Now that the AGU exposure-dating rush is over it is time to take a look at the online exposure age and erosion rate calculator usage statistics. Here are the yearly usage stats for the last four years of operation for the online calculators:
| Year | Erosion rate calculations | Exposure age calculations | Total calculations |
| 2006 | 1367 | 8698 | 10065 |
| 2007 | 1919 | 29068 | 30987 |
| 2008 | 3565 | 55078 | 58643 |
| 2009 | 3104 | 41748 | 44852 |
These are compiled by counting each request for an individual exposure age or erosion rate calculation once. That is, if you submit 10 samples at the same time, 10 calculations are logged. The “test samples” accessible from the dropdown menu are not counted. Of course, 2009 is not quite over yet but the period between AGU and the end of the year is generally pretty slow.
Here are the monthly stats:
And the daily stats:
Some observations: first, after rapid growth in 2006-08, usage has stabilized and dropped off a bit in 2009. Why is this? For one thing, the number of calculations submitted to the exposure age calculator exceeds the global number of Be-10 and Al-26 AMS measurements by approximately an order of magnitude. So it is possible that most people have finished calculating exposure ages from old data, and the amount of calculator usage has fallen more into line with the amount of actual new data being generated. It’s also possible that we are seeing the effects of competition from a partially completed mirror site at the University of New Mexico or from the recently released “ACE” software. Overall, it seems most likely that the calculator usage has simply dropped into an equilibrium with the number of people who are actually interested in cosmogenic-nuclide geochemistry.
Second, exposure age calculations continue to be more than ten times as popular as erosion rate calculations. Why is this? One guess is that users interested in exposure dating would like to interpret exposure-age measurements at a much higher level of precision than users interested in erosion rates. For most applications of erosion-rate measurements to actual geologic problems, precision at the ~10% level is more than adequate. However, many users of exposure dating would like to make interpretations at a much higher level of precision, to answer questions like whether or not a moraine belongs to the Younger Dryas or the Antarctic Cold Reversal. Whether or not this is a good question to ask belongs to a different discussion, but I envision these users repeating their calculations with various different production rate calibration data sets, surface erosion rates, etc., to find out what effect these adjustments have on their results. Of course, I specifically constructed the online calculators to make this practice as inconvenient as possible — they are supposed to provide a standardized calculation method, not a means of production-rate shopping — but I suspect that this sort of activity accounts for a lot of repeated exposure age calculations. On the other hand, once an erosion-rate calculation is done once, it’s done and there’s no need to revisit it.
A blast from the early days of targeted advertising:
A recent article by Lebatard and many co-authors in the Proceedings of the National Academy of Sciences shows why correct error propagation is important. In this article, incorrect error propagation leads to a wrong conclusion. Correcting it largely invalidates the point of the paper. The article is open access and is here.
What these authors are trying to do is date the occurrence of the early human ancestor Sahelanthropus tchadensis in a lake sediment section in Chad. They use the Be-10/Be-9 ratio of the lake sediments to accomplish this, on the basis that the 10/9 ratio of leachable Be in the lake and surface sediments is constant through time. Thus, the present 10/9 ratio of lake sediments preserved in a stratigraphic section is related to their age by:
Where 
This is straightforward except that there is no way to be sure from first principles that the key assumption — constant depositional 10/9 ratio over time — is true. Be-10 is supplied from fallout of cosmic-ray produced Be-10 in the atmosphere, which ought to be more or less steady. Be-9, on the other hand, comes from dissolution of Be-bearing minerals somewhere in the lake basin, which might not be steady. Thus, the only way to know whether this key assumption is true is to look at the change in the 10/9 ratio over time: if we see i) a smooth, steady decrease in 10/9 ratio with stratigraphic age, and ii) the same 10/9 ratio in stratigraphically closely spaced samples that should share the same age, then we might reasonably conclude that the depositional 10/9 ratio is more or less constant. The authors of this paper follow this sort of reasoning, as follows. First, they observe that ages from sets of samples from the same stratigraphic unit — which should be the same within measurement error — show values of the MSWD statistic that are near 1. MSWD near 1 indicates that the scatter in data is commensurate with the uncertainties in the data, i.e. no excess scatter is present. Second, they observe that average Be-10/Be-9 ages from certain stratigraphic intervals are broadly in agreement with biostratigraphic age constraints. These two observations lead them to conclude that the 10/9 ratio in lake sediments is constant through time.
The problem with this line of reasoning is that they have incorrectly calculated MSWD values, because of incorrect error propagation. This is clear from two observations. First, the stated relative uncertainties in the ages are greater than the relative uncertainties in the ratio measurements. For example, a sample at 6.1 meters in their section TM254 (readers who care may want to look at their Table 2 at this point) has an 8% measurement uncertainty on the ratio and an apparent age of 6.5 Ma. The reported uncertainty on the age is 0.75 Ma, a 10% uncertainty. This can’t be correct. Think about it — 7.2 Ma is five half-lives of Be-10. A 50% uncertainty on the ratio measurement would mean an uncertainty of one half-life, or 1.4 Ma. If the age is five half-lives, this is only 20% of the total age. So a 50% uncertainty in the ratio measurement becomes only a 20% uncertainty in the age estimate. The relationship is not quite linear, but this means that an 8% error in the ratio at this age should become something like a 4% error in the age. This is a general property of age uncertainties in radioactive decay systems: as age increases, the relative uncertainty on the age becomes much smaller than the relative uncertainty on the amount of parent remaining. Thus, the fact that these authors report relative age uncertainties that are larger than relative ratio measurement uncertainties indicates that something is wrong.
The other observation that clearly indicates that something is wrong comes from calculating the MSWD on the measured ratios, instead of the ages, for the sets of samples from particular stratigraphic levels that the authors have averaged. For example, six samples from 7.3-8.5 m in the TM254 section (Table 2 again) have 10/9 ratios that vary by a factor of 5 and have measurement uncertainties of 9-16 %. These measurements clearly do not belong to a single population and have a MSWD of 49.8. However, when the authors transform these ratios to ages, somehow the ages from the same samples have a MSWD of 1.1. If the ratios don’t belong to a single population, then clearly the ages derived from those ratios can’t belong to a single population either. Something is seriously wrong here.
An additional notable observation is that some of the MSWD values reported by the authors (0.10-0.28) are wildly improbable. This suggests overestimation of uncertainties.
So what happens if we do the error propagation correctly? Here is how to do the error propagation. Uncertainties in the ages come from three sources: i) uncertainty in the estimate for the depositional 10/9 ratio (
where
and 
| Stratigraphic ht (m) | 10/9 ratio (x 10^-10) | Apparent age (Ma) | Reported age uncertainty | Correct age uncertainty |
|
|
||||
| 8.5 | 16.36 +/- 2.60 | 5.39 | 0.92 | 0.31 |
| 8.4 | 7.68 +/- 0.76 | 6.87 | 0.80 | 0.19 |
| 8.4 | 3.07 +/- 0.34 | 8.67 | 1.11 | 0.22 |
| 8.1 | 9.04 +/- 1.13 | 6.55 | 0.91 | 0.25 |
| 7.9 | 6.89 +/- 0.65 | 7.08 | 0.80 | 0.18 |
| 7.3 | 6.20 +/- 0.83 | 7.39 | 1.08 | 0.26 |
|
|
||||
For these six samples, again, the authors computed a MSWD for the ages of 1.14 using the incorrect age uncertainties. Based on this value, they concluded that the ages belonged to a single population and they could properly average them to obtain a summary age and standard error for this part of the stratigraphic section. This is incorrect. The actual MSWD of these ages is 18, clearly showing that the apparent ages do not belong to a single population, as we expect from the fact that the 10/9 ratios clearly do not belong to a single population.
A plot of ratios and ages from this section shows this situation clearly:
The plot on the left shows that 10/9 ratios, as expected from the general concept of the method, do generally decrease with stratigraphic depth. However, they are widely scattered around this general trend by an amount well in excess of measurement uncertainty. More about this later. The plot in the center shows apparent ages with the (incorrect) uncertainties reported by the authors. It is clear from this plot why getting the error propagation wrong leads to a misleading conclusion: the large errors here give the impression that the data are scattered around a smooth increase in age with depth, by an amount that is commensurate with the measurement error. The third plot shows the same apparent ages with the correct uncertainties. It is clear that although ages do generally increase with depth, ages from the same stratigraphic level, like ratios from the same stratigraphic level, disagree by amounts well in excess of measurement uncertainty. Note again that the fact that we have not included uncertainties in the initial ratio and the decay constant does not change these conclusions: errors in these parameters would shift the entire array of ages without changing the relationship between them.
To summarize, one of the key observations that the authors cite in support of their claim that the depositional 10/9 ratio is constant through time is that ages from closely spaced stratigraphic levels agree within uncertainty. Doing the error propagation correctly shows that, in fact, this is not the case. In fact, the spread of 10/9 ratios from closely spaced levels is well in excess of measurement uncertainty. This shows fairly clearly that, in fact, the 10/9 ratio was not constant over time. It most likely stayed within a certain range — as shown by the overall trend of decreasing ratio with stratigraphic depth — but varied by as much as a factor of 5 over short time intervals.
Why this variation? Remember Be-9 is delivered to the lake by dissolution of Be-bearing minerals in the watershed. It seems certain that the rate of Be-9 supply is affected by hydrologic changes, and the fact that the sediments in question show a fluctuating lake level indicates that there were hydrologic changes. Thus, it seems very likely that orbital-scale hydrologic changes affected Be-9 delivery to the lake, and thus the 10/9 ratio of leachable Be in the lake system, on relatively short time scales. In any case, the data in this paper pretty clearly show that the assumption of constant 10/9 ratio that is necessary to apply this dating method, is false at short time scales.
Is the entire dating exercise wrong then? Probably not. Clearly the assumption of strictly constant depositional 10/9 ratio is wrong. However, ratios do clearly decrease with age, showing that changes in the depositional ratio most likely took place on a shorter time scale than is represented by the entire section, and thus that the ratio probably stayed within some bounds. So the 10/9 ratios do give us some age information. The important conclusion is that the true uncertainty in the actual age of the samples that the authors dated is much bigger than the measurement uncertainty. If the initial ratio is only known to a factor of 4, then the age can only be known with a precision of two half-lives of Be-10, that is, 2.8 Ma. So the ages reported in this paper are most likely within two million years of the true age of the true age of the sediments, and fossils, in question. The important conclusion is that the precision of the Be-10/Be-9 method is much poorer than proposed by the authors. The authors call attention to the fact that the ages agree with biostratigraphic age constraints (which also have a precision of 1-2 Ma) and suggest that the 10/9 ages are more accurate than the biostratigraphic ages. In fact this is not the case; the precision of the two methods is similar.
Could this be fixed? Yes. The key is to know the amount and the time scale of changes in the depositional 10/9 ratio. These could easily be obtained by high-resolution sampling at the presumably orbital time scales that have the largest effect on the lake basin hydrology. Once known, this information could be used to find out what amount of time averaging would be needed to ensure that the constant-initial-ratio assumption was true.
Is Sahelanthropus tchadensis actually 6.8-7.2 Ma? Perhaps. Nothing in this paper disproves that hypothesis. However, it does not prove the hypothesis either. Likewise, the hypothesis that Australopithecus bahrelghazali at this site is contemporaneous with the extremely well dated (by Ar-Ar) Lucy skeleton in Ethiopia is neither supported nor refuted by the Be-10/Be-9 results.
One of the more suspenseful questions surrounding the periodic CRONUS-Earth and CRONUS-EU meetings is: how is the geological calibration exercise going? This is important because currently the vast majority of exposure ages are computed using a “global calibration data set” composed of a variety of Be-10 and Al-26 production rate calibrations conducted between 1989 and 2005. Henceforth this will be abbreviated “GCDS” (however, it should not be confused with George H.W. Bush’s and this reporter’s alma mater) Also, the term ‘reference Be-10 production rate’ will henceforth refer to the Be-10 production rate due to spallation at sea level and high latitude, normalized to the Be AMS standards of Nishiizumi et al. (2007). The reference Be-10 production rate derived from the GCDS is exhaustively documented by Balco et al. (2008), and is 4.49 atoms/g/yr for the “St” scaling scheme, and 4.87 atoms/g/yr for the “Li” scaling scheme (these abbreviations are from the Balco et al. reference — St is the Stone(2000)/Lal(1991) scaling scheme, and Li is that of Lifton(various references). The Li scheme is more or less representative of several scaling schemes based on neutron monitor measurements that give similar results).
Recently a couple of studies have indicated that the reference Be-10 production rate derived from the GCDS is too high to give correct exposure ages for at least some times and places. Balco et al. (2009) compiled a handful of Be-10 production rate calibration measurements from late-glacial sites in northeastern North America; these yielded a reference Be-10 production rate about 10% lower than that derived from the GCDS. Aaron Putnam (UMaine) and colleagues recently unearthed an excellent calibration site in New Zealand — an early Holocene landslide that placed exposure-datable boulders directly on top of flattened but radiocarbon-dateable underbrush — and got similar results (these are described in Aaron’s Goldschmidt 2009 abstract).
One main point of the CRONUS-Earth project was essentially to redo the GCDS, that is, to find, exhaustively document, and comprehensively analyse a global set of high-quality calibration sites. This has now been in progress for a couple of years. So the question is, are the early CRONUS data in agreement with the GCDS, or do they also show that we have been using a production rate that is generally too high?
With regard to Be-10, there now exist new measurements from three calibration site locations: the wave-cut shorelines of Lake Bonneville, Utah (true exposure age of 17,400 years); several late-glacial moraines in Scotland (11,600 years); and a late-glacial moraine in New Hampshire (13,900 years). Most of these samples have been analysed by both the UW and Lamont prep labs, and a handful by several other labs. One important aspect of the entire project is to compare the results from multiple laboratories, but I’ll ignore this for the time being and focus on the data from UW that have been compiled by John Stone here.
First, a refresher on what the 2008 GCDS looks like. The following figure is part of Figure 5 from Balco et al. 2008, that shows the scatter of all the various calibration data around the reference production rates derived therefrom, for St and Li scaling schemes. This has not been renormalized to reflect the 2007 Nishiiumi restandardization: to bring it up to date, divide the y-axis values by 1.106. Two things are clear from this: first, a lot of the measurements have large uncertainties; second, there is a lot of scatter. Furthermore, even with some rather large measurement uncertainties, the scatter is still well in excess of that expected from measurement uncertainty.
Now, compare this to a similar plot for the early CRONUS results. This is a slightly different plot, requiring the following steps. First, determine the reference production rate that best fits the calibration data; second, using that production rate, calculate the exposure age of all the calibration samples from their measured Be-10 concentrations; third, compare to the actual age of the calibration sites by computing the ratio t_calculated/t_actual. If everything goes as planned, the calculated exposure ages should all be indistinguishable from the actual ages, and all data will plot on the line y = 1 within error. This plot is functionally the same as the production rate vs. elevation plot shown above, except that the best-fitting reference production rate is normalized to one. Both plots show the scatter of the calibration data set around the best-fit production rate. The choice of sample elevation as the independent variable mainly serves to spread out the data nicely.
This first plot shows the early CRONUS results by themselves on the Li and St scaling schemes:
Two things are important here: One, the uncertainties on the individual measurements are much smaller, mostly around 3%. This is largely due to steady AMS improvements at LLNL (where these measurements were made) over the last ten years. Second, the scatter of the individual samples around the best-fit production rate is much smaller. Statistically, no excess scatter is present. This is not quite a fair conclusion yet — because the new data are not as geographically scattered as the 2008 GCDS, so scaling scheme errors are suppressed — but the scatter in the new data is in fact much less than that in any geographically equivalent subset of the 2008 data set.
Next compare these results to the 2008 GCDS. The actual values for the reference production rates derived from the new CRONUS data, for comparison to those derived from the GCDS discussed above, are 4.2 atoms/g/yr for the St scaling scheme and 4.65 atoms/g/yr for the Li scaling scheme. These are lower. This is the same figure above, with the GCDS calibration samples added by calculating their exposure ages using the best-fit production rate from the new data. Old data in red, new data in black.
The reference production rate derived from the new data systematically overestimates the exposure age of the calibration sites from the 2008 GCDS. This is another way of saying that the reference production rate implied by the new data is significantly (by almost 10%) lower than that implied by the 2008 data set.
The reference production rates implied by these new data are, however, similar to the reference production rates implied by the Northeast North America and New Zealand calibration data sets described above. The following figure makes this comparison — we are still normalizing to the reference production rate that best fits the new CRONUS data, these data are shown in black, the NE North America data are in green, and the NZ data are in blue.
The early CRONUS data (black) show good agreement – well within measurement uncertainty — with the NE North America calibration data (green), although the latter display more scatter and somewhat of a tail on the low end. Decent agreement between these two data sets is not a huge surprise because of their geographic overlap. The New Zealand calibration data, on the other hand, predict significantly lower reference production rates than the early CRONUS data for all available scaling schemes (both shown and not shown). This is unexpected — although geographically far apart, the NZ sites and the CRONUS sites are fairly similar in elevation and magnetic field characteristics. The remaining disagreement suggests that we may be missing something in the production rate scaling process, but it’s not clear what that might be.
To summarize, these early CRONUS results agree with the recently published regional calibration data sets in indicating fairly clearly that the 2008 GCDS overestimates production rates, at least at the elevations (low) and latitudes (high) of the new calibration data. Thus, exposure ages computed using the 2008 GCDS — which is incorporated into the CRONUS online exposure age calculators by default — may be systematically too young (although, it is important to note, still contained within the 10% uncertainty of the GCDS-derived production rates). This of course, puts the CRONUS project in a situation like that of an epidemiologist who finds that patients given the experimental drug seem to be dying a lot faster than those in the control group. Should he stop the study? Should we change the default production rates in the online calculator to reflect the fact that the currently accepted production rates seem to be too high?
At present it is probably not a good idea to do this, mainly because the CRONUS geological-calibration efforts are progressing steadily but still half-baked. No one has yet compiled results from multiple labs in such a way as to determine whether inter-lab biases are important. More measurements on these calibration sites as well as from others that will increase the range of age, elevation, and magnetic field strength spanned by the data set are still in progress. New information is still coming in about the true age of many calibration sites. None of the calibration results have been comprehensively enough documented in the public literature that others can evaluate how good they are.
On the other hand, there are two things that can be done now. The first is to remember that if authors of exposure-dating papers include ALL the data necessary to recalculate the exposure ages with a different production rate calibration data set, there is no problem. If all these data are recorded — in the paper itself or in a permanent and easily accessible online data repository, not in the author’s file cabinet — then it will be easy to recalculate exposure ages in future to account for improved production rate calibrations.
The second thing, of course, is that one can calculate exposure ages using one of the new calibration data sets. In order to facilitate this, I’ve placed a handful of pages on the ‘developmental’ section of the CRONUS-Earth online exposure age calculators that allow one to calculate exposure ages using i) the Balco et al. 2009 northeast North America calibration data set, ii) Aaron Putnam and colleagues’ New Zealand calibration data set, and iii) the early CRONUS results from the UW lab described above. Will these yield more accurate ages? In the situation where one is applying a calibration data set that is close in space and time to one’s unknown-age sites — that is, using the NE North America calibration to compute exposure ages for late-glacial NE North America or the NZ calibration to compute ages in NZ — yes, the resulting ages are almost certainly more accurate. On the other hand, whether or not the new CRONUS calibration data will yield more accurate ages than the GCDS for all sites globally is still unknown. At this point, the main thing that is certain is that there will be some future revisions to the Be-10 production rate. Again, the observation that there still seems to be a lot to learn about production rates emphasizes the importance of complete data reporting — any exposure-dating papers that don’t contain enough data to recalculate the ages will rapidly and invariably become not only incorrect, but useless to future researchers.
Incomplete list of references:
Balco G., Stone J., Lifton N., Dunai T., 2008. A simple, internally consistent, and easily accessible means of calculating surface exposure ages and erosion rates from Be-10 and Al-26 measurements. Quaternary Geochronology 3, pp. 174-195.
Balco G., Briner J., Finkel R.C., Rayburn J., Ridge J.C., Schaefer J.M., 2009. Regional beryllium-10 production rate calibration for late-glacial northeastern North America. Quaternary Geochronology 4, pp. 93-107.
K. Nishiizumi, M. Imamura, M. Caffee, J. Southon, R. Finkel, and J. McAnich. Absolute calibration of Be-10 AMS standards. Nuclear Instruments and Methods in Physics Research B, 258:403–413, 2007.
Perhaps the most impressive presentation at the cosmogenic-nuclide-fest that was the recent Goldschmidt meeting was the unveiling of two new measurements of the Be-10 half-life, by a European group spearheaded by Friedhelm von Blanckenburg. This is described in two Goldschmidt abstracts, this one by Gunther Korschinek and this one by Jerome Chmeleff.
This is important because it appears to finally resolve a complicated and embarrassing problem with Be-10 measurements and the exposure ages derived from these measurements. Basically, past measurements of the Be-10 half-life, although individually precise, differed by approximately 10%. This was an unfortunate situation for cosmogenic-nuclide applications that rely on radioactive decay of Be-10 — burial dating in particular — but in itself of limited importance for the main application of Be-10 measurements, exposure dating of surfaces that are very young with respect to the Be-10 half-life. A more important problem for exposure dating came from the link between half-life measurements and the Be isotope ratio standards used for AMS measurement of exposure dating samples. AMS measurement of sample Be-10/Be-9 ratios relies on comparison between samples and Be standards whose 10/9 ratio is absolutely known — and the way one determines the absolute amount of Be-10 in one of the source materials used to make these standards is by decay counting. Thus, if you start with an incorrect value for the half-life, you get the wrong isotope ratio in the standard and then the wrong isotope ratio in the sample. This means that if one were to take a particular sample and measure it against two AMS standards whose assumed isotope ratios were derived from different values of the half-life, you would infer different isotope ratios and hence Be-10 concentrations. In principle this is not a problem if i) all measurements on calibration samples used to determine nuclide production rates, and ii) all measurements on unknowns, are referenced to the same AMS standards, but in practice it is difficult to ensure this, and the existing Be-10 literature is rife with inconsistent standardizations.
Two steps were needed to fix this problem. First, an absolute determination of the isotope ratios of commonly used AMS standards that did not rely on an existing half-life measurement. Second, a measurement of the half-life that did not rely on any assumed concentrations of existing isotope ratio standards.
Kuni Nishiizumi and a handful of co-workers, mostly from LLNL, accomplished the first of these a couple of years ago (in a 2007 paper noted below). They used the LLNL accelerator/detector array to implant a precisely known number of Be-10 atoms in a silicon wafer, then added a measured amount of Be-9 to obtain a sample of Be with an absolutely known 10/9 ratio. They could then use this as a primary standard to measure the true 10/9 ratio of many of the commonly used AMS Be standards. This solved the problem of Be-10 concentration measurement by uncoupling the assumed isotope ratios of AMS standards from any particular value for the Be-10 half life. This in turn made it possible to determine how many atoms of Be-10 were present in a sample without any assumptions about the Be-10 half-life.
Chmeleff, Korschinek, and their co-authors have now solved the second half of the problem by determining the Be-10 half-life without recourse to any of the existing stocks of Be-10-enriched Be. They began by manufacturing a new Be-10 enriched Be solution. In order to determine the Be-10 half-life from such a solution, one must i) measure the Be-10 activity by decay counting, and ii) determine the amount of Be-10 present, which typically involves measuring both the total Be concentration and the absolute 10/9 ratio. The activity is straightforward to measure by liquid scintillation counting, and each group made a separate activity measurement using this method. The difficult part of the overall project is to measure the absolute 10/9 ratio.
The Chmeleff group accomplished this by ICP-MS, a technique which is straightforward except for the problem that the instrument has a large mass fractionation. They first attempted to account for the mass fractionation using a Be-7 spike; for a variety of interesting reasons this proved to be an extremely instructive radiochemical parable — if you have the opportunity to get this story from someone involved in this project, ask them — but not an successful measurement. Fortunately they could fall back on determining the mass fractionation characteristics of the ICP-MP by analysing samples of numerous other elements with known isotope ratios and establishing an atomic mass – mass fractionation relationship.
The Korschinek group used a completely different method known as heavy ion elastic recoil detection. To the extent that I understand how this works, one coats a silicon wafer with the Be solution to be analysed, and then bombards it with a high-energy ion beam. Be atoms are scattered from the surface with sufficient energy to be individually identified in an energy-loss detector similar to that used for AMS measurements.
The impressive part of these two experiments is that they involved two completely independent measurements of the quantity of Be-10 and its activity, but both obtained equivalent results for the Be-10 half-life, the mean of which is 1.387 +/- 0.012 Ma. This value is i) consistent with the value inferred by retroactively applying the Nishiizumi et al. (2007) restandardization to the Be solutions from which the half-life was originally determined, but ii) significantly more precise.
To summarize, even though Kuni Nishiizumi made an excellent point at the meeting — that early on in the development of radiocarbon dating, the C-14 community thought they had measured the C-14 decay constant accurately, but they were wrong – in my opinion the issue of the Be-10 half-life is now for all practical purposes solved.
The combination of this result and the Nishiizumi et al. (2007) restandardization of AMS standards has two important effects on cosmogenic-nuclide geochemistry. First, production rate calibration measurements and exposure-dating measurements in the existing and future literature, even if made against different AMS standards, can now be restandardized to a common basis. This makes it possible to accurately compare the results of different exposure-dating studies. The ability to compare two exposure-dating studies on a common basis may seem like a trivial thing, but to the embarrassment of the entire community it has not in general been possible in the past. We can stop looking away and mumbling about the weather when questioned on this topic by other geochemists.
Second, a much more precise determination of the Be-10 half-life significantly increases the precision of cosmogenic-nuclide burial dating. This method is becoming a lot more popular — in large part for purposes of dating hominin fossils and stone tool assemblages in Plio-Pleistocene sections without volcanic ashes — and half-life uncertainties are a significant fraction of the total uncertainty in this method.
Only two challenges remain. First, the difficulty of determining which AMS standards were used, and what isotope ratios were assumed for these standards, in studies from the existing exposure-dating literature is pathetic and appalling. No matter how much we know about the true isotope ratios of AMS standards, if a paper doesn’t document what standard and assumed ratio was used – and most do not — the exposure ages in that paper are a useless waste of time and money. Authors, editors, and reviewers must do a better job of making sure that all exposure-dating publications contain enough information to unambigously define how many Be-10 atoms are present in each sample. Sure, fully understanding this issue is complicated, but it is not optional. Second, we now must persuade von Blankenburg, Chmeleff, and Korschinek to measure the Al-26 half-life with equal precision.
Reference:
K. Nishiizumi, M. Imamura, M. Caffee, J. Southon, R. Finkel, and J. McAnich. Absolute calibration of Be-10 AMS standards. Nuclear Instruments and Methods in Physics Research B, 258:403–413, 2007.
Q: I was recently reading through a JGR paper and noticed a probability density plot created with a Matlab script called “Camelplot” that was attributed to you. The figure developed from this plot looks great. Where do I get a copy of this code?
A: The m-file is here. A condition of using this code is that you must refer to the diagrams it produces as “camel plots” rather than “probability density plots.”
Q: Do the online exposure age calculators compute years before present? That is, years before 1950, like calibrated radiocarbon ages?
Short answer: The exposure age calculator computes the exposure age, that is, the length of time the sample has been exposed to the cosmic-ray flux. It does not give an absolute age in years before 1950 (or any other year).
For example, say a moraine boulder was emplaced 1000 years ago, that is, in 1009 AD. Barring any other complicating factors, if you computed the exposure age of this sample using the online calculator you would find that its exposure age was 1000 years. However, if you could date the same event by radiocarbon dating, and everything also worked perfectly, you would obtain a calibrated radiocarbon age of 942 years before 1950.
Obviously, this discrepancy is smaller than the age uncertainty in nearly all exposure dating applications, so in the vast majority of cases it is not necessary to worry about it.
Long answer: The calculator is always computing the exposure age in the sense of years the sample has been exposed before analysis, not as “years before present” where the present is some defined calendar year.
The only places that 1950 comes in are as follows:
1. Some of the production rate calibration sites have independent ages in calibrated radiocarbon years before 1950. I did not correct these to 2008, or whatever date the samples were analysed, before computing the production rates. That is, if a calibration site is, say, 15,000 calibrated radiocarbon years old and the samples were analysed in 1996, I did not correct the age to 15,046. This is a ballpark average age for the calibration sites, which means that the production rates are, technically, too high by a factor of approximately (50/15000) = 0.3 %. True, this is wrong, but as you can see it is not very important in light of the numerous other uncertainties in the production rate.
2. For the time-dependent scaling schemes, the time step is 500 years during the Holocene. The magnetic field at time zero is represented by the 1950 DGRF magnetic field. This is technically wrong too, because time zero in an exposure age calculation is not 1950, it’s the time you collected the sample. Then the cutoff rigidity is assumed to change linearly from whatever it is at time 0 to whatever it is at time 500 years ago. No shorter-time-scale magnetic field variability is represented. No shorter-time-scale solar variability is represented either — that record gets filtered at 500 years as well. Sorry Nat.
So “years before 1950″ are NOT what is being calculated. In order to do it that way, you would have to actually subtract some number of atoms/gram from the measured value to get back to whatever the Be-10 concentration was in 1950, and in order to do that the user would have to enter the year of sample collection. As users do not have to do this, there would be no way to implement this scheme. To be honest, it is not clear to me why anyone would do it this way — to me, the concept of an “exposure age” clearly indicates the number of years that a sample has been exposed. However, recently a bunch of people have asked about this so there appears to be some confusion.
One implication of this is that the absolute time to which the exposure age is referenced (and the absolute times to which all the time steps in the paleomagnetic field reconstruction are referenced) is a moving target. That is, an exposure age of 200 years measured in 2000 gives the year 1800, whereas an exposure ages of 200 years measured in 2008 gives the year 1808. At present low-level measurements are not precise enough to care about this issue, but, sure, we should probably fix it. Certainly this will need to be fixed after, say, another hundred years have elapsed.
I didn’t think that any parts of the calculator output pages or documentation contained the phrase “years before present” instead of just “exposure age.” Unfortunately, as of July 11 I am embarassed to note that I did place “yr BP” on the axes of some of the diagnostic plots on the single-sample output page. That is now fixed. I apologize for the oversight.
The main thing that really should be fixed at some point is to include shorter-timescale magnetic field variability as you approach the present. Realistically, this would be over-precise with regard to the production rate calibration (because all the production rate calibration sites are much older) so I don’t think it would result in a real improvement in the results. In fact, in the absence of any additional calibration data from young sites, I believe it would result in an overly optimistic estimate of the precision of the dating technique for young samples. However, it would be the proper way to do things.
Finally, the reference production rates refer to sea level, high latitude, at time zero.
At the Goldschmidt meeting last week, Silke Merchel gave a talk about sort of an ad hoc AMS intercomparison exercise that she carried out recently. Basically, she prepared a large number of Be-10 and Cl-36 AMS cathodes from a few solutions with different isotope ratios, and shipped them off to various AMS labs to be analysed as unknowns. In this talk, she then revealed the results, and stated which AMS lab produced which result. At first appearance the results were not too good: results from the full set of AMS labs differed by up to tens of percent for both nuclides, and there appeared to be significant systematic differences between various pairs of labs. A PDF of her abstract (which unfortunately gives only a fraction of the information in her talk) is here.
This is sort of a controversial thing to do. Immemorial custom in the radiocarbon-dating community requires that AMS intercomparison exercises be carried out in an anonymous fashion, where a central authority distributes an intercomparison material, the labs run it and submit results in sealed envelopes to the central authority, and the C.A. compiles the results and publishes them as statistical abstracts without associating specific labs with specific results. This is a comfortable and nonconfrontational way of doing things, and the idea is that labs whose own results are far away from the average result will take steps to get their act together without further prodding, whereas a public airing of inter-lab differences would just make people look bad, annoy them, and inhibit rather than increase cooperation.
However, this isn’t the most satisfying method from the user’s perspective. As a user I’d like to know how various labs perform so I can make a sensible decision about where to send samples. Thus Silke’s talk was extremely refreshing. I would like to see this exercise carried out in public more often.
However, it did bring up the important question of whether or not we should panic about this. If AMS labs analyse the same material and get results that vary by 10%, then actual exposure ages could be totally wrong by an additional 10% on top of production rate errors etc. If inter-lab differences were systematic, then PRIME Lab users would always assign moraines in New Zealand to the Younger Dryas, whereas LLNL users would find only the Antarctic Cold Reversal. This would be bad.
I don’t think things are that bad, for a couple of reasons. First, Silke’s results are not in agreement with other measurements, including some of the CRONUS rock sample intercomparisons, that were not as elaborate, and are hard to directly compare to these results, but produced more consistent results between labs than Silke suggests. Second, at most AMS labs this experiment only involved a couple of analyses of a couple of cathodes. Thus, measurement error hasn’t completely (or at all) been taken out of the experiment, which makes it hard to evaluate the results. This experiment would be much better if all labs were obligated to carry out a large number of analyses of each intercomparison solution.
Third, I am nearly certain that the Be-10 results at least are still contaminated by Be isotope ratio standardization errors. Remember, in making a Be isotope ratio measurement you are comparing the ratio in your sample to the ratio in a standard material with a defined isotope ratio. Get the defined ratio of the standard wrong and you get the sample wrong too. The problem here arises because different labs use different standard materials, and the assumed isotope ratios of these materials aren’t internally consistent. Thus, to properly compare Be isotope ratio measurements from different labs, you need to i) determine which standards they were normalized to, ii) determine what the assumed isotope ratios of those standards were, iii) determine (from an entirely separate set of experiments that may or may not ever have been conducted) whether the assumed isotope ratios for the standards are mutually consistent, and iv) if they’re not, correct the sample results accordingly before comparing them. This is extremely difficult to get right. When Silke distributed the samples, she told the receiving AMS labs to submit results that were normalized to a particular standard. However, given the fact that different labs use different assumed isotope ratios for this standard (and others) these instructions left, in my opinion, too much wiggle room, and it is nearly certain that the results in Silke’s data sent have not been consistently standardized. Silke’s instructions probably prevented apples-to-oranges comparisons, but some oranges are still probably being compared to grapefruit.
A better approach would have been to not specify a particular standardization, but to obtain from each lab the following pieces of information: i) the measured ratio of the sample, ii) the identity of the normalization standard used to make this measurement, and iii) the isotope ratio assumed for the normalization standard. With this information, it would be possible to ensure that internally consistent ratios were being compared, as well as to discard from the experiment any situations where adequate data to do the renormalization didn’t exist (i.e., if the two normalization standards in question had never been compared). Without this information, we continue to wonder if each datum is an orange or a grapefruit.
To summarize, I think Silke’s exercise was a very good thing to do. It is certainly embarassing to the cosmogenic-nuclide community that large differences appear to exist among AMS labs. Silke’s talk called much-needed attention to the issue and made AMS operators squirm a little. Unless anonymous intercomparisons are supplemented with fully reported public ones, labs risk having low credibility with the user community. More public intercomparison, more credibility. However, this experiment was not quite fair. If you’re going to stir up a storm of public opinion, you should do it with adequate data. Random measurement error should be taken out of the equation by standardizing the number of cathodes to be run (at a large number). More importantly, one needs to make damn sure all standardization issues have been sorted out before concluding that there really are unresolved sytematic differences. So we should do this again — send out intercomparison standards and make the results fully public — but we should do a better job next time.
A paper by Joerg Schaefer and numerous others, about exposure ages on Holocene moraines in New Zealand, came out in Science a couple of weeks ago. The overall point of this paper is that they exposure-dated a large number of Holocene moraines and discovered that Holocene glacier advances in New Zealand were neither synchronous or asychronous with Northern Hemisphere glacier advances. This is interesting from the paleoclimate perspective, and I’ve talked about why at some length in a commentary article in the same issue (you can get this article by clicking through this page).
From the perspective of cosmogenic-nuclide exposure-dating nerds, there are some other interesting features to this article that are much too obscure for the general Science readership. Thus, commentary here. Mainly, the Schaefer paper is notable because i) they measured a very large number of exposure ages, ii) they were very young exposure ages, and iii) they are very precisely measured. Items ii) and iii) mainly highlight hard work in the Lamont chem lab and impressive AMS skills at LLNL-CAMS, but i) is interesting because the size of the data set makes it possible to take a look at some of the beliefs that come into relating exposure ages of moraine boulders to the age of the glacier advance that formed the moraine.
Basically, when one measures the exposure age of a bunch of boulders on a particular moraine, they aren’t all the same. They differ, for three reasons. First, all boulders could have the same true exposure age but their measured exposure ages would still differ due to measurement uncertainty. Second, the boulders could have different true exposure ages because of post-emplacement moraine disturbance, that is, some boulders may have been uncovered, or had their surfaces eroded, after the moraine was abandoned. This is most likely not the primary issue for the very young moraines in the Schaefer paper. Third, some or all boulders could have had an “inherited” exposure age when they were initially emplaced on the moraine, that was left over from some past period of exposure that the boulder experienced.
Mostly people deal with this issue by using some sort of a statistical test to determine whether or not the distribution of measured ages could be accounted for by measurement error alone. If their observed ages pass this test, then they can reasonably average the measured ages and argue that this number is really the true age of the moraine. The reduced chi-squared statistic is commonly used for this; this statistic compares the deviations of the measurements from their mean with the uncertainty of all the measurements and comes up with a summary statistic. If the value is approximately equal to 1, then the scatter in the measurements is about as expected from the measurement uncertainties. If it’s significantly larger (what “significantly” means depends on the number of data), then some other source of scatter is present, which implies that averaging the data probably does not give the true moraine age.
The interesting thing about the Schaefer data is that the reduced chi-squared value for exposure ages from a particular moraine increases — a lot — as the age of the moraine becomes smaller. That is, for the older moraines, the exposure ages are scattered about as much as one expects from measurement uncertainty — reduced chi-squared values are near one — but for the younger moraines, the scatter is much more than expected from measurement uncertainty alone. The following plot shows the relationship between mean moraine age and reduced chi-squared for the Schaefer data set.
So the question is, what source of scatter becomes more important as exposure ages get younger? Boulder surface erosion and moraine degradation cannot explain this effect: both of these processes would result in greater excess scatter in older, rather than younger, moraines. The obvious answer to this is cosmogenic-nuclide inheritance. Many if not most of the boulders on these moraines must have originated as supraglacial debris shed from cliffs above the glaciers, so they were exposed to the cosmic-ray flux for at least some time prior to transport and emplacement in the moraines. Thus, they must have contained some inherited Be-10 at the time they were delivered to the moraines. Of course, we don’t know how much. The advantage of this data set is that it enables us to estimate how much. So make two assumptions: first, all moraine boulders were emplaced at the same time and experienced simple exposure thereafter; second, all boulders contain inherited Be-10 whose concentration is variable, but obeys a uniform distribution between 0 and a maximum value. With these assumptions, the exposure age of a moraine boulder is:
Where t is the apparent Be-10 exposure age of a boulder (yrs; this is what we observe and is just the measured Be-10 concentration divided by the production rate); t_true is the true depositional age of the moraine (this is what we want to know); e(t) is a measurement error term (yr) which is normally distributed around zero and has a standard deviation equal to the 1-sigma measurement error of the apparent age; and t_i is an inherited Be-10 concentration, expressed as an age, which is uniformly distributed between 0 and a maximum inherited age t_i,max (alternatively, t_i is the inherited Be-10 concentration divided by the Be-10 production rate). By generating random values of t_i and e(t) that follow the specified probability distributions, we can simulate the apparent exposure age distributions we would observe on a moraine of a certain age. We can then repeat this experiment multiple times and look at the distribution of reduced chi-squared values we would expect for moraines of various ages and uniformly distributed inheritance.
One important thing is that the measurement uncertainty is a function of the age — older boulders have more atoms and hence lower measurement uncertainties. We need to account for this, which we can accomplish by using the relationship between age and uncertainty in the Schaefer data to estimate measurement uncertainties in our simulation. Here is the relationship:
The red dots are the actual measurements; the blue line is a model relationship that I will use in the simulation.
To get to the point, here is the result of a Monte Carlo simulation that predicts the relationship between moraine age and reduced chi-squared — the relationship that caught my attention in the first place — by repeatedly evaluating the equation above to generate synthetic apparent age distributions, and then computing their reduced chi-squared values. The only free parameter left in our model is the maximum value of inheritance. It turns out that the value of this parameter that best reproduces the observed relationships is 200 years, that is,boulder inheritance is uniformly distributed between 0 and 200 yrs. The red dots are the data shown above; the solid blue line is the average value of the reduced chi-squared predicted in the simulation for a moraine of a particular age, and the dashed blue lines are the 1-sigma confidence bounds on that value.
Clearly this does a pretty good job of reproducing the observed striking relationship between reduced chi-squared and moraine age. For comparison, the next figure shows the result for 0-200 years (blue) compared with the results for 0-100 (red) and 0-300 (green) years:
So the summary of this all is that an extremely simple model for inheritance enables us to i) very precisely reproduce the striking relationship between moraine age and excess age scatter evident in the Schaefer data set, and ii) quantitatively estimate the mean inheritance in the boulders. To summarize, the average value of inheritance in these moraine boulders is most likely near 100 yrs.
The authors of the paper actually tried to estimate inheritance in a different way by dating several boulders on a historically observed moraine that was known to have formed ca. 1860-1895, i.e. 100 years ago. Several boulders from this moraine had apparent ages scattered between 150-200 yr, indicating inheritance of 50-100 yr. Which estimate is better? Both are consistent; a few values drawn from a uniform distribution between 0-200 yr could easily fall between 50-100 yr. For the older moraines, it seems most sensible to subtract 100 +/- 60 (the mean standard deviation of a uniform distribution between 0-200) years from apparent exposure ages to arrive at a better estimate for the true age of the moraine.
Q: I have some Be-10 measurements made at ETH using their “S555″ standard. What should I enter for the Be-10 standardization in the version 2.2 entry page?
A: The ETH standards have now been added. See the standards page. Basically, the S555 standardization is very close to the KNSTD standardization.
