Dear Mr Renoult,

I am now in receipt of 4 reviews on your paper: 2 commissioned reviews and 2 short comments. As is often the case, the assessments are quite split: reviewer 1 describes your methodology as "transparent", whereas reviewer 2 describes it as "remarkably opaque". This lack of clarity is echoed in Short Comment #2 by Philip Sansom and Daniel Williamson, and I am glad that your responses suggest that you are taking this criticism to heart.

In light of these responses, and of the fact that the recommended changes will not lead to fundamental reassessments of the results, I happy to recommend your article for publication after minor but mandatory revisions. In particular, I recommend that you expound on the mathematical model in much greater detail, along the lines of what Reviewer #1 recommends. I also agree with this reviewer that the use of a complex Hamiltonian Monte Carlo method like NUTS seems like a hammer to swat a fly. Though I understand your rationale for using it as a base from which to build a more complex model, I recommend that you implement Reviewer 1's recommendation of using an Inverse Gamma prior so you can obtain a closed-form posterior, and check that the algorithm matches this known solution ; this can be done in an appendix.

Beyond that, articulating the difference between your approach and pre-existing ones seems important, and three of the comments have made you aware of the necessity to clarify the limitations of a Kalman filter in this context.

We look forward to your revised submission.

Best regards,
Julien Emile-Geay

Dear Mr Renoult,

I wish to thank you and your co-authors for comprehensively addressing the reviewers’ concerns in your revisions. From my vantage point, this seems a case of productive peer-review, with the process resulting in an improved presentation and correction of errors in the code and tables.

RC1 had only made minor suggestions, which I feel you adequately addressed.
RC2 made more substantial comments regarding the mathematical formalism, which is more explicit now. However, the discussion comparing your approach to OLS seems to dance around the issue of forward vs inverse regression, a storied theme in the regression literature, treated for instance by Brown (1994). It would seem especially important for the paper to be clear on this topic ; unfortunately, I find the current discussion still confusing. This is echoed by some of SC2’s points, which you concede with “We might have taken a non-elegant shortcut”, yet the paper could still use some sharpening. On other accounts, I agree with your stance that the goal of your paper is to present and substantiate a novel formalism, not to adjudicate or review all possible approaches to the emergent constraint idea.

RC2 also asked you to compare the results of NUTS with those using a conjugate prior. I could be mistaken here, but it seems like the idea was to use the same prior in NUTS and the analytical approach, to make sure you get the same result within numerical precision. While the credible intervals you cite are similar, they are by no means identical, which I would view as concerning from the standpoint of numerical validation. You write “The differences between both methods is minimal with respect to the range of the posterior parameters and can be attributed to natural variability and differences between the Half Cauchy and Inverse Gamma prior. “. It would seem as though the second difference can easily be erased by choosing the same prior in both experiments. As for the first, “natural variability” is a climate neologism that no other field of the mathematical sciences uses, and which is particularly opaque to outsiders. If I understand correctly, you are referring to “stochasticity”, though in the limit of large samples, the differences should all but vanish. I am therefore perplexed that there are any differences to speak of, and I would want to see this better explained (if not eliminated) in a revised version.

Overall, I find merit in your philosophy of building a flexible inference system, which can be made more complex as needed. One obvious generalization is the incorporation of observational errors on tropical paleotemperature Indeed, apart from borehole paleothermometry, temperature is never obtained directly from “geologic proxy data”; it is always inferred from a model thereof, sometimes quite a complex Bayesian model (eg Tierney & Tingley, 2014, 2018). So while I am sympathetic to the notion that the resulting uncertainties may be overwhelmed by model spread in your study, this heuristic seems to depend heavily on trusting the assessments of uncertainties given by existing reconstructions, which could be overly narrow for the exact same reason that the OLS estimate if S is (artificially shallow slope in the limit of uninformative/noisy data). It would therefore seem worth mentioning somewhere in the discussion that a proper error propagation analysis of paleotemperature would be an important extension of the framework. Indeed, it would also be a feasible one if the computational framework is as flexible as you say.


Re: your response to these comments, I find the formulation “a certain uncertainty” most unfortunate. I suggest “a given uncertainty” as a clearer substitute.

I hope these minor comments help you further refine the manuscript, so it can be better digested by the community in the rather crowded field of “emergent constraints research”.

Best regards,
Julien Emile-Geay


References:

Brown, P. J. (1994), Measurement, Regression, and Calibration, Oxford Statistical Science Series, vol. 12, s ed., 216 pp., Oxford University Press, USA.

Tierney, J. E., and M. P. Tingley (2014), A Bayesian, spatially-varying calibration model for the TEX86 proxy, Geochimica et Cosmochimica Acta, 127, 83–106, doi: 10.1016/j.gca.2013.11.026.

Tierney, J. E., and M. P. Tingley (2018), Bayspline: A new calibration for the alkenone paleothermometer, Paleoceanography and Paleoclimatology, 0(0), doi:10.1002/2017PA003201.

Dear Dr Renoult,

thank you for your corrections, which bring the manuscript within inches of publication. The appendix is now much clearer, and convincingly demonstrates that your MCMC approach does land on the same distribution as the analytical (conjugate prior) solution, which is always reassuring.

Regarding the other revision, I regret to say that the new paragraph (L137-147) falls short of fully clarifying the matter. The question at hand is one of modeling assumptions more than inference method. As such, I think the focus should be not so much on OLS vs Bayes, as much as it is on forward vs inverse regression. The frequentist (maximum likelihood) or Bayesian part comes into play only when one wish to estimate model parameters and/or make predictions under that model. Tingley et al, (2012, doi:10.1016/j.quascirev.2012.01.012) make this point quite nicely in a slightly different context, when they write: "assuming a linear relationship between two variables is a modeling assumption, while the decision to use least squares, method of moments, Bayesian inference, or some other tool to perform the statistical inference is an analysis choice." This is a good guide for clarifying this discussion, and I suggest you reframe it in those terms.

After such clarification, I will be happy to recommend your article for publication.

Best regards,
Julien Emile-Geay