Raising paleoceanography

Abstract

[1] Generation of multiply replicated, intensely sampled, paleoceanographic "type sections," together with additional attention to data reproducibility, would improve the breadth and reliability of paleoceanographic results and thus the importance of the field, but it would require additional resources for implementation. The rapid rise in the importance of paleoceanography recommends more resources to support a higher level of investigation. Paleoceanography appears ripe for generation of multiply replicated "type sections," with international interlaboratory duplication. To this very interested and enthusiastic friend of paleoceanography, the added effort and expense would be more than justified by the improved confidence in the science and the improved ability to communicate with the public and policy makers. [2] The experience of the Second Greenland Ice Sheet Project (GISP2) and Greenland Ice Core Project (GRIP) central Greenland ice coring may be relevant. On the basis of a highly noncomprehensive exercise during June 2003, the subject line "GISP2 and ice" located 238 entries in the online ISI Web of Science since 1986, and "GRIP and ice" 241 more, almost all related to the ice cores. Just one GRIP paper (that by Dansgaard et al. [1993], which was not located by the "GRIP and ice" search) had been cited over 900 times. In comparison, "Cariaco Basin" returned 41 matches with just over 600 total citations, and "Bermuda Rise" located 44 entries again with just over 600 citations, and with some of the papers unrelated to paleoceanography. Despite the wonderful science done at the Cariaco Basin, Bermuda Rise, and elsewhere, for the last ice age it appears that the central Greenland ice cores are serving as the unofficial "type section" to which other records are compared. [3] As one who played a small part in the central Greenland ice coring, I am confident that the success of GRIP and GISP2 does reflect the quality of the natural archive, and the hard work, dedication and indeed brilliance of my colleagues [Mayewski and Bender, 1995; Hammer et al., 1997]. The high time resolution, accurate dating, and multiparameter reconstructions recommend the ice cores for intercomparison. I also believe that the existence of both GRIP and GISP2 contributes to this success (just as the earlier Dome C, east Antarctica, ice core aided the success of the Vostok project). The almost complete duplication of effort in central Greenland between the GRIP and GISP2 teams surely demonstrates the quality of the records; to disbelieve a team, one must explain how almost identical results were obtained by an independent team using different instruments on different ice in different laboratories in different nations. Where possible, measurements on each core were made by more than one laboratory as well, improving confidence further. Blind intercomparisons within a team and between the teams [e.g., Sowers et al., 1997] were unequivocally successful in demonstrating accuracy of the studies and even in identifying flow disturbances in very deep ice but their absence in most of the record. Snow-pit and shallow-core studies of spatial variability, sampling each of many orders of magnitude from centimeters to hundreds of kilometers, increased confidence further. Analysis for as many indicators as possible improved and extended the paleoclimatic insights [Mayewski and Bender, 1995; Hammer et al., 1997]. [4] This multiply duplicated, multiparameter strategy was made possible by visionary leadership of the projects from the science and funding sides and by a lot of help from distinguished scientists, including paleoceanographers. For example, the GISP2 project led by chief scientist P. Mayewski benefited from an advisory committee chaired by W. Broecker that included J. Andrews, C. Bentley, G. Denton, J. Imbrie, and S. Lehman. (I was a graduate student during GISP2 planning and take absolutely no credit for the wise approach adopted.) The strategy was expensive, time-consuming, and quite honestly, often a pain. Delays in agreement with collaborators really do affect graduate students, postdoctoral fellows, and untenured faculty wishing to publish before they perish. However, for such really important records, the effort proved highly worthwhile; in discussing climate change with a policy maker, we can pound the table and insist that the results are solid, because the level of duplication and intercomparison provides such high confidence. [5] The paleoceanographic realm does have very accurate well-duplicated records, but many other records are more difficult for an outsider to evaluate. Do differences between two cores reflect paleoclimatically significant spatial heterogeneity in the ocean, local sedimentary conditions, dating uncertainty, bioturbation, analytical uncertainty, mistakes in core handling, foram picking, sample labeling, or instrument calibration? (Having studied many kilometers of ice core, I know that even vigorous effort does not always produce perfect data from perfect core, and I suspect that the same may apply to marine muds.) [6] A single laboratory sampling, analyzing, and publishing on a single core is the fastest, least expensive, most efficient way to generate hypotheses. However, for discussion with policy makers, the exploratory results leave one less confident than ideal. [7] I believe that three actions would advance paleoceanography further. First, all of us must help make the case for the funding agencies that additional resources are required. Because second, the price of paleoceanographic research should go up. Collection and analysis of duplicate cores from a site, and of duplicate samples from a core, should become more common, as should higher time resolution in sampling and dating. Journal space and page charges will be needed to show the extra data generated from this effort, including routine presentation of error bars and implied sedimentation rates. Greater attention to laboratory standards and intercalibration is warranted. Third, discussions should be started on how and where to generate a few internationally coordinated, multiply replicated, multiparameter, high time resolution-type sections of oceanic change. The great size, horizontal and vertical variability, and potentially long time histories in the ocean will complicate selection of ideal type sections, but good candidates are almost guaranteed to emerge. [8] It is easy for me to type this into a computer and hard for a community to then do the work. However, the payoff should be worth the effort. In the Earth system the oceans play a critical central role that cannot be fully understood without a better grasp of their history. Having seen the vigor of the paleoceanographic community, it is easy for me to be optimistic about the future. [9] I thank numerous colleagues including David Lea, Mike Arthur, Lloyd Keigwin and Wally Broecker for stimulating discussions and the National Science Foundation Office of Polar Programs for support. I declare that I have no competing financial interests of which I am aware, and that this contribution is not under consideration for publication elsewhere.

Keywords

Affiliated Institutions

• Pennsylvania State University US

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