in this paragraph. Are you performing the cluster analysis on the 500 m gridcells?

P4L15: “most robust” – how is this determined?

Figure 2: The colors for mixed forest and deciduous broadleaf are hard to distinguish and the histograms largely overlap. I suggest switching these to more contrasting colors.

P7L11: “(500 mm vs 1000 mm)” – I could not find where the precipitation dataset is described. Please check that the precipitation dataset is described and cited.

P7L30: “toto”

References

He et al. (2020). Tracking seasonal and interannual variability in photosynthetic downregulation in response to water stress at a temperate deciduous forest. Journal of Geophysical Research:Biogeosciences, 125, e2018JG005002.https://doi.org/10.1029/2018JG005002

Joiner, Joanna, and Yasuko Yoshida. "Satellite-based reflectances capture large fraction of variability in global gross primary production (GPP) at weekly time scales." Agricultural and Forest Meteorology 291 (2020): 108092. https://doi.org/10.1016/j.agrformet.2020.108092

Jung et al. Scaling carbon fluxes from eddy covariance sites to globe: synthesis and evaluation of the FLUXCOM approach, Biogeosciences, 17, 1343–1365, https://doi.org/10.5194/bg-17-1343-2020, 2020.

Turner, A. J., Köhler, P., Magney, T. S., Frankenberg, C., Fung, I., and Cohen, R. C.: A double peak in the seasonality of California's photosynthesis as observed from space, Biogeosciences, 17, 405–422, https://doi.org/10.5194/bg-17-405-2020, 2020.

Turner and others use SIF observations to estimate GPP across the U.S. and note that its interannual variability is driven in large part by extreme events. There are many interesting elements to the manuscript, but many aspects were difficult to follow and/or incompletely described which made it difficult to be confident in the results.

Referencing could be improved in many places (e.g. lines 19 & 22. On p. 2. Consecutive line numbering is so helpful, please don’t re-start the line numbers on every page as a courtesy to reviewers.)

Figure 1: I have questions. Some of the sites shown are meant to study lakes or are in mountainous terrain, but it is hard to tell. Is there no list of sites used? Such a table would be extremely useful in the Supplement, and also to credit the data providers for their efforts in making the data available. At least one, if not more, appears to be a NEON site (anything starting with ‘x’), which is fine but NEON should be credited. Ah, I see now that the sites are listed in the Acknowledgements. This is nice but a table would be more useful to the reader. (And US-Men is meant to study a lake. A table with ecosystem type and latitude/longitude would be helpful all around.)

Why were no eddy covariance sites in three of the four areas denoted as important for interannual variability (Texas, South Dakota, and Illinois/Indiana/Ohio) used? I understand that data are only intermittently available, but the Nebraska Mead sites may be a reasonable stand-in and the Indiana sites may be helpful.

How was GPP estimated? Was this consistently using the nighttime (Reichstein et al., 2005 or similar) approach? If so was it consistently with the Reichstein algorithm? This uses a unique u* threshold every few months and respiration model parameters that change as a function of time. If these are interspersed with GPP estimates that use a different approach there will be differences in seasonality of GPP estimates due to methodological differences alone.

Figure 2: I’m not entirely convinced that the ‘dominant cluster’ approach is useful or even necessary given that the peaks of the pdfs vary between about 15 (mixed forest) and 17 (evergreen needleleaf forest) and that estimating these land cover types using MODIS is rather well-established.

In Table 1, is the value behind the +/- sign the standard error of the mean or the standard deviation? (I’m assuming its not the variance). The table legend was not described in very much detail.

Per the previous comment, the structure of the manuscript was a bit bewildering. It was difficult to determine how the methodology took place because methods were interspersed throughout the manuscript starting on Page 1 with the equations. For example, I appreciate that uncertainty is (mostly) noted about carbon flux estimates but how is this uncertainty determined? Is the bootstrapping approach used to determine the uncertainty of the SIF-GPP relationship which is then propagated? Is uncertainty owing from the 16-day moving window used?

Per the previous comment again, extreme events often happen quickly by definition. Is a 16-day moving window sufficient to fully describe how flooding of flack drought for example impacts ecosystems? I appreciate that the proposed precipitation mechanisms are described as ‘hypothesized’ and the notion that precipitation is the culprit makes great sense, but the devil might be in the details, which were not described again in sufficient detail.

30: GPP does not scale linearly with PAR; the GPP/PAR relationship will usually be saturated at 1:30 pm during the growing season. How does this impact equation 4?

Please note the typo in the legend of Figure 3.