the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 15 Dec 2025
Timing of the anthropogenic carbon invasion in the Southern California Current
Abstract. The role of Eastern Boundary Upwelling Systems (EBUS), such as the southern California Current System, is a well-known high productivity region driven by alongshore winds, although their role as atmospheric carbon sources and sinks is poorly understood in the global carbon cycle. In the southern CCS, off Baja California, wind-driven vertical mixing upwells nutrient and carbon-rich waters from late winter to early summer, while weaker winds during the rest of the year allow the intrusion of nutrients and carbon-depleted subtropical surface waters. Here, we interpret the isotopic composition of organic carbon and calcitic records spanning 150 years from high-resolution sediment cores collected off Baja California in the context of seasonal variability observed between 1990 and 2011. The results show a clear trend toward lighter carbon isotopic compositions of the organic and inorganic carbon for the past seven decades. These trends are similar to the atmospheric records associated with the Suess effect, suggesting an atmospheric carbon invasion into the surface waters of the California Current. Nevertheless, the slope of the atmospheric carbon isotopic records is steeper than our marine record, most likely related to the upward mixing of subsurface waters with a relatively heavier carbon isotopic signature and advection processes inherent to the strong seasonality of the CCS southern boundary. These results will allow a better characterization of the relative role of the EBUS regions in the global carbon cycle.
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Status: final response (author comments only)
- RC1: 'Comment on egusphere-2025-5945', Anonymous Referee #1, 05 Mar 2026
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RC2: 'Review', Anonymous Referee #2, 09 Apr 2026
This paper describes d13C data since 1850 from sediment cores in the California Current System. The data show that the Suess Effect is a major component of the time series, but also that this fossil fuel induced trend is smaller than in the atmosphere and therefore upwelling processes which bring waters heavier in d13C of DIC might also play a role here.
I cannot say anything on the methods, so I focus on presentation and interpretation.
That said I find this study worth publishing, but the figures and the result sections needs in my view some revision to sharpen them and to bring them up to standards. Thus, all comments below (in chronological order) are a lot a small issues which should be considered during revision:- line 13-14: CCS is an oceanic sink or source to atmospheric CO2, not an „atmospheric carbon source or sink“
- If I got it right, you have new data from ~1850 to 2011, so about 160 years. Please correct throughout (eg abstract says 150 years).
- Seasonal context (first mentioned in l 19, section 3.1 incl Fig 2): The importance of this seasonal context is not clear to me. First, if you keep it in, you need to clearly state, that this is not your data, but from SOCAT. This appear in the in caption to Fig 2, but not at all in the text. Second, Fig 2A mixes anthropogenic rise with seasonality. You would need to detrend them first and one might calculate a mean seasonal cycle to be of use here. However, your data have no seasonal resolution at all and you also discuss d13C of atm CO2 not on a seasonal timescale (those data would be available, eg. https://scrippsco2.ucsd.edu/graphics_gallery/isotopic_data/mauna_loa_and_south_pole_isotopic_c13_ratio.html). I think you use this seasonality to argue which time of the year your area might be a sink or a source for CO2. That is, however for d13C rather not important. Air-sea gas exchanges happens in both directions throughout the year even if the fugacitiy of CO2 in the surface ocean and the atmosphere are always in balance. The CO2 imbalance (source or sink) is not so important for d13C. I suggest to completely drop this section.
- l 21: Please change „Suess effect“ into „13C Suess effect“ throughout the draft. There is also a 14C Suess effect.
- l 34: The reference to Sabine et al., 2004 on the oceanic uptake of anthropogenic emissions is a bit outdated. Maybe use a recent paper from the Global Carbon Project (Friedlingstein et al.,: Global Carbon Budget 2024, Earth Syst. Sci. Data, 17, 965–1039, https://doi.org/10.5194/essd-17-965-2025, 2025) and check their Table 8 for recent numbers on relative oceanic uptake.
- l 42: delete „natural“. Citiation for d13CO2 (Baldwin et al. 2005), again is a bit outdated. Since your data go until 2011 your need a newer references than this, I suggest Graven et al. https://doi.org/10.5194/gmd-10-4405-2017, 2017. whic is a nice summary of existing atm d13CO2 data, but check if your given citation to Rubino et al. 2019 might be a better fit here.
- l 85 or so. A recent compilation of d13C_orgC data is contained in Verwega, M.-T., Somes, C. J., Schartau, M., Tuerena, R. E., Lorrain, A., Oschlies, A., and Slawig, T.: Description of a global marine particulate organic carbon-13 isotope data set, Earth Syst. Sci. Data, 13, 4861–4880, https://doi.org/10.5194/essd-13-4861-2021, 2021.
- Figure 1: Frame around upper fiugre ? The given d13C data (atm, ocean, orgC) need a reference in the caption. There is no „d13C_vertical mixing“, This is maybe d13C_DIC? Overall, I find the lower figure not very helpfull and I suggest you only keep the top map.
- l 118-119: The description of where the image was taken is already given in the caption of Fig 1, so the sentence here can be deleted
- l 186-191: This paragraph does not make sense to me:
- a: in Fig 3 your d13C_OC starts at 1850, here you say, it starts at 1800 (if so, show data).
- b: Are you using the data to calculate a fractionation factor of -21 permill or are you assuming the factor? If I look at Fig 3 d13C_OC is around -21 permil, but I am missing a calcuation (mean +. error). Furthermore, this is NOT your fractionation factor. For that you need to know / assume d13C_DIC, which in surface waters is around +1.5 to +2.0 permil (Gruber et al., 1999) which together gives you a fractionation of about -22 to -23 permil.
- c: „Second, we used the d13Ccalc from G. ruber and N. dutertrei, assuming isotopic equilibrium fractionation at the depths where each species calcifies. We estimated the d13CDIC yearly by subtracting the organic carbon fractionation factor from the corresponding d13Ccalc. This difference represents the inferred d13CDIC throughout the water column.“ I do not get it. I see that your first sentence says: d13Ccalc = d13C_DIC, which makes sense to me, your data in Fig 3 agree with Gruber et al. 1999). Why all the rest?
- Fig. 2 (which hopefully is deleted or heavily revised, see above): Why 1993-2013 on the right hand side, but 1957-2013 on the left hand side?
- Fig. 3: units are missing. Instrumental d13C_CO2 data go until 2010 or so, therefore the given reference to Keeling et al. 2001 cannot be correct.
- Fig. 4: units are missing. r2 of the regression lines are missing. Why do you use only data from 1975 here and from 1950 in Fig. 5? Give arguments and/or at best use the same time windows for analysis.
- Fig. 5: y-axis is not only d13C_calcite, but also d13C_DIC, maybe say only d13C. Units missing, r2 of regression lines missing. Why do you have a different version of the equation here and in Fig. 4 (here: y=a+bx; Fig 4: y=bx-a). None is wrong, but comparing both figures is thus more difficult than necessary.
- l 227: See my comments above on the fractionation factor.
- l 247: The slope per decade depends on your window of analysis. It is different on Fig 4 and 5. Give arguments for your choices.
- l 309: „atmospheric CO2 trends“. They are not restricted to Law Dome, but also in other ice cores, and, more important, for the last 40 years or so, also contained in instrumental measurements.
- Overall: You should put your finding into perspective of other studies on the 13C Suess effect in the ocean, eg Eide et al. (2017), which is cited, but I do not think the results presented there are widely discussed here. Do you (dis)agree with Eide?Citation: https://doi.org/10.5194/egusphere-2025-5945-RC2
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- 1
"Timing of the anthropogenic carbon invasion in the Southern California Current"
In their manuscript "Timing of the anthropogenic carbon invasion in the Southern California Current," Contreras-Pacheco et al. (2025) address a critical gap in our understanding of the global carbon cycle: quantifying how and when anthropogenic CO2 has penetrated the surface waters of Eastern Boundary Upwelling Systems, regions that remain poorly constrained in global carbon budgets despite playing a disproportionately important role as seasonal sources and sinks of atmospheric carbon. The authors address this gap through stable carbon isotope records spanning approximately 150 years, derived from organic carbon and shells from two foraminifera species in laminated sediments. These sediments offer an unusual high resolution archive for the southern domain of the California current, a region that is at the boundary between cool productive waters and warm subtropical waters and therefore sensitive to changes in both upwelling intensity and atmospheric carbon loading.
The manuscript has several strengths, such as the well-justified study site and the use of laminated sediments that provide a high-resolution archive extending back to the preindustrial era. The utilization of the multi-proxy approach combining two planktonic foraminifera from different depth habitats is methodologically sound. The integration of modern SOCAT CO2 fugacity data to establish the seasonal source-sink behavior of the region before interpreting the long-term sedimentary record is particularly commendable, as it grounds the paleoceanographic findings in directly observable present-day dynamics.
However, I have a few comments that I think will make the manuscript more robust. My main concerns revolve around quantitative analysis, lack of statistical treatment, and uncertainty quantification.
1) My first and most important concern relates to the chronological framework of the study. For a manuscript whose title explicitly addresses the timing of anthropogenic carbon invasion, the age model is surprisingly underdeveloped and, as presented, cannot be independently evaluated by the reader. In the main text, the age model receives only a single short paragraph (Section 2.4), with no figure, no sedimentation rates, and no uncertainty quantification. The supplementary material, while providing Figure S1, does little to resolve this concern. The entire chronology of core SaLa11-E19-MC1 rests on a single-proxy stratigraphic correlation based on calcium carbonate content matched against core BAP96-6C. This approach raises several methodological concerns because the visual correlation between the two carbonates is ambiguous, multiple peaks could be matched in different ways, resulting in a potentially non-unique stratigraphic alignment. There is also the underlying assumption that carbonate fluctuations are synchronous across the basin, which is stated, but it is not demonstrated, which makes the reader incapable of evaluating the reliability of the chronology on which everything else depends. The age uncertainty is never quantified. I suggest explicitly mark and justify the tie points used in the carbonate correlation, quantify the age uncertainty propagated into SaLa11-E19-MC1, and discuss how the 15-year gap between core collection dates (1996 versus 2011) was handled in the stratigraphic alignment.
2) A second important gap concerns the statistical treatment of the isotopic trends, which are the paper's primary quantitative contribution. The authors present slope comparisons between atmospheric and marine δ¹³C records reporting values of −0.12‰ per decade for foraminiferal calcite and −0.15‰ per decade for organic carbon, against −0.27‰ per decade for the atmosphere as central findings of the study, yet none of these trends are accompanied by any formal statistical analysis. There are no confidence intervals, no R2 values, no p-values, and no uncertainty propagation reported anywhere in the manuscript, given the substantial variability evident in Figures 3–5. Without knowing whether these slopes are statistically distinguishable from one another, or whether the trends themselves are statistically significant, the paper's main interpretive argument that the marine records show a systematically lower slope than the atmospheric trend due to upwelling buffering cannot be evaluated. I suggest a test of significance to determine whether the marine slopes are distinguishable from the atmospheric slopes.
3) Another aspect I am concerned about relates to the assumption of a constant phytoplankton fractionation factor used to reconstruct δ¹³C_DIC from the organic carbon record. The authors derive a fixed value of ε = −21‰ from the preindustrial period (1800–1940) and apply it uniformly across the entire 150-year record. The authors cite Young et al. (2013) whom in their paper, showed that phytoplankton fractionation change measurably between 1960 and 2010 in response to rising atmospheric CO2, using a fixed preindustrial fractionation factor to the post 1950 introduces a systematic bias into the reconstructed δ¹³C_DIC values which are then used to validate the foraminiferal calcite in Figure 5. The authors should explicitly acknowledge this limitation in the manuscript.
4) In Figure 5, the authors shows the presence of an δ¹³C offset between G. ruber and N. dutertrei explained in the text purely in terms of the different depth habitats of the species but do not discuss how the depths of the calcification may shift seasonally and interannually in response to changes in upwelling intensity, thermocline depth and chlorophyll maximum position especially for N. dutertrei whose preferred habitat is tied to the chlorophyll max. if the habitats have changed over the 150 year record, in response for example to the upwelling intensity this could introduce a non atmospheric component into the isotopic trends that are currently attributed entirely to the Suess effect, the author should address the potential sources of bias explicitly in the manuscript.
4) I also have a few comments related to the structure and depth of the discussion section, which is largely qualitative and somewhat circular. In the paper, the author shows that the upwelling of older, isotopically heavier subsurface waters partially buffers the atmospheric Suess effect signal, explaining the shallower slope observed in the marine records relative to the atmosphere. This is invoked repeatedly but never quantitatively, is it possible to estimate what fraction of the observed slope attenuation can be explained by subsurface water mixing alone?
5) I think it would be better to compare the other EBUS records from different ocean basins in the discussion such as Humboldt Current off Peru and Chile, or the Benguela Current off southwest Africa. This would substantially strengthen the paper's contribution to understanding how the Suess effect propagates through EBUS regions globally. If similar slope attenuations are observed in other EBUS sedimentary records, this would powerfully support the authors' mechanistic interpretation and elevate the paper's findings from a regional observation to a globally relevant result. However, if the attenuation observed in their system is stronger or weaker than in other EBUS regions, this would open an important discussion about how additional factors can control the regional expression of the Suess effect. I suggest that the authors add a dedicated paragraph in the discussion addressing this broader EBUS context.
Minor comments:
1) Abstract: Line 12 should mention the abbreviation CCS used in line 14
2) Lines 12-13 needs to be rewritten. How is the role of EBUS a well known high productivity region? Maybe remove ‘the role of’
3) Lines 28-29 need to be rewritten or removed. it is better to start the introduction by line 32: ‘over the past century, the ocean’s carbon uptake… then talk about the processes.
4) lines 37-40: There is no obvious link between this part and the previous part.
5) The caption for Figure 1 appears to be duplicated in the text at lines 117–119 of the manuscript.
6) Figure 3 is particularly overcrowded, with multiple cores, proxies, and reference datasets sharing overlapping symbol styles. I suggest at least separating the 3 figures so the separation is visual.
7) The conclusions section introduces some new interpretive content that does not appear in the discussion, particularly regarding the 1950s shift mirroring the Law Dome ice core record, which should either be developed properly in the discussion, or removed from the conclusions or mentioned in some way as a perspective.