Hennekam et al. provide a new calibration of XRF-CS derived Ti/Al measurements from Mediterranean core ODP 967 – a key site for the study of Plio-Pleistocene Saharan climatic variability. This is an important record which provides additional evidences for the timing and intensity of wetter/drier periods in the Sahara and the potential global/orbital controls of these fluctuations.  The article is well written, with little grammatical revision required to the main body of the text. I believe this article asks two key questions: 1) how best can non-destructive and destructive geochemical methods be combined to provide an accurate record of past climatic variability? And 2) what can this new record inform about the long-term orbital influences on Saharan climatic variability throughout the Early Pleistocene to Mid Pleistocene?

The major strength of this manuscript is that it offers a valuable method to mitigate loss of material though WD-XRF analysis by instead selecting fewer (1060) samples to calibrate a non-destructive XRF-CS record (8497 samples). This permits a higher resolution Ti/Al record to be produced. However, I have a few concerns with this section.

• I believe the authors would benefit from emphasising the novelty of their study more clearly. Currently, on the basis of the text, it does not seem entirely clear how this calibration and XRF-CS record differs from that of Grant et al. (2022). Did the authors obtain new Ti/Al measurements? Or did they use those of Grant et al. (2022)? Similarly, did Grant et al. (2022) use the same WD-XRF dataset (Konijnendijk et al. 2014, 2015) to calibrate their record? Is this study using the same data and method as Grant et al. (2022), and simply testing how many samples are needed for accurate calibration? The authors must make the last two paragraphs of the introduction (and the materials and methods section) much clearer so that readers can establish the data output of this study.
• The results table (Table 1). Instead of a Y or N value to indicate whether the null-hypotheses have been rejected, the authors should provide the P-value and test specific values. This could be included in supplementary material rather than the main text, but they must be accessible for researchers. Additionally, the authors need to account for the “multiple comparison problem” by adjusting the 𝑎 value
• It is necessary for the authors to better explain why 53 samples are required for accurate calibration, and why, if this is sufficient, the 1060 sample calibration record is favoured for the subsequent discussion. I understand that it is necessary to reduce the number of samples to achieve the authors aims. However, I believe the justification for this amount is unclear as the test specific results have not been made available.

For the high-resolution XRF-CS Ti/Al analysis and correlation to orbital records, I would like to first say that I am generally supportive of this analysis. The authors provide a detailed insight into the varying controls of orbital parameters on African wetter/drier periods. Unlike hematite dust transport, Ti/Al ratios provide a method to study the intensity of wetter/drier periods. Their statistical analysis and interpretation, that high-latitude forcing played an increasingly dominant role after the Mid Pleistocene Transition, appears reasonable and well argued. However, I believe this section needs further work and clarification/justification.

Firstly, the application of a 401 kyr window running correlation (long eccentricity band), based on the text, does not seem justified to the reader. Why was this running correlation window selected? The authors must explain why such a large window is necessary and crucial to their analysis and interpretations.

Secondly, as can be seen from the very well-made figures, the 95% confidence intervals (while they do represent extremes) are large and, considering this, there is some uncertainty when distinguishing the shift from low to high running correlation between >1.2 and <1.2 Ma. This is more of an issue for the correlation with sea-levels. Additionally, the claim for constant high correlation with sea-level after the MPT is not so clear; it appears that higher correlations exist from about 1.7 Ma, with an abrupt dip at 1.1 Ma, after which the high correlation returns. Perhaps the authors could perform a t-test of running correlation values between these two periods to test for significant differences? Furthermore, both the correlation with insolation (is this SITIG, 65N, 35N or 15N? Please clarify on figures) and sea-levels timing may benefit from further investigation using ChangePoint analyses. If using the R statistical software package, this can be achieved with packages such as BCP or ChangePoint. This may result in slightly different ages identified for these changes, but combined with the current analysis, would add an additional line of support to the authors argument. In either case, I believe that, while there is a deal of statistical uncertainty, the authors analysis provides important information for understanding the orbital controls on Saharan wetter/drier periods throughout the Pleistocene.  

While I am supportive of their analysis, the authors may benefit from additional reference to various studies which describe the suppressive effects of glacial termination melt-water discharge on low-latitude forcing during the Middle and Late Pleistocene, causing monsoon intensification to lag insolation (e.g., Marino et al., 2015; Menviel et al., 2021; Häuselmann et al., 2015; Böhme et al., 2015). While most of these studies are limited to the LIG or Holocene, this may provide an additional line of support for some of the authors arguments.

I recommend that this paper be published in Climate of the Past subject to the authors addressing the concerns and the few grammatical/technical notes below. I suggest minor revisions as 1) results of the statistical testing and consideration of the “multiple comparison problem” (this may have some impact on the results, but is difficult to estimate without seeing the test specific results); and 2) the interpretation/discussion needs further analysis and justification to support these arguments, and currently the novelty is not well emphasised. However, I believe that this work will make a valuable contribution once these concerns are addressed.

Technical/grammatical notes:

Line 37-39: References. The authors may benefit from adding a few references to palaeoanthropological/archaeological outputs and discussions, that are not necessarily climatic research initiatives, to highlight the broader relevance of their work. (E.g., Potts et al. 2020; Groucutt et al. 2015)

Line 58-86: The last two paragraphs of the introduction. I believe these paragraphs are, in short, saying "As WD-XRF is destructive, how many samples are required to accurately calibrate a non-destructive XRF-CS record?". The authors may benefit from revising these paragraphs to emphasise the aims of the manuscript more concisely (or perhaps directly). Maybe this is due to my unfamiliarity with the methods, but it took me a few attempts to work-out the novelty of this article, as Grant et al. (2022) is described as having conducted a very similar WD-XRF calibration of an XRF-CS record for the 5 Ma period of the core. The paragraphs must emphasise the novelty of this study more clearly.

Line 172: There have been various comments that WD-XRF analysis is more precise/better established than other methods. Can the authors provide further quantification of this?

Line 223-224. The authors may wish to add a comment on the work of Tzedakis et al. (2017).  Nature, 542: 427-432.

Table 1. Please include the results of the statistical tests either here or in supplementary material.

Fig. 2 and caption. “XRF-bead”. Perhaps change this to WD-XRF-bead for clarity?

Fig. 3 may benefit from the addition of correlation coefficients of the XRF-CS Ti/Al record and the respective humidity/aridity records from ODP 967.

Fig. 4g. Please clarify if insolation is the SITIG, 65N, 35N or 15N.

Fig. 5c. The figure may benefit from a dashed line running horizontally from 0. This would allow the reader to track changes more easily in the correlation.

Figures. (not necessary). The cyan text may benefit from being a few shades darker.

Review of the manuscript entitled « Accurately calibrated XRF-CS record of Ti/Al reveals Early Pleistocene aridity/humidity variability over North Africa and its close relationship to low-latitude insolation” by Hennekam et al.

General comments

The study by Hennekam et al. has two major objectives: (1) investigate how to reliably calibrate core-scanner elemental records using the example of core ODP 967 from the eastern Mediterranean Sea, and (2) discuss changes in North African humidity and aridity over the last 3 Ma (with a special focus on the Mid-Pleistocene Transition (MPT), ~1.2-0.7 Ma), and their drivers (orbital parameters, insolation, ice volume). First, the authors test various numbers of WD-XRF calibration samples and two ways of selecting calibration samples, and discuss how much the calibrated core-scanner Ti/Al record compares statistically to the reference Ti/Al record. Then, the authors discuss calibrated Ti/Al changes in terms of North African aridity changes over the last 3 Ma, in agreement with available high-resolution records. Aridity over North Africa was particularly enhanced after the MPT. They confirm the strong control of orbital parameters (precession, obliquity, eccentricity) on North African humidity. Whereas low-latitude forcing dominates between 3 and 1.2 Ma, North African climate became more sensitive to high-latitude climate forcing when global ice volume increased during the MPT.

The manuscript is concise, well written, easy to read. Figures are clear and well explained. The methodology is sound and generally clear. However, I have two major concerns about the manuscript. First, I find the two parts appear to be rather disconnected one from another. It almost gives the impression two small studies have been merged together to build a manuscript.

Second, I find it difficult to identify the new information this study brings in comparison to previous studies. It is stated (lines 292-293) :“our detailed analysis of the 2.3-1.2 Myr interval and extensive testing of the calibration approach is novel.” (NB: Is the Data availability section the right place to make such a statement?) However, even if I find the calibration testing exercise interesting (though frustrating by lack of more detailed discussion), I wonder to which extent it is needed for the interpretation of the Ti/Al record (see specific comment 1 below). Also, even if I am not an expert of North African climate over these time scales, the manuscript gives the impression it confirms previous hypotheses on the control of North African humidity (rather than brings novel ideas). I also have the feeling the study brings more insight on North African changes during the MPT than between 2.3 and 1.2 Ma (as indicated in lines 85-86, and 293).

In conclusion, I think this manuscript deserves publication in Climate of the Past, provided the authors are able to better highlight the added value of this study (compared to already published works), to better link the two parts of the manuscript (calibration exercise and interpretation of Ti/Al in terms of North African humidity) and to better highlight the usefulness of the calibration exercise for the study and the community, by further developing its discussion.

Specific comments

1. Calibration testing exercise

I wonder to which extend the detailed exercise of comparing calibrations is really needed for the study, for 3 main reasons, which would all require additional discussion in the text.

(a) Why is the XRF calibration published by Grant et al. 2022 not included in the testing exercise? The study by Grant et al. 2022 is cited in lines 72-74. It uses 42 WD-XRF reference samples (cited as more accurate than ED-XRF samples). So why not include this calibration in the comparison?

I had also been wondering how much the calibrated Ti/Al record published in Grant et al. 2022 differs from the Ti/Al record adopted in this study until I reached the Data availability section, where we can read (lines 290-291): “The calibrated XRF-scanning record of Grant et al. (2022) is essentially the same as the final calibrated XRF-scanning record presented here […]. We recommend to use that record for paleoenvironmental purposes.” (NB: Is again the Data Availability section the right place for such a statement?) Above all, is a new calibrated Ti/Al ratio necessary here if it is the same as the one published by Grant et al. 2022?

If the calibration exercise remains in the revised manuscript, I would advice to include the calibration by Grant et al. 2022 in the comparison, extend the discussion on how much calibrated Ti/Al records differ and clarify the ambiguous statement on the record recommended for paleoenvironmental purposes (the one by Grant et al. 2022 or the newly calibrated one with 1060 reference samples?), and for which reasons one record is preferred if they are essentially the same.

(b) The comparison between the different tests of calibration is based on five statistical tests comparing the calibrated core-scanner Ti/Al and the reference WD-XRF dataset (Table 1). I remain highly frustrated by the currently limited discussion (lines 141-147) on how many reference samples are recommended or suitable for the calibration, and which type of selection of reference samples should be preferred (even spacing or Xelerate automatic selection). I find it very difficult with this limited discussion to draw inferences for other calibration studies. In light of the exercise, what is the minimum recommended number of reference samples? (What about the recommendation by Weltje et al. 2015 (equation 21.15a) of having as number of calibration samples at least 3 times the number of elements to be calibrated?) How should reference samples rather be selected: evenly spaced, manually or automatically with Xelerate? Indeed, I am quite surprised to see that even spaced samples seem to give a more robust calibration than automatically selected samples and would have liked to read a more extended discussion in lines 146-147. In summary, I would strongly advice to develop the discussion on the comparison of calibrations to make it more meaningful and useful to the community beyond the case study of core ODP 967.

Similarly, I would advice to add a direct comparison of the differently calibrated Ti/Al records and discuss their possible differences in the text. Indeed, at first sight from Figure 2, there do not seem to be major differences between the various Ti/Al records. Thus, the reader wonders why a detailed calibration exercise is included in the manuscript if all tested calibrations provide relatively similar calibrated log-ratios.

(c) So far, I thought that calibration of core scanner intensities was a requirement in provenance studies (where absolute values of elemental ratios are compared to the composition of source material) and a bonus in classical paleoenvironmental studies, as it is the case here. In my own experience, the calibration modifies the absolute values and amplitude of change of elemental ratios, but not so much their downcore variations. It does not seem to be the case here (Figure 2, mostly below 30 m) and I am curious to know why. Thus, I would also recommend to develop the discussion on how much the calibration modifies the uncalibrated Ti/Al record. I think it would make more convincing and better illustrate the statement of the necessity of the calibration for paleoenvironmental purposes (lines 158-159, 292). It would also reinforce the usefulness of having the exercise comparing the various calibrations within the manuscript and strengthen the link between the two “parts” of the manuscript.

Finally, I think the information provided on the calibration would deserve clarification at two places. First, I would state more clearly in lines 122-124 that 10 elements are calibrated, give the name of calibrated elements and provide (as a supplement?) an illustration of the retained calibration for all elements (e.g. the Xelerate figure with reference vs. predicted concentrations). Second, I wonder how the authors managed to run the Xelerate software with 22 reference samples only for 10 calibrated elements, when I think the software requires as number of reference samples at least 3 times the number of elements (equation 21.15a in Weltje et al. 2015).

2. Changes in North African humidity

(a) As a non-expert on these long time scales, I would have liked to have more information on the chronologies and related age uncertainties. In particular:

What is an estimate of age uncertainties in core ODP 967 (lines 95-99)?

How were constructed the age models of sites ODP 659 and 721-722 (lines 192-194)? What is the related age uncertainty? What is an estimate of the age offset that is expected between the records of these sites and core ODP 967 for the period of interest?

How was estimated the small lead of 2 ka of obliquity over Ti/Al (line 230) and how does it compare to age uncertainties for the period?

(b) I would also have liked to read more detailed information (lines 235-239) on the climate model results (Bosmans et al. 2015a, b). Which type of simulations was run? Climate sensitivity experiments? What was exactly tested? Which results are observed?

(c) I am not fully convinced by the values of the coefficients of correlation between Ti/Al and the Gibraltar relative sea level record (Figure 5c). Can we speak of a high correlation when the absolute value of the coefficient reach 0.3-0.4?

Also in Figure 5 I think the method how “Sapropel intervals are removed in this data set and data accordingly interpolated” (line 475) should be explained.

Technical comments

Line 27: I would write “the longest period and highest amplitude”

Line 45-46: I would write “throughout the Pleistocene”

Line 59: I would write “during 0-1.2 Ma and 2.3-3.2 Ma”

Line 112: Please correct the reference “Zhan, 2005”.

Line 131: Please indicate which version of Analyseries has been used.

Line 146-147: I would rather write “(i.e. all calibrated elements)”.

Line 459: Is the Ba/Al ratio shown in Figure 3f also calibrated? Please specify.