GENERAL COMMENT

The paper presents MIRS predictions of soil total C and N concentrations (TC, TN) in six regions of Central Africa separately, using the AfSIS Sub-Saharan library with no Central African soils (Strategy 1), possibly completed with the samples from the five other regions (Strategy 2), possibly completed with spiking samples from the same region (Strategy 3). This is done with the Memory-based learning (MBL) regression procedure, which uses spectral calibration neighbors for building a PLS regression for each target sample individually.

This is very interesting, but the paper suffers several drawbacks. Some methodological aspects are not presented (selection of the number of latent variables in global calibrations developed for optimizing spectral pretreatment; window size for calculating spectral similarity; possible cut-off value for spectral similarity; minimum and maximum number of latent variables for calculating weighted average predictions) or not discussed (pretreatment selection on X residues instead of Y residues, as usually; forcing spiking samples into neighborhoods; why not testing a strategy without AfSIS dataset, to evaluate its usefulness), some terms are not introduced/defined (hold-out and validation sets; MEpred; notion of accurate prediction), and some points are unclear (what were Central African samples out of the six core regions used for? why were AfSIS sentinel sites divided into hold-out and validation sets?). Some results are misinterpreted (using RMSE for comparing predictions between regions with different distributions of TC or TN; differences between strategies), others are not presented in the text (effect of the number of spiking samples) or not discussed (negative effects of Strategy 2 in several cases), and conclusions often seem too optimistic ("accurate predictions" etc. while error represented >=30% of observed mean in most cases).

For these reasons, I recommend moderate revision.

SPECIFIC COMMENTS

The title is short, which may be an advantage, but I wonder if it is informative enough; moreover the genericity of the work is not highlighted (i.e. using a large spectral library for predictions in poorly documented areas).

L8-9. What was done with the six core regions, and what the three levels of extrapolation consisted of, should probably be specified a little bit. Moreover, specifying the size of AfSIS SSL would be useful. And as explained below, "accurate prediction" seems overoptimistic.

L13-14. Improvement was not clear for TC, from RMSE=0.38-0.86% to 0.41-0.89%. Moreover, I wonder if such prediction errors allow considering the approach as particularly useful (i.e. is information ACCURATE ENOUGH?). Note that RMSE is not particularly informative as long as distribution has not been specified (e.g. RMSE=3 is small if mean=30 and SD=10, but high if mean=10 and SD=5), so adding RPIQ would be useful.

L38. Cost is one reason, there are probably others.

L52-53. The notion of "positive predictive transfer" is unclear for me.

L64-67. LOCAL and Locally weighted PLSR should probably be cited, as they also aim at selecting spectral calibration neighbors, and were used earlier in soil spectroscopy.

L64-70. In my opinion, approach complexity should be considered: some approaches are rather simple (e.g. spiking) thus widely usable, while others are complex thus usable only by experts (e.g. the fuzzy rule-based system proposed by Tsakiridis et al. 2019).

L86. "covers a large geographic area" is questionable as the sample population is clustered, and a wide area is not represented (i.e. between Kinshasa, Tshopo and Katanga).

L99. The way samples were dried should be specified, moreover they had probably been 2-mm sieved previously.

Tab.2. I've not understood how samples from Equateur, Bas-Uélé, North Kivu and Kongo-Central were used (they are not mentioned in Strategy 2, L204-205).

L106-107. Does this suggest charcoals were considered organic, or negligible?

L112. SPECIFYING PARTICLE SIZE WOULD BE USEFUL (< 0.2 mm? < 0.1 mm?).

L113, L125. Spectral range and resolution should probably be specified.

L125. Spectra were collected on AfSIS and CSSL samples with different spectrometers, so the question of compatibility should be addressed (e.g. was there standardization?).

L132. A reference dealing specifically with soils would probably be more appropriate.

L140. p is not defined. Actually P is a d x l matrix, not a d x p matrix.

L145-161. The error E depends on the NUMBER OF LATENT VARIABLES (l). HOW WAS THIS PARAMETER DEFINED? Moreover, the EXPECTED BENEFIT OF THIS APPROACH (i.e. computing Xcssl residues) for optimizing spectral pretreatment SHOULD BE PRESENTED, when compared with examining RMSE associated with every pretreatment (i.e. computing Ycssl residues, as commonly done).

L165."spectral matrices which can be properly represented by a PLS model" is unclear. Moreover, the assumption that SIMILAR PRETREATMENTS OPTIMIZED GLOBAL AND LOCAL CALIBRATION SHOULD BE DISCUSSED (e.g. according to literature).

L170. The problem with multiplicative scatter correction is that the transformed spectrum depends on the spectrum population it belongs to, so changes when this population changes.

L195. Why 20 spiking samples per regional set, not 10 or 30?

L197. The way k-means works could (should?) be briefly presented.

L199. The strategies considered are: AfSIS alone; AfSIS +other Gi; AfSIS +other Gi +Ki. Other strategies would have been interesting: only using other Gi, or other Gi + Ki, to EVALUATE THE USEFULNESS OF AfSIS (which would be very interesting); AfSIS +Ki, to evaluate the usefulness of other Gi; Ki only, to evaluate the usefulness of AfSIS and other Gi. But this would require much additional work!

L217-219. HOW WAS w DEFINED? Moreover, WHAT p STANDS FOR IS NOT CLEAR: it has not been defined, but according to L140, was apparently used in place of l (number of latent variables); but I'm not sure this makes sense here. Furthermore, I'm not sure to understand what k=1 means. I also note that d has already been used (number of wavelengths; L139). So CLARIFICATION IS REQUIRED. We might also wonder why evaluate dissimilarity (1-S) and not similarity (S), when the objective is to select calibration samples similar to the target sample (cf. L311). Furthermore, I WONDER IF A SIMILARITY/DISSIMILARITY CUT-OFF VALUE WAS DEFINED, below/above which spectra were not considered neighbors (i.e. no prediction for target samples with too few neighbors); and if yes, how this cut-off value was defined.

L220-225. According to Shenk et al. (1997), the weighted average is calculated over a range of latent variables, i.e. from a MINIMUM TO A MAXIMUM NUMBER OF LATENT VARIABLES CONSIDERED, AND THESE PARAMETERS HAVE TO BE SPECIFIED. Moreover, both s1:j and gj are calculated for the jth latent variable, so writing "s1:j" instead of "sj" is unclerar. Furthermore, Shenk et al. (1997) did not call this approach "Weighted averaged PLS"; but why not...

L230-232. Hold-out and validation sets have not been introduced, so this part is not very clear (e.g. why dividing regional AfSIS sub-libraries into hold-out and validation sets? L256 and Tab.3 these sub-libraries were not separated).

L233. I understand the minimum requested number of neighbors was 150, and the maximum possible number of neighbors was 500. WHAT IF A TARGET SAMPLE HAD LESS THAN 150 NEIGHBORS?

L236. FORCING SPIKING SAMPLES INTO THE NEIGHBORHOOD of every target sample is questionable, and the discussion should address this point.

Fig.3. Beside orange and green circles, many grey circles were also outside AfSIS black circles, and it would be useful to mention where they originated from.

L265-267. CRITERIA FOR "GOOD PREDICTIVE RESULTS" HAVE NOT BEEN SPECIFIED. Actually many results were not so good, especially for TN, especially with Strategy 1 (e.g. RMSE for TC and TN was >=50% of observed mean for 2-3 regions with Strategy 1, and >=30% of the mean for 4-5 regions with Strategy 2). And ACCORDING TO RPIQ, PREDICTIONS FOR SOUTH KIVU AND IBURENGERAZUBA WERE OFTEN AMONG THE BEST ONES, so the reasons for considering they "showed the lowest accuracy levels" should be revised, or at least explained.

L271-272. RMSEpred is useful for comparing strategies for a given region, but CANNOT BE THE FIRST PARAMETER CONSIDERED FOR COMPARING PREDICTION ACCURACY BETWEEN REGIONS WHERE DISTRIBUTIONS OF TC OR TN WERE DIFFERENT. R² describes proportionality, not similarity; so, though understood by a wide audience, should be used with care. Comparison between regions should firstly be based on RPIQ, which showed good results for Kabarole, Iburengerazuba and (for TC) South Kivu and poor results for the other regions, especially Tshopo for TC and Haut-Katanga for TN.

L277-279. The fact that CENTRAL AFRICAN SAMPLES WERE POORLY REPRESENTED BY AfSIS SHOULD ALSO BE MENTIONED AS POSSIBLE REASON.

L282-283. Again, RMSEpred should not be used for comparisons between regions.

L284-286. RMSEpred for TC increased in three regions from Strategy 1 to 2, strongly sometimes, which is counter-intuitive so should be underlined, and POSSIBLE REASONS SHOULD BE PROPOSED (as was done for better TN predictions with Strategy 2 than 1).

L287. Better TN predictions with strategy 2 than 1 "was due", not "might be due".

L290. RPIQ for TC "tended to be the same" except for Kabarole; but actually RPIQ decreased in South Kivu and Tshuapa, not much, but this is counter-intuitive.

L292. South Kivu was not an exception, as TN prediction was also improved.

Fig.5. THESE RESULTS SHOULD BE PRESENTED in the text, and an optimal number of spiking samples could be proposed for each region.

L309, L317, L391. "Accurately predicted/model" "highly accurate predictions" are OVEROPTIMISTIC, e.g. when RPIQ <2 or RMSE > mean/2.

L317-318. The point is that for TC, Strategy 2 reduced RMSEpred in only 3 out of the 6 regions considered; so "improved prediction accuracy" is questionable. And POOREST PREDICTION WITH STRATEGY 2 than 1 FOR 3 REGIONS SHOULD BE DISCUSSED.

L322-325. There is STRONG MISINTERPRETATION, as in these two regions, TC (and TN in Iburengerazuba) was accurately predicted (RPIQ >2.3).

L338. These results have not fully presented in the results section.

L339. Three regions are cited, not two. Moreover, Strategy 3 yielded highest RPIQ whatever the region for both TC and TN; and the improvement was strong sometimes, with 10 spiking samples only (Kabarole and Iburengerazuba).

L343-344. For TN in South Kivu, RPIQ increased from 1.1 to 1.6 from Strategy 1 to Strategy 2, so prediction was noticeably improved.

L345. "RMSE remained relatively high", but TC and TN were much higher than elsewhere! Considering RMSE without considering TC and TN distributions leads to misinterpretation.

L345. "slightly" does not seem appropriate: e.g. for Iburengerazuba RPIQ increased from 2.8 to 3.6 for TC and from 3.2 to 4.5 for TN.

L349. As said above, the effect of spiking was strong sometimes (Iburengerazuba and Karabole).

TECHNICAL CORRECTIONS

L6. 1800 soils or 1800 soil samples?

L7. "wider" is not clear for me in "Congo Basin and wider African Great Lakes region".

L10. % is not a SI unit and may cause confusion for comparisons or changes (e.g. TC increased by 5%), so G KG-1 WOULD BE MUCH PREFERABLE.

L59. sol vs. soil.

L77. Predicting a region is confusing.

L84. The sentence should be checked (e.g. layers vs. layer).

Tab.1. Université catholique de Louvain and IITA/ICRAF are not references. Moreover, for the last reference, 2021a,b would be more appropriate than 2021b,a (this is detail).

L103. Total Al, Fe, Ca etc., or some particular fractions?

L115. In general absorbance = log(1/reflectance), not 1/reflectance.

L118. I note the manufacture place is mentioned here, which should probably be systematic.

L134. Actually PLS has most often been defined as Partial least squares.

L207. The sentence should be checked.

L234, L243. Equation 8? Equations have not been numbered.

Fig.3 is not very readable; projections on PC1-PC2 and PC1-PC3 would probably be more suitable.

Tab.4. What MEpred stands for should be specified.

L275. Tshopo, not Tschopp. Four regions are cited, not three.

L426-427, L432-433, L436, L439, L445, etc. Are two DOIs or two URLs necessary? I note that non-DOI URLs do not always work ("error 404", "page not found", etc.).

L442, L445, L508, L540, L564, L567, L570, L573, L584-585, L615, L617-618. Same (or almost same) DOI mentioned twice.

L448, L469, L473, L485, L512, L599. DOI should be added.

L482. What ISMEJ is should be specified.

L487, L498, L530, L590, L591, L593, L611. The references do not seem complete.

L501. European Commission Edn? Soil Atlas Series?

L530. The publisher should be specified.

L613. This reference does not seem at the right place (Vagen et al. after Vollset et al.).

L615. The end of the reference should be checked.

L622. I.W.G.?

The research aimed to present a mid-infrared soil spectral library (SSL) for central Africa (CSSL) to predict key soil properties, thus allowing (i) for future soil estimates with (ii) a minimal need for expensive and time-consuming soil laboratory analysis. The CSSL contains over 1,800 soils from ten distinct geo-climatic regions (from the Congo Basin and wider African Great Lakes region) for a whole of six hold-out core regions.

The paper is affected by several issues, and therefore I must suggest its rejection.

In the following points, my main concerns:

• General comment: used methods or obtained results do not justify several sentences. In the following points, some example are reported, but many other occurs;

• Abstract: “we present a mid-infrared soil spectral library (SSL) for central Africa (CSSL) that can predict key soil properties”…but after the author state, “We present three levels of geographical extrapolation, deploying Memory-based learning (MBL) to accurately predict carbon (TC) and nitrogen (TN) contents in the selected regions.”. So, you are not presenting a CSSL to predict key soil properties, but “only” some selected soil properties! The authors should be consistent throughout the text.

• Abstract and Discussion: “The Root Mean Square Error of the predictions (RMSEpred) values were between 0.38–0.86 % and 0.04–0.17 % for TC and TN, respectively, when using the AfSIS SSL only to predict the six regions. Prediction accuracy could be improved for four out of six regions when adding central African soils to the AfSIS SSL. This reduction of extrapolation resulted in RMSEpred ranges of 0.41–0.89% for TC and 0.03–0.12% for TN.” Ok, but immediately after I read, “In general, MBL leveraged spectral similarity and thereby predicted the soils in each of the six regions accurately; the effect of avoiding geographical extrapolation and forcing regional samples in the local neighborhood (MBL-spiking) was small)” or, even along the Discussion section (line 309), “We showed that TC and TN in six regions of our CSSL can be accurately predicted”…so, in the same paper, the authors write two opposite things. I agree, according to your results, that the first sentence was more closes to reality than the second one, but this bring to an additional issue, i.e., see point 4;

• Abstract, Discussion, and Conclusions: your results don’t look so “promising” (lines 17, 352) as you state, and some of your results and the following discussion are too much speculative;

• Results and Discussion: authors didn’t explore limits in their proposed method. For instance: issues arising from the use of RMSE to compare predictions among regions with different pedoenvironmental features and, consequently, total C and total N.

• Soil sampling method and approach: soils were sampled according to a prefixed depth technique (Table 1) without considering soil variability in terms of main genetic horizons. So, this means that there is huge variability in processes and, consequently, pedogenetic features. But this problem is not considered as a possible cause of errors in obtained results. This is totally a mistake for this reviewer. Indeed, looking at Table 2, it was clear that a quite high pedovariability exists in investigated soil samples (samples comes from five different RG);

• Whole paper: a group of references should always be avoided. It could be preferred to use a max of 2 refs. after every important statement. Otherwise, it could be quite impossible to verify if reported references was cited in a good way;

• Whole paper: several acronyms appear without any explanation!.

• Whole paper: several typing mistakes occur. Some are reported here (vide infra), but many others occur. Additionally, the correctness of some sentences is questionable;

• Title: too generic and not fully in agreement with obtained results (vide infra). Indeed, I am not sure that you have filled a gap; at least in an accurate way;

• Abstract (line 11): AfSIS!?!

• Introduction (from l. 28-30): “Despite the expected severity of these impacts, our understanding of the effects in the humid tropics are limited by sparse data and uneven distribution of low-latitude research”. Too vague and generic sentences. For instance, such a sentence is not true for many areas of Brazil;

• Introduction (l. 30-31): “which contains the second largest tropical forest ecosystem on Earth and represents a considerable reservoir of soil C (FAO and ITTO, 2011)”. Old reference. Ten years are already gone by. In case of such important statement more recent, an updated information must be reported;

• Introduction (l. 33): “Thus, the projected drastic population growth in the coming decades (Vollset et al., 2020)” a quantification in terms of percentage, or something like this, is always required; otherwise, it is just a vague statement;

• Introduction (l. 35-36): “In the wake of these current and future impacts, more spatially explicit soil information is urgently needed in many research fields.” Again, too vague and generic sentence. Which field of research?;

•  Introduction (l. 44): “low cost” always depends on the point of view. What does for the authors “low cost” means? Why not introducing a specific brief paragraph for cost estimation by comparing soil analysis vs. DRIFT spectroscopy;

• Introduction (l. 50-55): too speculative sentences. It seems more an authors’ self-convincement rather than a scientifically based questions;

• Introduction (l. 52-53): sorry, I really don’t know what "positive predictive transfer" means;

• Method (l. 91): WRB, 2006? Really? Are you aware of the 2015 updated version?

• Method (general comment): What about the way you selected “latent variables” for the global calibration you did for optimizing spectral pretreatment?;

• Method: “Note, even if the proportion of samples with inorganic carbon was very low (5%), the term TC will be used in the study.” As usual! Why do you need to specify such an obvious aspect?;

• Method: I think that the way you pretreated your soil samples should be specified;

• Method: “A gold standard was used as a background material for all measured soils” which kind of “standard”? It was a reference soil certified material? Why not including such important information?;

• Method (Table 2): For this reviewer, it was not so clear if you used all the reported nr. of soil samples. It would help if you were more clear from this point of view;

• Method: “Reflectance was transformed into absorbance (1/reflectance) before further processing and subsequent modeling.” No reference!;

• Method: “Four replicates per sample were measured and an average of 32-co-added scans were used for each sample” why? Four replicates are enough for you? If yes, you need to explain the reasons from a statistical representative viewpoint;

• Results (general comment): very aseptic. It looks like a technical report totally detached from the context;

• Results (paragraph 3.1 and Fig. 3): I discover for the first time that the authors applied a multivariate approach too. In particular, they used a PCA. Unfortunately, they didn’t explain to us anything about how it was implemented. This is really unusual for this reviewer. Indeed, when a multivariate tool is used, data-pretreatment represent a pivotal matter, but the authors didn’t explain anything about this. Additionally, several authors, statisticians included, clearly demonstrated that PFA was better for variability interpretation in a soil dataset with soil data;

• Line 268: soils rather than “sols”;

• Results (lines 267-268): “This was expected as the principal component analysis indicates that the sols of these regions might not be properly represented by the AfSIS library.” Where? I don’t see such an information from PCA;

• Results (lines 276-279): I do not fully agree with the suggested reasons for the total C and N predictions underestimation trend in the six investigated regions. Indeed, several outliers occur in your dataset. This was typically due to an underestimation in investigated pedovariability (vide supra);

• “Results” and “Discussion” (general comment): both these parts are full of “could”, “may”, “might”, etc. I understand that caution is always required in a scientific text, but some more certainties should be given. So, I wonder: are the authors sure enough of the applied method and the validity of the obtained results or not? As a reviewer, the text has several methodological drawbacks, which bring me to hypothesize that all these doubts could be the demonstration of a low statistical robustness of obtained results;

• Discussion (line 309): “We showed that TC and TN in six regions of our CSSL can be accurately predicted”. Honestly, I am not agreed. In previous pages and Tables, total C and N prediction can be rarely defined as “accurate”;

• Discussion (line 309): “The advantage of using MBL is that it finds spectrally similar observations for every new observation to fit specific models”. This is an obvious observation that can be written for every prediction “model”;

• Discussion (line 312): “)”…?;

• Discussion (general comment): extremely redundant with the “Results” section. A combination of the “Results and Discussion” section it would have improved the paper in terms of overall quality, clarity, and readability;

• Discussion (general comment): readability is made really low due to the presence of too many acronyms. I understand that several acronyms characterize the whole paper, but some strategies would have improved readability (for instance, avoiding its use while preferring a “recall” of their original meaning);

• Discussion (line 319-323): another obvious observation that strongly affect your paper in terms of novelty;

• Discussion (line 324-326): “We conclude that the particularly high soil diversity in these two regions in terms of soil biogeochemical properties introduces additional complexity in the soil spectral prediction workflow” this is the point! Even if, in my opinion, it would be better to use “soil bio-physical-chemical features” rather than “soil biogeochemical properties”. However, this clearly confirm all my previous doubts, and I am astonished that the authors recognized such a big issue only at the end of their paper without additional insights about this;

• Discussion (line 324-326): “Regions that occupied the same score space of the first two principal components as the corresponding other regions and the AfSIS SSL (Figure 3) showed only a minimal effect from spiking (Figure 1)” where I can see such an outcome? It is not contained in Fig. 3 and 1 for sure;

• Discussion (l. 348-250): “Even though spiking is described as particularly effective in improving performance of small sized models (Guerrero et al., 2010), spiking, in our study, did not have as strong of an effect as reported by earlier studies (e.g., Guerrero et al., 2014; Seidel et al., 2019; Barthès et al., 2020; Wetterlind and Stenberg, 2010)…and the reason is!?!;

• Discussion (l. 353-354): “The addition of geographically proximal regions to the large-scale library, which are included in our CSSL, improved prediction accuracy significantly”. Sorry but once again, I disagree with the authors. From your reported results, it seems that accuracy improved but not in a so highly significant degree;

• References: Total nr. of references: 77…too much for an original article; Total nr. of references before 2011 > 20; Self-citations > 10