the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 18 Sep 2024
Bio-climatic factors drive spectral vegetation changes in Greenland
Abstract. The terrestrial Greenland ecosystem (ice-free area) has undergone significant changes over the past decades, affecting biodiversity. Changes in air-temperature and precipitation have modified the duration and conditions of snowpack during the cold season, altering ecosystem interactions and functioning. In this study, we statistically aggregated the Copernicus Arctic regional reanalysis (CARRA) and remotely-sensed spectral vegetation data from 1991 to 2023 by using principal component analysis (PCA), in order to I. examine key sub-surface and above-surface bio-climatic factors influencing ecological and phenological processes preceding and during the thermal growing season in tundra ecosystems; II. interpret spatio-temporal interactions among bio-climatic factors on vegetation across Greenland; III. investigate bio-climatic changes dependent on location and elevation in Greenland; IV. identify regions of ongoing changes in vegetation distribution.
Consistent with other studies, PCA effectively clustered bio-climatic indicators that co-vary with summer spectral vegetation, demonstrating the potential of CARRA for biogeographic studies. The duration of the thermal growing season (GrowDays) emerged as the pivotal factor across all ecoregions (with increases up to 10 days per decade), interacting with other bio-climatic indicators to promote vegetation growth. Regions with significant snow height decrease occur along with an earlier snowmelt period (up to 20 days per decade), which triggers the onset of GrowDays earlier. In most regions, we find that shallower snowpacks tend to melt slower. We hypothesise that slow snowmelt rates foster microbial activity, enriching the soil with nutrients. The combined effect of soil nutrients and the resulting warming in spring (up to 1.5 ºC per decade), promotes early plant development. These bio-climatic changes, in the cold and summer season, have led to northward and upward vegetation expansion. The distribution of vegetation has expanded in Northeast Greenland by 22.5 % increase with respect to 2008–2023, leading to new vegetated areas. We report little to no change in the length and onset of the GrowDays along the coast in Northeast Greenland, in contrast with more pronounced changes inland and at higher elevations, hence showing an elevation-dependent response (increases up to 5 days per decade per km elevation). Our study determines a set of bio-climatic indicators relevant for understanding vegetation. These insights provide a basis to validate bio-climatic indicators from climate models to assess future vegetation changes across Greenland under a changing climate.
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RC1: 'Comment on egusphere-2024-2571', Rúna Magnússon, 20 Oct 2024
Dear authors, dear editor
Thank you for inviting me to review “Bio-climatic factors drive spectral vegetation changes in Greenland”, by T. Silva et al. for Biogeosciences. The manuscript explores the role of a wide range of bio-climatic factors in explaining satellite-derived vegetation dynamics in Greenland. The authors aimed to identify which sub-surface and above-surface climate factors were associated with greening in Greenland, and how such associations differed among ecoregions and latitudinal and altitudinal gradients. They report that increases in the duration of the thermal growing season show the strongest association with greening, with additional influences of snowpack dynamics, and differential strength of association across regions and altitudinal and latitudinal gradients.
This study is relevant in the context of rapid ongoing climate change in the Arctic, observed dynamics of “Arctic greening” and their implications for the future functioning of tundra ecosystems. The authors analyze a substantial amount of data for a large region, using various sources and environmental disciplines in a holistic and, generally, appropriate way. The manuscript is well within the scope of Biogeosciences and presents a relevant and timely case. I do, however, have several major concerns about some of the methodological choices and the structuring and argumentation of the work. I advise a round of thorough revision and rewriting of substantial parts of the manuscript before it can be considered for publication. This has resulted in a rather lengthy review report, but I would also like to stress that many of the points I raise are interrelated or specific examples of the major points, so I hope it is not discouraging. I am sure the ms will find a good home in a respected journal.
I have performed this review together with 7 MSc students for an open review course assignment at Wageningen University. Their help has been valuable, and they appreciated the opportunity to learn from this ambitious and relevant paper, and to contribute to the scientific publishing process. We have all enjoyed this activity and we wish you all the best as the manuscript comes to full maturity!
Rúna Magnússon,
with input from Annika Robben, Djordy Potappel, Aron den Exter, Muriël de Vries, Rikuto Shinagawa, Yente Reniers and Yorick Kwakkel.Major comments
- I hope the authors can make clarify how the potential mismatches between AVHRR and VIIRS NDVI products (e.g. masking differences) have been accounted for during statistical analysis and trend detection. Explanations on how this was done are sparse and not sufficiently clear to understand the implications. Beside adding the shaded min-max range in Fig. 2 (that I also don’t fully understand the procedure behind, can this be clarified?), how did you prevent the use of two different records and sensors from affecting your temporal trends? And especially, how do you prevent this from unduly influencing the comparison between 2008-2023 and 1991-2007, that you describe in L. 380-392? This appears to be based on counts of NDVI > 0.15, where differences in bandwidth and snow/water/cloud detection easily become problematic. Miura et al. (2012) may be an appropriate source to evaluate the validity of trend detection across two satellite platforms, and you may want to statistically test for absence of trend breaks coinciding with the switch from one platform to another.
- Your methodology is ambitious and extensive, which is laudable. It does however lead to many choices during the processing of the data, and not all of these have been properly backed or described yet. Examples include (1) the use of 0.15 as an NDVI threshold without a reference, (2) the described use of CryoClim data that only go to 2015 without any visible inclusion of these data throughout later analyses, (3) why has only altitude, and not for example slope aspect, been included into the study?. These, and further examples, are given in the minor comments. I suggest that the authors critically go through every step in the methodology and check whether all choices are described in sufficient detail for an independent reader to reproduce the study, and that choices are back-up either by literature, data or statistics. If needed, details on processing can be described in a supplementary methods section to prevent disruption of the flow of the main text.
- From L. 227 onwards, it reads as if the distinction between methods, results and interpretation of results (discussion) is lost. For example: results and maps are presented in the methods in L. 227-247. New information on choices of processing, variable selection and statistical tests (Pearson correlations) are introduced in the results in L. 275-305, L. 311-314 L. 380-384 and many other places. Throughout the entire (lengthy) results section, interpretations are added that go beyond the statistical results of your own methods. Lines 320 -350 for instance are very speculative for a results section, and other paragraphs and show similar interpretation or speculation. These would be better suited for the discussion and require backing by references. Please rewrite the methods-results-discussion in such a way that: (1) all methodological choices and tests are explained in the methods (2) only numerical and statistical outcomes are presented in results (with a minimum interpretation to make the results understandable, e.g. writing out abbreviations and description of patterns) and (3) interpretation and relation to unmeasured mechanisms such as permafrost, latent heat processes or photosynthesis are only kept for the discussion.
- In the results section and abstract, observed greenness dynamics are attributed to processes such as nutrient dynamics and permafrost. This gives the reader the impression that such variables were included or that you can at least confidently attribute greening dynamics to such processes. Given the set of bioclimatic factors that were included, however, I doubt whether you can make such claims. These processes can be touched upon in the discussion, with support from literature, but should not be presented in a way that readers might think that these are actual conclusions from this study. I also think that to properly discuss their role in the discussion, you will need to evaluate several lines of reasoning more critically: are the subsurface products (soil water and soil ice) that you include, given the limited representation of subsurface dynamics in the used reanalysis products, actually representative of permafrost conditions or hydrology? How can you better argue the role of snowmelt rates in relation to microbial activity and nutrient dynamics, especially to an audience that may not be familiar with works such as musselman et al.? Because at first it is very counterintuitive that shallower snowpacks melt more slowly and with the current explanation provided, this line of argumentation is very hard to follow. I suggest you evaluate to what extent your bioclimatic variables are representative of processes such as permafrost dynamics and melt rates and nutrient dynamics, discuss their potential roles in the discussion section, and refrain from making any hard statements about their role in the abstract/results/conclusion sections.
Minor comments
- The writing could be improved by splitting up some very long compound sentences into shorter ones. I provide some examples in the “technicalities”, but I recommend a thorough re-reading for writing style and grammar.
- The abstract ends with the conclusion that you “identify a set of bioclimatic variables” and that you provide a “basis to validate bioclimatic indicators from climate models”. Your conclusions section states more or less the same. I suggest that you reflect more specifically on how exactly your findings help to achieve this (more to the point). This will hopefully also better explain how you advance the field, since the role of growing season onset and snowmelt timing are already well established in Arctic ecological studies.
- 35 – 43. Several references seem out of place in this paragraph. I suspect you mean Bjorkman et al. (2018) instead of Metcalfe et al. (2018), since Metcalfe et al. (2018) does not deal with the type of findings you describe at all, and Anne Bjorkman’s paper does. Sturm et al. (2001) is a rather old and case-specific (albeit popular) reference for shrubification of the Arctic. ITEX papers (e.g. Elmendorf et al., 2012) or syntheses (e.g. Mekonnen et al., 2021; Martin et al., 2017; Myers-Smith et al., 2011) would be more appropriate.
- 66 – 68, this proposed increase in nutrient availability under deeper snow is at odds with your statements in the abstract, results and discussion that shallower snowpacks should melt more slowly. It should be clear from the introduction onwards which snowpack properties can be expected to facilitate faster or slower melt, and how would relate to nutrient cycling. If the literature on the influence of snow dynamics on microbial turnover and nutrient availability is ambiguous in itself, then I would refrain from making any statements about nutrients as a mediating effect between snow dynamics and greenness.
- 111, here you mention the use of CryoClim data, that was chose to represent daily snow cover rather than the CARRA dataset. I do not see how this could be done since the data only goes to 2015, and this data product is not mentioned anywhere anymore in the remainder of the ms. Did you actually use it and if so, how? Perhaps it is a nice addition to incorporate data sources directly into Table 1 to resolve unclarities like this.
- 128-153: Can you give an indication of the match between AVHRRR and VIIRS? Calibration against MODIS does not seem to be the most relevant thing to mention here, since you do not use MODIS. See Miura et al. (2012), there seem to be some structural NIR differences and non-linear NDVI relationships between VIIRS and AVHRR?
- 143, why did you use an NDVI threshold of specifically 0.15?
- 146, can you provide a sharper definition of “interannual extent of vegetation”? To ecologists, this may be confusing since extent almost always refers to spatial extent.
- 147-155. It is very difficult for readers who are not intimately familiar with the AVHRR and VIIRS datasets to follow this paragraph, even though it is quite important for the quality of the results. Terms like “flag” and “n” may be unclear. Please provide more explicit description of exactly how the monthly max/mean/min nr. of valid pixels was used and how this translates to the CI’s in Fig. 2. From reading this several times I still did not understand if any correction was applied before further analysis (and looking at Fig. S1 I would expect for that to be necessary).
- 163, it would be useful to report an accuracy metric here.
- 169, why only from January onwards and not in autumn-winter previous year?
- 169-171, I have a slight doubt about the way that the melt rate is calculated here. If this basically represents the time that passes between the peak SWE and moment of complete snowmelt, and peak SWE occurs early in the winter-spring season, how representative is this timeframe really for the spring melt season and water release? Especially if heavy snowfall occurs later in spring and is followed by warming, this automatically leads to a situation where deep snow appear to melt more rapidly. As a reader, it is hard to fully grasp how such nuances in the choice of processing influence the results.
- 176, you mention rain, but rainfall does not seem to be included as a bioclimatic variable as far as I can see (Table 1, Fig. 3), while snowfall was, and rain fraction too. You refer to fig S10 for statements on the role of rain, but this figure refers to “solid precipitation” which suggests that this is about snow. Since you discuss the role of rain regularly, why not include rain (total summer season liquid precipitation) as a bio-climatic variable explicitly? This would make your conclusions and discussion points on the role of rain more explicit and justifiable.
- You could statistically back up your choice for PCA and its assumption of linear relations. You could do this by reporting axis lengths, for instance.
- 1, here results are presented, and completely new information comes in (NAO / GBI), so perhaps the figure should be presented later, in the results. I also miss a scale bar for greenness and it is unclear what “greenness” represents here (is this one the extent variables you calculated, or a mean, and are pixels < 0.15 included or not?).
- 227-247 seem to be combined methods and results. The source for the climate oscillation data, and the rationale for including them, have not been properly covered earlier in the methods. It is also unclear how the use of oscillations relates to your study aim and research questions.
- 250, Pedregosa et al does not seem like the most appropriate reference for the use of PCA. I advise to find papers that specifically deal with the considerations and strengths of using PCA in a pixel-based remote sensing context.
- 259, the use of Mann-Kendall tests is state of the art, but it appears that later on you only show results for growdays and greenness, not all bioclimatic factors as suggested here? Perhaps mention only growdays and greenness then?
- 262, please explain the use of a 90% confidence interval rather than 95%. With the vast amount of pixels at your disposal, and the relatively long timespan of the study, I would expect that the generally accepted 95% CI would be fine and I would be curious to know why you deviated from this standard.
- 271-273, the statements made here need backing; how did you test whether significant long-term trends in vegetation extent were evident? Mann-Kendall test? Could sensor discrepancies play a role here?
- 275-279, reads like methods and introduces a whole new aspect of the methodology. I would also provide some more explanation of why the use of detrended Pearson correlations is an appropriate method to evaluate linearity assumptions for a PCA.
- 290 & 296, you describe how specific variables were removed from analysis a priori. This is essential information that should go into methods, and it seems at odds with your earlier statement that variables were excluded from PCA based on contribution to cumulative explained variance. I would recommend to present a single, unambiguous criterium for the inclusion of variables into PCA and figures, in the methods. Especially since the identification of useful bio-climatic indicators was an explicit aim of the study.
- 291-292 & L. 294-295, examples of interpretation of results, and no backing (figure, reference) provided to support these interpretations.
- 311-314, I had to read this section a few times to understand the rationale and approach. So if I read correctly, you applied the PCA for all years and ecoregions separately, and then tested whether the variances explained by PC1 and PC2 were similar across the two time periods. I am not fully sure how this would demonstrate that the two NDVI records are comparable and valid in this context. The variances may be similar, but the greenness dynamics, and the associations between different variables and PC axes may not be (do I understand this correctly)? Sidenote: a lot of this information again reads like methods and not results.
- This is a nice figure! Also here, a scale bar for greenness would help the reader understand what kind of magnitudes we are talking about, across regions.
- 318-319, “PC2 is heavily shaped by continentality, permafrost extent and precipitation patterns, meaning that snow-related indicators, like SWEMAX and MeltRate have the highest explanatory power”. I struggle to see how your variables and methods could allow you to conclude anything about continentality or permafrost. This needs to be either backed up better, or (ideally) kept for the discussion. I also do not see how this means that snow related indicators are most important (snow is something different than permafrost and continentality?).
- L 320 – 350 are altogether quite speculative and many of the claims here need to be supported either by a figure, statistics or literature (and in the latter case, it is better suited for the discussion). I would advise to back up your statements much more. And please carefully evaluate whether reported drivers are really drivers, or just represent the overall role of warming (e.g. increases in rainratio cannot really be teased apart from warming effects so I do not see how you would attribute change to rainfall patterns specifically, especially if total rainfall is not included in the analysis). I think this paragraph needs a thorough rewriting.
- 349-350, please consider how this relates to the aims of the study (oscillations are not introduced anywhere), report the approach in the methods, and report the test statistics either here or in the appendix.
- 380, at this point the different terms used (here: spectral vegetation expansion) become a bit confusing. It would be nice to have a single, consistent term for each of the various manifestations of greening that you study in this paper, and present all of these early on.
- 382, see also major comments, here I was very unsure whether the differences in bandwidths and quality filtering might introduce artefacts into the comparison. Perhaps also good to remind the reader that ‘greenness’ here refers to the 0.15 threshold (related to comment above).
- 417-420, How can you demonstrate that soil ice has an additional role, additive to warming and rainratio? Aren’t they just all sides of the same coin? Could it also be, for instance, that the northern regions still feature most frozen ground conditions in summer and that in southern regions, soils were already mostly above 0 degrees in the summer season, and that hence this dynamic is mostly evident in northern regions? I would carefully read this part of the discussion and evaluate which claims can be made with certainty, and which ones just reflect collinearity within the bio-climate variables.
- Overall, the discussion would really benefit from a thematic subdivision, for instance into different sets of climate variables, or into driving mechanisms and a section on how they differ among regions? Right now the reader easily gets lost between different lines of argumentation.
- 426 – 435, I found the descriptions of slower melt of shallower snowpacks very difficult to follow (and frankly, counterintuitive, but then I am not a snow physics expert). Even if the melt rate is lower, wouldn’t the timing of complete snowmelt still be earlier for shallow snow than for deeper snow? What then is the exact role of the slower melt rate and potentially better water absorption within the context of your findings? I have a feeling that similar claims could be made about the role of deeper snow and its impact on soil temperature and microbial activity (as you also state in the introduction), so I am still in the dark about the role of melt rate in nutrient availability. I would recommend rewriting his in a way that is more accessible to readers without a background in snow physics and staying closer to your own results.
- 428, Heijmans et al (2022) doesn’t deal with the release of nutrients in relation to spring water availability. Perhaps we cite others in our review that have relevant findings on this topic, but to me this doesn’t seem to be an appropriate reference here.
- 463-465, maybe you can back up this hypothesis about the role of shrubs or potentially other species groups by checking your greenness trends against the CAVM or Karami et al. (2018)?
- 475, what exactly do you mean by “validating bio-climatic indicators”? I think you could explain your proposed course of action a bit better, and also explain how that would help understand future trends.
- The implications section reads like a rather surprising selection of several implications, of which I am not really sure if all the main ones are represented, and whether the ones that are now discussed most extensively are in fact the most important ones. For example, a lot of attention is dedicated to PBAPs and fog, but no mention is made of carbon dynamics or surface energy balance feedbacks. Even if this is deliberate, it would be good to highlight why specific implications are discussed while others are not. You do mention some of these aspects in the limitations, but they are of course also relevant from an implications perspective.
- 506 – 510, I would expect that such episodes of warm, humid conditions should be evident from your PCA analysis, so I do not see the point of mentioning the role of this particular episode as a limitation?
- 517-520, needs references for the claims made. I would like to add that while permafrost thaw can indeed release moisture or lead to ponding, deeper thaw fronts also often lead to deeper infiltration and surface drying (Liljedahl et al., 2016). This section could use more nuance and backing.
- 525 – 530, I do not want to send you back to the drawing board, but I am interested why elevation was added to your analysis, while aspect and slope were not. You rightfully stress their importance and I would (perhaps naively!) assume that it would not be such an enormous effort to include them in your analysis as well?
- Rather than reiterate what you did, you could summarize the actual findings and try to align better with the original aims (perhaps mention which set of variables or which variables show the strongest associations?) and mention the key advance you have made? This would make the conclusion more informative.
Technicalities & Language
- 10 “summer spectral vegetation”. This is an unusual term, it would be good to rephrase it or explain it so that there can be no ambiguity about what it means.
- 18 “by 22.5% increase” should be “by 22.5%”. I also recommend to be more explicit about what you mean by “the distribution of vegetation”. Do you mean that the vegetated area of Greenland (determined here as summer NDVI > 0.15?) expanded in area by 22.5%? Perhaps you want to rewrite this sentence.
- 25, what do you mean by “regional Greenland”? Perhaps that specific regions of Greenland are warming three times faster.
- 31, add “and” instead of comma between “composition” and “alterations”.
- 48, is it really necessary to mention the specific methods of Gamm et al ( ”using [..], […] and […]”)? This is not done for other papers that you cite?
- 53-55, this reads like a repetition of L. 43-44.
- 62, I do not think “snow cover melt” is a very generally used term. Maybe write “snowmelt timing” or “snow melt rate”, depending on what you mean exactly?
- 71, maybe write “large amounts of snow” rather than “large amounts of snow coverage”, since from what I understand snowpacks were also very deep, not just spatially extensive.
- 81-82, example of a grammatically confusing sentence.
- 83-86, implications for phytoplankton seem beyond the scope of your study system and I do not see the added value of discussing it here (it seems more of an implication rather than an example of the importance of subsurface flow to terrestrial vegetation).
- 105, add “the” between “to” and “CARRA”.
- 132, “and thereafter is then continued” should be “and is thereafter continued”.
- 133, add “is” between “mask” and “spectrally”.
- Figure 5) Final sentence in the caption: Do you mean that the trend was considered significant if the 90% CI of the estimate did not overlap 0? This is what I am used to. Similar for Fig. 6
- 376, replace “evidence” with “shows”?
- Table 2) perhaps a no brainer, but it would be good to explain what the fraction mean; is this % of total area of that ecoregion?
- 446, change “favourable areas” into “a more favourable area”.
- 498, change “as” into “as in”
References
Martin, A. C., Jeffers, E. S., Petrokofsky, G., Myers-Smith, I., & Macias-Fauria, M. (2017). Shrub growth and expansion in the Arctic tundra: an assessment of controlling factors using an evidence-based approach. Environmental Research Letters, 12(8), 085007.
Bjorkman, A. D., Myers-Smith, I. H., Elmendorf, S. C., Normand, S., Rüger, N., Beck, P. S., ... & Weiher, E. (2018). Plant functional trait change across a warming tundra biome. Nature, 562(7725), 57-62.
Miura, T., Turner, J. P., & Huete, A. R. (2012). Spectral compatibility of the NDVI across VIIRS, MODIS, and AVHRR: An analysis of atmospheric effects using EO-1 Hyperion. IEEE Transactions on Geoscience and Remote Sensing, 51(3), 1349-1359.
Liljedahl, A. K., Boike, J., Daanen, R. P., Fedorov, A. N., Frost, G. V., Grosse, G., ... & Zona, D. (2016). Pan-Arctic ice-wedge degradation in warming permafrost and its influence on tundra hydrology. Nature Geoscience, 9(4), 312-318.
Mekonnen, Z. A., Riley, W. J., Berner, L. T., Bouskill, N. J., Torn, M. S., Iwahana, G., ... & Grant, R. F. (2021). Arctic tundra shrubification: a review of mechanisms and impacts on ecosystem carbon balance. Environmental Research Letters, 16(5), 053001.
Citation: https://doi.org/10.5194/egusphere-2024-2571-RC1 - AC1: 'Reply on RC1', Tiago Silva, 28 Nov 2024
- I hope the authors can make clarify how the potential mismatches between AVHRR and VIIRS NDVI products (e.g. masking differences) have been accounted for during statistical analysis and trend detection. Explanations on how this was done are sparse and not sufficiently clear to understand the implications. Beside adding the shaded min-max range in Fig. 2 (that I also don’t fully understand the procedure behind, can this be clarified?), how did you prevent the use of two different records and sensors from affecting your temporal trends? And especially, how do you prevent this from unduly influencing the comparison between 2008-2023 and 1991-2007, that you describe in L. 380-392? This appears to be based on counts of NDVI > 0.15, where differences in bandwidth and snow/water/cloud detection easily become problematic. Miura et al. (2012) may be an appropriate source to evaluate the validity of trend detection across two satellite platforms, and you may want to statistically test for absence of trend breaks coinciding with the switch from one platform to another.
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RC2: 'Comment on egusphere-2024-2571', Anonymous Referee #2, 21 Oct 2024
Dear Silva et al. & the editors of Copernicus Biogeosciences,
Thank you for the invitation to review this manuscript. It's a great privilege to contribute to our scientific community. Please see the text below for my review of the manuscript, "Bio-climatic factors drive spectral vegetation changes in Greenland" by Tiago Silva et al.
This study seeks to identify bioclimatic drivers of changes in greenness and greenness distribution across Greenlands ice-free terrestrial ecosystem. Understanding the impacts of climate change on this ecosystem is extremely important, particularly in the context of recent studies highlighting changes in vegetation ("Arctic greening") and permafrost dynamics. The authors do a good job summarizing the major points of current literature in these regions and highlighting the importance of their study. The authors seek to assess these drivers by combining remotely sensed NDVI as observed from AVHRR and VIIRS between 1991 - 2023 with a gridded climate data set, the Copernicus Arctic Regional Reanalysis (CARRA). The authors use Principal Component Analysis (PCA) to identify correlations between "greenness" and a matrix of bio-climatic variables. Additionally, they use non-parametric methods to identify trends in bio-climatic indicators and assess their directionality in magnitude over time across 5 sensibly delineated ecoregion across the terrestrial Greenland ecosystem.
General CommentsI commend Silva et al. for their ambitious analysis of a substantial amount of data from a sensitive ecosystem of broad scientific interest. For this reason, it is my opinion that the study's aim is well suited for the readership of Copernicus Biogeosciences and is an important undertaking. However, I have major concerns about the implementation of methods and the interpretation of results. Most importantly, there is a critical misalignment between the stated goals of the study and the methods used to achieve these goals (as well as the title of the paper).
To summarise my concerns: The authors sought "to gain a deeper understanding of the spatio-temporal patterns of spectral vegetation changes across ice-free regions of Greenland (ln 90)" and "examine the combined effects of bio-climatic indicators ranging from sub-surface factors (such as soil water availability) to above-surface factors (such as the thermal growing season, heat stress, and frost) with summer spectral greenness (ln 91 - 95)." However, the authors provide contradictory statements about the goals of the PCA. Throughout the paper they explicitly state that they use PCA to assess drivers of *changes* in NDVI over time within a pixel, as well as having used PCA to assess drivers in changes of greenness *distribution*. Reviewing the methods and results of the PCA, it seems that the dimensionality reduction algorithm was actually used to assess bio-climate indicators that correlate with average summer spectral greenness ("greenness distribution"). I elaborate on these concerns below.
Specific comments
Major Concerns1) There is a critical misalignment between the stated goals of the study and the methods used. In Section 3.4, the authors mention that "PCA was used to investigate the combined influence among bio-climatic indicators on summer greenness _changes_" (ln 249-250; _emphasis added_). However, in the Results section, it is stated that "PCA was used to investigate the combined influence among bio-climatic indicators with summer greenness" (ln 307), which suggests an analysis of greenness levels rather than _changes_ in spectral greenness. This discrepancy is further supported by the caption for Figure 4, which notes that the biplots' scores "are colour-coded based on the summer spectral greenness as in Figure 1," where spectral greenness is defined as the "averaged spectral greenness (based on the period 1991-2023) for June, July, and August." Additionally, greenness is included in the PCA but defined differently as "seasonally averaged monthly NDVI," a quantity briefly mentioned in Section 3.1. The authors highlight that PC1 and PC2 "largely capture and explain Greenness distribution" (ln 320-321), suggesting a focus on greenness levels rather than changes.
It may be possible that the inclusion of "changes" in lines 249-250 was unintentional. However, the broader context suggests that the issue extends beyond a simple wording error. The title ("Bio-climatic factors drive spectral vegetation changes in Greenland"), the abstract (ln 10-15: "GrowDays... emerged as the pivotal factor across all ecoregions...to promote vegetation growth."), and the discussion (e.g., ln 417-419: "Our [PCA] results suggest that in the northern ecoregions, the reduction in soil ice during summer...is enabling vegetation growth, leading to northward expansion of vegetation." and ln 433-435: "The combined effect of soil nutrients with increased soil water availability in spring (SoilWaterMAM) and T2mMAM, promotes early plant growth. Therefore, leaves are more developed in early summer, which in association with increased T2mJJA and longer periods of solar radiation, allow for greener vegetation.") all imply a focus on changes in greenness values over time.
As the analysis currently stands, PCA is used to assess the variation in climate variables, which is then visually compared to average summer greenness from 1991-2023 with biplots. Separately, the authors explore trends in vegetation expansion using Mann-Kendall tests and thresholds of NDVI between two discrete periods (1991 - 2007 and 2008 - 2023). Despite a lack of generative or predictive models linking these two goals, the authors then interpret PCA loading vectors as "explaining" changes in greenness and greenness distribution. It is also not clear to me how the authors made these interpretations; I speculate this was done by visual comparison of the maps of PCs in the supplementary material with the maps of greenness distribution and greenness change over time in Figure 6.
2) Loading vectors should not be interpreted causally in the way the authors have. While it is true that alignment between two loading vectors indicate correlation and orthogonal vectors are uncorrelated, PCA is a function purely on a matrix of features without explicit regard for response variables. Since PCA is generally used for dimensionality reduction, data compression, or exploratory analysis, its application to infer causal relationships between bio-climatic factors and greenness requires further qualification. If the goal is to assess the relative importance of climate variables on changes in greenness, a causal (or at least an interpretable predictive) model is required.
3) The inclusion of "seasonally averaged" spectral greenness as a feature in the PCA and then coloring the scores in the biplots of Figure 4 based on average summer spectral greenness over the growing seasons (1991-2023) raises concerns about circular reasoning. Further clarification on how this aspect was handled could help alleviate these concerns.
4) Generally, the methods are not described in enough detail. In addition to my confusion about the methods as described above:
4a) I agree with a note from another reviewer, the calibration procedure addressing potential systematic biases between AVHRR and VIIRS NDVI should be elaborated.
4b) The calculation of "seasonally averaged NDVI" is somewhat unclear. I assume this involves averaging monthly NDVI across the growing season, but further explanation would be helpful.
4c) Given the potential impact of cloud cover and other factors on NDVI observations, more information on how observation frequency (described as "n" in Section 3.1) was used to assess uncertainty and uneven sampling would strengthen the analysis. This seems like it was at least tangentially covered given the brief mention of this in Section 3.1 and the first figure in the Supplementary Materials -- but more explanation of the procedures is needed.
4d) More details on the PCA and Mann-Kendall implementations would also be valuable. For example, when using scikit-learn for PCA, describing the optimizer and input data shape would help ensure transparency, as some solvers are better optimized for particular data configurations. Similarly, the choice of the standard Mann-Kendall test variant in pyMannKendall should be justified, especially regarding serial autocorrelation, which is an important consideration in trend analysis. While MK tests are the current state of the art for landscape-scale analysis like this, pyMannKendall offers options that seek to account for autocorrelation, and discussing whether this was assessed in the data would clarify the robustness of the trend analysis.
Minor Concerns & Technical Corrections.
In addition to minor concerns pointed out by another reviewer, there are some instances of speculation that are not supported by the PCA analysis in the results section which should removed, or moved to the discussion section and include citations. These are also specific examples of where I think a inappropriate causal interpretation of loading vectors has occurred (Major Concern 2). For example:
- (ln 326) "The decreasing trend of snow rates (SnowDJF and SnowMAM) has led to SWEMAXDOY to occur earlier. Despite the increasing trend in T2mMAM, the still-low solar elevation and the still-low near-surface air-temperatures result in low melting rates of the snowpack (MeltRate). These slow melt rates favour slow meltwater percolation (SoilWaterMAM loading vector opposite to MeltRate loading vector)."
- (ln 329) "Additionally, the earlier onset of the thermal growing season allows vegetation to produce energy via photosynthesis, particularly in the ecoregions in lower latitudes with adequate 330 sun exposure (Onset loading vector opposite to Greenness loading vector)."
- (ln 333) "Therefore, increases of RainRatioJJA promote high greenness (aligned loading vectors), as vegetation in such environmentally harsh places likely developed mechanisms to effectively retain/absorb liquid water whenever possible."
This sentence is a tautological argument:
(ln 465) "The wide-spread summer spectral greening occurs as a result of greener vegetation as certain sites."
The importance of solar radiation exposure is described as important in several places, including the conclusions, but are not included explicitly in the PCA or other analyses (ln 327, 435, 534).
Figure 4 - It would be helpful to readers if the PC1 axis was flipped for Ecoregion 2 and 4 so that the quadrants with higher greenness scores were all in the same vicinity in the biplots across Ecoregions.
The color palettes in Figures 5 and 6 rely on a reader's ability to distinguish red and green, which is a common color-blindness.
Grammar checks needed throughout.
Citation: https://doi.org/10.5194/egusphere-2024-2571-RC2 - AC2: 'Reply on RC2', Tiago Silva, 28 Nov 2024
Interactive discussion
Status: closed
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RC1: 'Comment on egusphere-2024-2571', Rúna Magnússon, 20 Oct 2024
Dear authors, dear editor
Thank you for inviting me to review “Bio-climatic factors drive spectral vegetation changes in Greenland”, by T. Silva et al. for Biogeosciences. The manuscript explores the role of a wide range of bio-climatic factors in explaining satellite-derived vegetation dynamics in Greenland. The authors aimed to identify which sub-surface and above-surface climate factors were associated with greening in Greenland, and how such associations differed among ecoregions and latitudinal and altitudinal gradients. They report that increases in the duration of the thermal growing season show the strongest association with greening, with additional influences of snowpack dynamics, and differential strength of association across regions and altitudinal and latitudinal gradients.
This study is relevant in the context of rapid ongoing climate change in the Arctic, observed dynamics of “Arctic greening” and their implications for the future functioning of tundra ecosystems. The authors analyze a substantial amount of data for a large region, using various sources and environmental disciplines in a holistic and, generally, appropriate way. The manuscript is well within the scope of Biogeosciences and presents a relevant and timely case. I do, however, have several major concerns about some of the methodological choices and the structuring and argumentation of the work. I advise a round of thorough revision and rewriting of substantial parts of the manuscript before it can be considered for publication. This has resulted in a rather lengthy review report, but I would also like to stress that many of the points I raise are interrelated or specific examples of the major points, so I hope it is not discouraging. I am sure the ms will find a good home in a respected journal.
I have performed this review together with 7 MSc students for an open review course assignment at Wageningen University. Their help has been valuable, and they appreciated the opportunity to learn from this ambitious and relevant paper, and to contribute to the scientific publishing process. We have all enjoyed this activity and we wish you all the best as the manuscript comes to full maturity!
Rúna Magnússon,
with input from Annika Robben, Djordy Potappel, Aron den Exter, Muriël de Vries, Rikuto Shinagawa, Yente Reniers and Yorick Kwakkel.Major comments
- I hope the authors can make clarify how the potential mismatches between AVHRR and VIIRS NDVI products (e.g. masking differences) have been accounted for during statistical analysis and trend detection. Explanations on how this was done are sparse and not sufficiently clear to understand the implications. Beside adding the shaded min-max range in Fig. 2 (that I also don’t fully understand the procedure behind, can this be clarified?), how did you prevent the use of two different records and sensors from affecting your temporal trends? And especially, how do you prevent this from unduly influencing the comparison between 2008-2023 and 1991-2007, that you describe in L. 380-392? This appears to be based on counts of NDVI > 0.15, where differences in bandwidth and snow/water/cloud detection easily become problematic. Miura et al. (2012) may be an appropriate source to evaluate the validity of trend detection across two satellite platforms, and you may want to statistically test for absence of trend breaks coinciding with the switch from one platform to another.
- Your methodology is ambitious and extensive, which is laudable. It does however lead to many choices during the processing of the data, and not all of these have been properly backed or described yet. Examples include (1) the use of 0.15 as an NDVI threshold without a reference, (2) the described use of CryoClim data that only go to 2015 without any visible inclusion of these data throughout later analyses, (3) why has only altitude, and not for example slope aspect, been included into the study?. These, and further examples, are given in the minor comments. I suggest that the authors critically go through every step in the methodology and check whether all choices are described in sufficient detail for an independent reader to reproduce the study, and that choices are back-up either by literature, data or statistics. If needed, details on processing can be described in a supplementary methods section to prevent disruption of the flow of the main text.
- From L. 227 onwards, it reads as if the distinction between methods, results and interpretation of results (discussion) is lost. For example: results and maps are presented in the methods in L. 227-247. New information on choices of processing, variable selection and statistical tests (Pearson correlations) are introduced in the results in L. 275-305, L. 311-314 L. 380-384 and many other places. Throughout the entire (lengthy) results section, interpretations are added that go beyond the statistical results of your own methods. Lines 320 -350 for instance are very speculative for a results section, and other paragraphs and show similar interpretation or speculation. These would be better suited for the discussion and require backing by references. Please rewrite the methods-results-discussion in such a way that: (1) all methodological choices and tests are explained in the methods (2) only numerical and statistical outcomes are presented in results (with a minimum interpretation to make the results understandable, e.g. writing out abbreviations and description of patterns) and (3) interpretation and relation to unmeasured mechanisms such as permafrost, latent heat processes or photosynthesis are only kept for the discussion.
- In the results section and abstract, observed greenness dynamics are attributed to processes such as nutrient dynamics and permafrost. This gives the reader the impression that such variables were included or that you can at least confidently attribute greening dynamics to such processes. Given the set of bioclimatic factors that were included, however, I doubt whether you can make such claims. These processes can be touched upon in the discussion, with support from literature, but should not be presented in a way that readers might think that these are actual conclusions from this study. I also think that to properly discuss their role in the discussion, you will need to evaluate several lines of reasoning more critically: are the subsurface products (soil water and soil ice) that you include, given the limited representation of subsurface dynamics in the used reanalysis products, actually representative of permafrost conditions or hydrology? How can you better argue the role of snowmelt rates in relation to microbial activity and nutrient dynamics, especially to an audience that may not be familiar with works such as musselman et al.? Because at first it is very counterintuitive that shallower snowpacks melt more slowly and with the current explanation provided, this line of argumentation is very hard to follow. I suggest you evaluate to what extent your bioclimatic variables are representative of processes such as permafrost dynamics and melt rates and nutrient dynamics, discuss their potential roles in the discussion section, and refrain from making any hard statements about their role in the abstract/results/conclusion sections.
Minor comments
- The writing could be improved by splitting up some very long compound sentences into shorter ones. I provide some examples in the “technicalities”, but I recommend a thorough re-reading for writing style and grammar.
- The abstract ends with the conclusion that you “identify a set of bioclimatic variables” and that you provide a “basis to validate bioclimatic indicators from climate models”. Your conclusions section states more or less the same. I suggest that you reflect more specifically on how exactly your findings help to achieve this (more to the point). This will hopefully also better explain how you advance the field, since the role of growing season onset and snowmelt timing are already well established in Arctic ecological studies.
- 35 – 43. Several references seem out of place in this paragraph. I suspect you mean Bjorkman et al. (2018) instead of Metcalfe et al. (2018), since Metcalfe et al. (2018) does not deal with the type of findings you describe at all, and Anne Bjorkman’s paper does. Sturm et al. (2001) is a rather old and case-specific (albeit popular) reference for shrubification of the Arctic. ITEX papers (e.g. Elmendorf et al., 2012) or syntheses (e.g. Mekonnen et al., 2021; Martin et al., 2017; Myers-Smith et al., 2011) would be more appropriate.
- 66 – 68, this proposed increase in nutrient availability under deeper snow is at odds with your statements in the abstract, results and discussion that shallower snowpacks should melt more slowly. It should be clear from the introduction onwards which snowpack properties can be expected to facilitate faster or slower melt, and how would relate to nutrient cycling. If the literature on the influence of snow dynamics on microbial turnover and nutrient availability is ambiguous in itself, then I would refrain from making any statements about nutrients as a mediating effect between snow dynamics and greenness.
- 111, here you mention the use of CryoClim data, that was chose to represent daily snow cover rather than the CARRA dataset. I do not see how this could be done since the data only goes to 2015, and this data product is not mentioned anywhere anymore in the remainder of the ms. Did you actually use it and if so, how? Perhaps it is a nice addition to incorporate data sources directly into Table 1 to resolve unclarities like this.
- 128-153: Can you give an indication of the match between AVHRRR and VIIRS? Calibration against MODIS does not seem to be the most relevant thing to mention here, since you do not use MODIS. See Miura et al. (2012), there seem to be some structural NIR differences and non-linear NDVI relationships between VIIRS and AVHRR?
- 143, why did you use an NDVI threshold of specifically 0.15?
- 146, can you provide a sharper definition of “interannual extent of vegetation”? To ecologists, this may be confusing since extent almost always refers to spatial extent.
- 147-155. It is very difficult for readers who are not intimately familiar with the AVHRR and VIIRS datasets to follow this paragraph, even though it is quite important for the quality of the results. Terms like “flag” and “n” may be unclear. Please provide more explicit description of exactly how the monthly max/mean/min nr. of valid pixels was used and how this translates to the CI’s in Fig. 2. From reading this several times I still did not understand if any correction was applied before further analysis (and looking at Fig. S1 I would expect for that to be necessary).
- 163, it would be useful to report an accuracy metric here.
- 169, why only from January onwards and not in autumn-winter previous year?
- 169-171, I have a slight doubt about the way that the melt rate is calculated here. If this basically represents the time that passes between the peak SWE and moment of complete snowmelt, and peak SWE occurs early in the winter-spring season, how representative is this timeframe really for the spring melt season and water release? Especially if heavy snowfall occurs later in spring and is followed by warming, this automatically leads to a situation where deep snow appear to melt more rapidly. As a reader, it is hard to fully grasp how such nuances in the choice of processing influence the results.
- 176, you mention rain, but rainfall does not seem to be included as a bioclimatic variable as far as I can see (Table 1, Fig. 3), while snowfall was, and rain fraction too. You refer to fig S10 for statements on the role of rain, but this figure refers to “solid precipitation” which suggests that this is about snow. Since you discuss the role of rain regularly, why not include rain (total summer season liquid precipitation) as a bio-climatic variable explicitly? This would make your conclusions and discussion points on the role of rain more explicit and justifiable.
- You could statistically back up your choice for PCA and its assumption of linear relations. You could do this by reporting axis lengths, for instance.
- 1, here results are presented, and completely new information comes in (NAO / GBI), so perhaps the figure should be presented later, in the results. I also miss a scale bar for greenness and it is unclear what “greenness” represents here (is this one the extent variables you calculated, or a mean, and are pixels < 0.15 included or not?).
- 227-247 seem to be combined methods and results. The source for the climate oscillation data, and the rationale for including them, have not been properly covered earlier in the methods. It is also unclear how the use of oscillations relates to your study aim and research questions.
- 250, Pedregosa et al does not seem like the most appropriate reference for the use of PCA. I advise to find papers that specifically deal with the considerations and strengths of using PCA in a pixel-based remote sensing context.
- 259, the use of Mann-Kendall tests is state of the art, but it appears that later on you only show results for growdays and greenness, not all bioclimatic factors as suggested here? Perhaps mention only growdays and greenness then?
- 262, please explain the use of a 90% confidence interval rather than 95%. With the vast amount of pixels at your disposal, and the relatively long timespan of the study, I would expect that the generally accepted 95% CI would be fine and I would be curious to know why you deviated from this standard.
- 271-273, the statements made here need backing; how did you test whether significant long-term trends in vegetation extent were evident? Mann-Kendall test? Could sensor discrepancies play a role here?
- 275-279, reads like methods and introduces a whole new aspect of the methodology. I would also provide some more explanation of why the use of detrended Pearson correlations is an appropriate method to evaluate linearity assumptions for a PCA.
- 290 & 296, you describe how specific variables were removed from analysis a priori. This is essential information that should go into methods, and it seems at odds with your earlier statement that variables were excluded from PCA based on contribution to cumulative explained variance. I would recommend to present a single, unambiguous criterium for the inclusion of variables into PCA and figures, in the methods. Especially since the identification of useful bio-climatic indicators was an explicit aim of the study.
- 291-292 & L. 294-295, examples of interpretation of results, and no backing (figure, reference) provided to support these interpretations.
- 311-314, I had to read this section a few times to understand the rationale and approach. So if I read correctly, you applied the PCA for all years and ecoregions separately, and then tested whether the variances explained by PC1 and PC2 were similar across the two time periods. I am not fully sure how this would demonstrate that the two NDVI records are comparable and valid in this context. The variances may be similar, but the greenness dynamics, and the associations between different variables and PC axes may not be (do I understand this correctly)? Sidenote: a lot of this information again reads like methods and not results.
- This is a nice figure! Also here, a scale bar for greenness would help the reader understand what kind of magnitudes we are talking about, across regions.
- 318-319, “PC2 is heavily shaped by continentality, permafrost extent and precipitation patterns, meaning that snow-related indicators, like SWEMAX and MeltRate have the highest explanatory power”. I struggle to see how your variables and methods could allow you to conclude anything about continentality or permafrost. This needs to be either backed up better, or (ideally) kept for the discussion. I also do not see how this means that snow related indicators are most important (snow is something different than permafrost and continentality?).
- L 320 – 350 are altogether quite speculative and many of the claims here need to be supported either by a figure, statistics or literature (and in the latter case, it is better suited for the discussion). I would advise to back up your statements much more. And please carefully evaluate whether reported drivers are really drivers, or just represent the overall role of warming (e.g. increases in rainratio cannot really be teased apart from warming effects so I do not see how you would attribute change to rainfall patterns specifically, especially if total rainfall is not included in the analysis). I think this paragraph needs a thorough rewriting.
- 349-350, please consider how this relates to the aims of the study (oscillations are not introduced anywhere), report the approach in the methods, and report the test statistics either here or in the appendix.
- 380, at this point the different terms used (here: spectral vegetation expansion) become a bit confusing. It would be nice to have a single, consistent term for each of the various manifestations of greening that you study in this paper, and present all of these early on.
- 382, see also major comments, here I was very unsure whether the differences in bandwidths and quality filtering might introduce artefacts into the comparison. Perhaps also good to remind the reader that ‘greenness’ here refers to the 0.15 threshold (related to comment above).
- 417-420, How can you demonstrate that soil ice has an additional role, additive to warming and rainratio? Aren’t they just all sides of the same coin? Could it also be, for instance, that the northern regions still feature most frozen ground conditions in summer and that in southern regions, soils were already mostly above 0 degrees in the summer season, and that hence this dynamic is mostly evident in northern regions? I would carefully read this part of the discussion and evaluate which claims can be made with certainty, and which ones just reflect collinearity within the bio-climate variables.
- Overall, the discussion would really benefit from a thematic subdivision, for instance into different sets of climate variables, or into driving mechanisms and a section on how they differ among regions? Right now the reader easily gets lost between different lines of argumentation.
- 426 – 435, I found the descriptions of slower melt of shallower snowpacks very difficult to follow (and frankly, counterintuitive, but then I am not a snow physics expert). Even if the melt rate is lower, wouldn’t the timing of complete snowmelt still be earlier for shallow snow than for deeper snow? What then is the exact role of the slower melt rate and potentially better water absorption within the context of your findings? I have a feeling that similar claims could be made about the role of deeper snow and its impact on soil temperature and microbial activity (as you also state in the introduction), so I am still in the dark about the role of melt rate in nutrient availability. I would recommend rewriting his in a way that is more accessible to readers without a background in snow physics and staying closer to your own results.
- 428, Heijmans et al (2022) doesn’t deal with the release of nutrients in relation to spring water availability. Perhaps we cite others in our review that have relevant findings on this topic, but to me this doesn’t seem to be an appropriate reference here.
- 463-465, maybe you can back up this hypothesis about the role of shrubs or potentially other species groups by checking your greenness trends against the CAVM or Karami et al. (2018)?
- 475, what exactly do you mean by “validating bio-climatic indicators”? I think you could explain your proposed course of action a bit better, and also explain how that would help understand future trends.
- The implications section reads like a rather surprising selection of several implications, of which I am not really sure if all the main ones are represented, and whether the ones that are now discussed most extensively are in fact the most important ones. For example, a lot of attention is dedicated to PBAPs and fog, but no mention is made of carbon dynamics or surface energy balance feedbacks. Even if this is deliberate, it would be good to highlight why specific implications are discussed while others are not. You do mention some of these aspects in the limitations, but they are of course also relevant from an implications perspective.
- 506 – 510, I would expect that such episodes of warm, humid conditions should be evident from your PCA analysis, so I do not see the point of mentioning the role of this particular episode as a limitation?
- 517-520, needs references for the claims made. I would like to add that while permafrost thaw can indeed release moisture or lead to ponding, deeper thaw fronts also often lead to deeper infiltration and surface drying (Liljedahl et al., 2016). This section could use more nuance and backing.
- 525 – 530, I do not want to send you back to the drawing board, but I am interested why elevation was added to your analysis, while aspect and slope were not. You rightfully stress their importance and I would (perhaps naively!) assume that it would not be such an enormous effort to include them in your analysis as well?
- Rather than reiterate what you did, you could summarize the actual findings and try to align better with the original aims (perhaps mention which set of variables or which variables show the strongest associations?) and mention the key advance you have made? This would make the conclusion more informative.
Technicalities & Language
- 10 “summer spectral vegetation”. This is an unusual term, it would be good to rephrase it or explain it so that there can be no ambiguity about what it means.
- 18 “by 22.5% increase” should be “by 22.5%”. I also recommend to be more explicit about what you mean by “the distribution of vegetation”. Do you mean that the vegetated area of Greenland (determined here as summer NDVI > 0.15?) expanded in area by 22.5%? Perhaps you want to rewrite this sentence.
- 25, what do you mean by “regional Greenland”? Perhaps that specific regions of Greenland are warming three times faster.
- 31, add “and” instead of comma between “composition” and “alterations”.
- 48, is it really necessary to mention the specific methods of Gamm et al ( ”using [..], […] and […]”)? This is not done for other papers that you cite?
- 53-55, this reads like a repetition of L. 43-44.
- 62, I do not think “snow cover melt” is a very generally used term. Maybe write “snowmelt timing” or “snow melt rate”, depending on what you mean exactly?
- 71, maybe write “large amounts of snow” rather than “large amounts of snow coverage”, since from what I understand snowpacks were also very deep, not just spatially extensive.
- 81-82, example of a grammatically confusing sentence.
- 83-86, implications for phytoplankton seem beyond the scope of your study system and I do not see the added value of discussing it here (it seems more of an implication rather than an example of the importance of subsurface flow to terrestrial vegetation).
- 105, add “the” between “to” and “CARRA”.
- 132, “and thereafter is then continued” should be “and is thereafter continued”.
- 133, add “is” between “mask” and “spectrally”.
- Figure 5) Final sentence in the caption: Do you mean that the trend was considered significant if the 90% CI of the estimate did not overlap 0? This is what I am used to. Similar for Fig. 6
- 376, replace “evidence” with “shows”?
- Table 2) perhaps a no brainer, but it would be good to explain what the fraction mean; is this % of total area of that ecoregion?
- 446, change “favourable areas” into “a more favourable area”.
- 498, change “as” into “as in”
References
Martin, A. C., Jeffers, E. S., Petrokofsky, G., Myers-Smith, I., & Macias-Fauria, M. (2017). Shrub growth and expansion in the Arctic tundra: an assessment of controlling factors using an evidence-based approach. Environmental Research Letters, 12(8), 085007.
Bjorkman, A. D., Myers-Smith, I. H., Elmendorf, S. C., Normand, S., Rüger, N., Beck, P. S., ... & Weiher, E. (2018). Plant functional trait change across a warming tundra biome. Nature, 562(7725), 57-62.
Miura, T., Turner, J. P., & Huete, A. R. (2012). Spectral compatibility of the NDVI across VIIRS, MODIS, and AVHRR: An analysis of atmospheric effects using EO-1 Hyperion. IEEE Transactions on Geoscience and Remote Sensing, 51(3), 1349-1359.
Liljedahl, A. K., Boike, J., Daanen, R. P., Fedorov, A. N., Frost, G. V., Grosse, G., ... & Zona, D. (2016). Pan-Arctic ice-wedge degradation in warming permafrost and its influence on tundra hydrology. Nature Geoscience, 9(4), 312-318.
Mekonnen, Z. A., Riley, W. J., Berner, L. T., Bouskill, N. J., Torn, M. S., Iwahana, G., ... & Grant, R. F. (2021). Arctic tundra shrubification: a review of mechanisms and impacts on ecosystem carbon balance. Environmental Research Letters, 16(5), 053001.
Citation: https://doi.org/10.5194/egusphere-2024-2571-RC1 - AC1: 'Reply on RC1', Tiago Silva, 28 Nov 2024
- I hope the authors can make clarify how the potential mismatches between AVHRR and VIIRS NDVI products (e.g. masking differences) have been accounted for during statistical analysis and trend detection. Explanations on how this was done are sparse and not sufficiently clear to understand the implications. Beside adding the shaded min-max range in Fig. 2 (that I also don’t fully understand the procedure behind, can this be clarified?), how did you prevent the use of two different records and sensors from affecting your temporal trends? And especially, how do you prevent this from unduly influencing the comparison between 2008-2023 and 1991-2007, that you describe in L. 380-392? This appears to be based on counts of NDVI > 0.15, where differences in bandwidth and snow/water/cloud detection easily become problematic. Miura et al. (2012) may be an appropriate source to evaluate the validity of trend detection across two satellite platforms, and you may want to statistically test for absence of trend breaks coinciding with the switch from one platform to another.
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RC2: 'Comment on egusphere-2024-2571', Anonymous Referee #2, 21 Oct 2024
Dear Silva et al. & the editors of Copernicus Biogeosciences,
Thank you for the invitation to review this manuscript. It's a great privilege to contribute to our scientific community. Please see the text below for my review of the manuscript, "Bio-climatic factors drive spectral vegetation changes in Greenland" by Tiago Silva et al.
This study seeks to identify bioclimatic drivers of changes in greenness and greenness distribution across Greenlands ice-free terrestrial ecosystem. Understanding the impacts of climate change on this ecosystem is extremely important, particularly in the context of recent studies highlighting changes in vegetation ("Arctic greening") and permafrost dynamics. The authors do a good job summarizing the major points of current literature in these regions and highlighting the importance of their study. The authors seek to assess these drivers by combining remotely sensed NDVI as observed from AVHRR and VIIRS between 1991 - 2023 with a gridded climate data set, the Copernicus Arctic Regional Reanalysis (CARRA). The authors use Principal Component Analysis (PCA) to identify correlations between "greenness" and a matrix of bio-climatic variables. Additionally, they use non-parametric methods to identify trends in bio-climatic indicators and assess their directionality in magnitude over time across 5 sensibly delineated ecoregion across the terrestrial Greenland ecosystem.
General CommentsI commend Silva et al. for their ambitious analysis of a substantial amount of data from a sensitive ecosystem of broad scientific interest. For this reason, it is my opinion that the study's aim is well suited for the readership of Copernicus Biogeosciences and is an important undertaking. However, I have major concerns about the implementation of methods and the interpretation of results. Most importantly, there is a critical misalignment between the stated goals of the study and the methods used to achieve these goals (as well as the title of the paper).
To summarise my concerns: The authors sought "to gain a deeper understanding of the spatio-temporal patterns of spectral vegetation changes across ice-free regions of Greenland (ln 90)" and "examine the combined effects of bio-climatic indicators ranging from sub-surface factors (such as soil water availability) to above-surface factors (such as the thermal growing season, heat stress, and frost) with summer spectral greenness (ln 91 - 95)." However, the authors provide contradictory statements about the goals of the PCA. Throughout the paper they explicitly state that they use PCA to assess drivers of *changes* in NDVI over time within a pixel, as well as having used PCA to assess drivers in changes of greenness *distribution*. Reviewing the methods and results of the PCA, it seems that the dimensionality reduction algorithm was actually used to assess bio-climate indicators that correlate with average summer spectral greenness ("greenness distribution"). I elaborate on these concerns below.
Specific comments
Major Concerns1) There is a critical misalignment between the stated goals of the study and the methods used. In Section 3.4, the authors mention that "PCA was used to investigate the combined influence among bio-climatic indicators on summer greenness _changes_" (ln 249-250; _emphasis added_). However, in the Results section, it is stated that "PCA was used to investigate the combined influence among bio-climatic indicators with summer greenness" (ln 307), which suggests an analysis of greenness levels rather than _changes_ in spectral greenness. This discrepancy is further supported by the caption for Figure 4, which notes that the biplots' scores "are colour-coded based on the summer spectral greenness as in Figure 1," where spectral greenness is defined as the "averaged spectral greenness (based on the period 1991-2023) for June, July, and August." Additionally, greenness is included in the PCA but defined differently as "seasonally averaged monthly NDVI," a quantity briefly mentioned in Section 3.1. The authors highlight that PC1 and PC2 "largely capture and explain Greenness distribution" (ln 320-321), suggesting a focus on greenness levels rather than changes.
It may be possible that the inclusion of "changes" in lines 249-250 was unintentional. However, the broader context suggests that the issue extends beyond a simple wording error. The title ("Bio-climatic factors drive spectral vegetation changes in Greenland"), the abstract (ln 10-15: "GrowDays... emerged as the pivotal factor across all ecoregions...to promote vegetation growth."), and the discussion (e.g., ln 417-419: "Our [PCA] results suggest that in the northern ecoregions, the reduction in soil ice during summer...is enabling vegetation growth, leading to northward expansion of vegetation." and ln 433-435: "The combined effect of soil nutrients with increased soil water availability in spring (SoilWaterMAM) and T2mMAM, promotes early plant growth. Therefore, leaves are more developed in early summer, which in association with increased T2mJJA and longer periods of solar radiation, allow for greener vegetation.") all imply a focus on changes in greenness values over time.
As the analysis currently stands, PCA is used to assess the variation in climate variables, which is then visually compared to average summer greenness from 1991-2023 with biplots. Separately, the authors explore trends in vegetation expansion using Mann-Kendall tests and thresholds of NDVI between two discrete periods (1991 - 2007 and 2008 - 2023). Despite a lack of generative or predictive models linking these two goals, the authors then interpret PCA loading vectors as "explaining" changes in greenness and greenness distribution. It is also not clear to me how the authors made these interpretations; I speculate this was done by visual comparison of the maps of PCs in the supplementary material with the maps of greenness distribution and greenness change over time in Figure 6.
2) Loading vectors should not be interpreted causally in the way the authors have. While it is true that alignment between two loading vectors indicate correlation and orthogonal vectors are uncorrelated, PCA is a function purely on a matrix of features without explicit regard for response variables. Since PCA is generally used for dimensionality reduction, data compression, or exploratory analysis, its application to infer causal relationships between bio-climatic factors and greenness requires further qualification. If the goal is to assess the relative importance of climate variables on changes in greenness, a causal (or at least an interpretable predictive) model is required.
3) The inclusion of "seasonally averaged" spectral greenness as a feature in the PCA and then coloring the scores in the biplots of Figure 4 based on average summer spectral greenness over the growing seasons (1991-2023) raises concerns about circular reasoning. Further clarification on how this aspect was handled could help alleviate these concerns.
4) Generally, the methods are not described in enough detail. In addition to my confusion about the methods as described above:
4a) I agree with a note from another reviewer, the calibration procedure addressing potential systematic biases between AVHRR and VIIRS NDVI should be elaborated.
4b) The calculation of "seasonally averaged NDVI" is somewhat unclear. I assume this involves averaging monthly NDVI across the growing season, but further explanation would be helpful.
4c) Given the potential impact of cloud cover and other factors on NDVI observations, more information on how observation frequency (described as "n" in Section 3.1) was used to assess uncertainty and uneven sampling would strengthen the analysis. This seems like it was at least tangentially covered given the brief mention of this in Section 3.1 and the first figure in the Supplementary Materials -- but more explanation of the procedures is needed.
4d) More details on the PCA and Mann-Kendall implementations would also be valuable. For example, when using scikit-learn for PCA, describing the optimizer and input data shape would help ensure transparency, as some solvers are better optimized for particular data configurations. Similarly, the choice of the standard Mann-Kendall test variant in pyMannKendall should be justified, especially regarding serial autocorrelation, which is an important consideration in trend analysis. While MK tests are the current state of the art for landscape-scale analysis like this, pyMannKendall offers options that seek to account for autocorrelation, and discussing whether this was assessed in the data would clarify the robustness of the trend analysis.
Minor Concerns & Technical Corrections.
In addition to minor concerns pointed out by another reviewer, there are some instances of speculation that are not supported by the PCA analysis in the results section which should removed, or moved to the discussion section and include citations. These are also specific examples of where I think a inappropriate causal interpretation of loading vectors has occurred (Major Concern 2). For example:
- (ln 326) "The decreasing trend of snow rates (SnowDJF and SnowMAM) has led to SWEMAXDOY to occur earlier. Despite the increasing trend in T2mMAM, the still-low solar elevation and the still-low near-surface air-temperatures result in low melting rates of the snowpack (MeltRate). These slow melt rates favour slow meltwater percolation (SoilWaterMAM loading vector opposite to MeltRate loading vector)."
- (ln 329) "Additionally, the earlier onset of the thermal growing season allows vegetation to produce energy via photosynthesis, particularly in the ecoregions in lower latitudes with adequate 330 sun exposure (Onset loading vector opposite to Greenness loading vector)."
- (ln 333) "Therefore, increases of RainRatioJJA promote high greenness (aligned loading vectors), as vegetation in such environmentally harsh places likely developed mechanisms to effectively retain/absorb liquid water whenever possible."
This sentence is a tautological argument:
(ln 465) "The wide-spread summer spectral greening occurs as a result of greener vegetation as certain sites."
The importance of solar radiation exposure is described as important in several places, including the conclusions, but are not included explicitly in the PCA or other analyses (ln 327, 435, 534).
Figure 4 - It would be helpful to readers if the PC1 axis was flipped for Ecoregion 2 and 4 so that the quadrants with higher greenness scores were all in the same vicinity in the biplots across Ecoregions.
The color palettes in Figures 5 and 6 rely on a reader's ability to distinguish red and green, which is a common color-blindness.
Grammar checks needed throughout.
Citation: https://doi.org/10.5194/egusphere-2024-2571-RC2 - AC2: 'Reply on RC2', Tiago Silva, 28 Nov 2024
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Tiago Silva
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