General Comments

The authors present high resolution δ¹⁸O and δ¹³C measurements of bivalve shells collected from the Oubangui River basin in the Central African Republic to reconstruct hydroclimate since the late 1800s. Isotopic data from archival and recent shells are contextualized by instrumental measurements of river discharge and precipitation. This work appears to be a follow-up on an earlier study by these authors and others (Kelemen et al., 2017) where they separately assessed the equilibrium δ¹⁸O_carb-temperature-δ¹⁸O_water relationship in this species and quantified a relationship between δ¹⁸O_water and river discharge at this specific sample site. They observe an imperfect fit between the discharge estimated from shell δ¹⁸O_carb using the aforementioned empirical relationship and the instrumentally measured discharge. They look to other observational records and conclude that the increased variability in δ¹⁸O since 2003 is probably related to changes in dry season precipitation and groundwater flow.

Overall the dataset presented here is impressive, the work is technically sound in terms of methodology and interpretation, and the quality of writing is good. It furthermore addresses pertinent questions about central African hydroclimate. My comments should be considered minor and mostly aim to clarify certain points or draw out select points of discussion. The abundance of data considered here leads to very nuanced discussion of site-specific circumstances, which is all sound, but the paper doesn’t circle back to the stated goal of evaluating the performance of bivalve δ¹⁸O_carb as a more widely applicable proxy for discharge. I would like to see more discussion of this angle and more explicit consideration of limitations in other contexts.

Specific comments

Line 137-144: A clearer way to introduce these equations would be to first state that Equation 1 is used for calculating the aragonite-water fractionation factor based on Dettman et al. (1999). Subsequently, δ¹⁸O_water was calculated using Equation 2, the alpha value from Equation 1, and the embedded VPDB to VSMOW conversion. As an additional note: why not use a more recent calibration such as Kim et al. (2007) or Grossman (2012)? What is the effect of using these different equations on reconstructed δ¹⁸O_water from the bivalves?

Line 210-213: Can the authors provide quantification or statistical tests for constancy in δ¹⁸O minima to then contrast with the reported baseline shift post-1970?

Line 226-227: “low discharge is overestimated” is a confusing turn of phrase here, particularly given the discussion of different effects on high vs low flow. Do the authors intend that overall discharge is simply underestimated (which seems to be what is represented in Fig. 6) or is there a component of low flow being referenced?

Line 226-231: It does not seem accurate to say that the shells “consistently” underestimated Q for historical specimens. I count six years where the reconstructed Q matches peak measured Q impressively well, and the quality of the match doesn’t seem to strictly depend on age of the record or size of the peak. What do the authors make of the variable accuracy of reconstructed Q, both before and after the hydrologic shift in low-flow water sources post-1970? They seem to suggest growth cessation during high discharge could account for this based on previous results (Kelemen et al., 2017), But how would this account for excellent accuracy during some of the highest peaks in the historical record? This is an important element of the discussion as the authors are setting this up as an evaluation of the proxy for future applications where less/no historical data is available.

Line 255: The authors state that a 5% overall reduction in rainfall post-1970 was only 5% cannot account for the 22% decrease in Q; they should quantitatively evaluate the significance of the change in dry season precipitation if they believe this to be a stronger causal mechanism.

Line 317-318: This sentence is confusing—do the authors mean to refer to historical specimens twice?

Conclusions: The paper is pitched as a broad evaluation of bivalve shell δ¹⁸O as an archive of various hydroclimate parameters, especially seasonal discharge but also precipitation dynamics, land cover, groundwater flow, and geography. Given the limitations and enmeshed signals that they explore throughout the discussion, the authors should end with an overarching conclusion about how this proxy will best be used and interpreted in other systems. Some guiding questions: Their assessment of possible changes in precipitation dynamics, land cover, groundwater flow etc. based on δ¹⁸O_water follow on from identification of a δ¹⁸O_water-Q mismatch. Could these factors be evaluated without an established δ¹⁸O_water-Q relationship (which would apply to any other river system and to historical systems without direct monitoring)? Could they be evaluated in a context where Q is indeed a direct control on δ¹⁸O_water? How would one identify when an empirical δ¹⁸O_water-Q relationship does break down in the past, as argued here for the Oubangui, without direct Q data for comparison? How far into the past could a δ¹⁸O-Q relationship measured recently be extended into the past even for the same river basin?

Figure 1: An inset map showing the basin’s footprint in the CAR with a lat/long grid would be appropriate to ground the reader in absolute space. Some of the text in the lower left is difficult to read against the dark background. Symbols could be slightly bigger.

Figure 2: A mixture of color and symbol could be used to differentiate overlapping records. Are the overlapping records matched absolutely in time based on collection date/band counting, matched based on features of the profile, or somewhat arbitrarily overlaid?

Figure 3: Same comment as Fig. 2.

Figure 6: Same comment as Fig. 2.

Technical corrections

Throughout: be consistent with use of Q as an abbreviation for discharge.

Throughout: The authors use the term “historical” as a contrast to “recent” shells throughout, but “historical” is used to group different subsets of shells in different parts of the discussion (e.g. pre-1960, pre-1970). It would be clearer to simply refer to groups of shells by their specific time periods since the collection dates are well-constrained.

Line 77: “Predicted” would be more apt than “hypothesized” here.

Line 84: superscript m³s^-1

Line 135: subscript on CaCO₃

Line 177: Cite Figure 3.

Line 189: Cite Figure 5.

Line 195: superscript on δ¹⁸O

Line 233: spacing on δ¹⁸O_water-Q.

Line 249: only in 1970 or beginning in 1970?

Line 159: superscript on δ¹⁸O

Line 267: better to say “All these factors could lead…"

Line 279: superscript on m³s^-1

Line 279: “Qmax/Qmin of about…”

Line 280: superscript on δ¹⁸O_water

Line 340: subscript on δ¹³C_DIC

This manuscript is well written, interesting, and has an easy to follow story. I think it absolutely deserves publication; well done authors! I have two suggestions that I think can improve the manuscript: I would suggest adding one or two sentences to the abstract or introduction explaining that higher oxygen isotope values are indicative of lower flow conditions. This relationship is key to understanding the premise and results of the paper, so I would recommend stating it explicitly, earlier in the paper. My second suggestion is to add more rationale in the method section as to why carbon isotopes were measured. Oxygen isotopes were clearly the focus, and it makes sense to also run carbon at the same time since the shell samples are already at the mass spec. But, I think more rational in the methods is needed for why carbon was included in the manuscript itself. I look forward to seeing this paper published.