Singer’s Proxy Claim Refuted

An article by a grad student of my acquaintance at UT. Quote from another paleoclimate grad student in conversation “the deniers never hate on us the way they do the tree ring people, ’cause our data is solid”. Anyway, the original is here, and Kaustubh (a.k.a “Kow”) retains copyright.

 

Proxy Evidence for Recent Warming

Dr. Fred Singer visited the UT campus last week and gave a talk containing the usual climate denial yarns and I hear, most artfully (not!) dodged scientific questions. I wish I could’ve attended but unfortunately, I had a class at the same time. This post was motivated by the following claim of his in a WUWT post (in retaliation to the BEST results being publicized and unfavorable to his interests) which he rehashed in the talk as well:
And finally, we have non-thermometer temperature data from so-called proxies: tree rings, ice cores, lake and ocean sediments, stalagmites. Most of these haven’t shown any warming since 1940!

To put it simply: this is false.

Here, I have compiled a (very short) list of scientific articles (keeping the Manns and the Briffas i.e. tree rings away) where the authors do report recent warming in various proxy data. Ice cores, foraminifera, diatoms, stalagmites, corals and lacustrine & marine sediment cores compose some of the listed proxies. Not only do these different proxies around the world show a pronounced warming in the late 20th century, they are also useful in revealing the fossil fuel signature source of recently accumulating carbon dioxide (the Suess effect, see here and here) in the atmosphere. I will happily provide pdfs of any papers if they are requested and will add your favourite scientific article if suggested in the comments.

Proxy evidence for recent warming:

This is a very small subset of papers where authors report late 20th century warming via non-tree ring proxies. Coincidentally (or not), the marine sediment core that I am currently working on shows a large 20th century warming signal as well. In fact, I would place more trust in proxies than pre-satellite (pre~1950) or reanalysis data in accurately recording temperature and other climatic variables.

Summary: (to reiterate), Dr. Singer’s claim is false.


Pat Frank responds at Watts’:

Michael Tobis says, “Since Heartland is happy to pay people to say things about science that just aren’t true,…,” with the link pointing to a blog supposing that Patrick Michaels is so very dead wrong to be skeptical of non-tree-ring temperature proxies.

Well, Michael, presumably you can point us to the physical theory that will extract a physically valid temperature from a diatom shell, or a spleothem, a coral band, a sedimentary varve, or an ice-core ring. Physically valid is not just scale-it-to-a-measurement-trend-and-call-it-temperature statistical hokum. It’s not just we-can-measure-deuterium-and-18-O and never mind about the possible monsoon shifts or rainings out that are hiding behind the curtain. And it’s not just the ad hoc and tendentious assignment of temperature to the PC1 of a proxy qualitatively judged to be temperature limiting.

Where’s the falsifiable physical theory, Mike? Where are the physical equations that will transform a spleothem (ice core ring, coral band, varve, etc.) into a temperature? If you don’t have them (and you don’t), then Patrick Michaels is correct, Heartland is innocent of any wrong-doing, your champion is wrong, and so are you. Proxy so-called temperatures are not physically real. They have no physical meaning.

I am so tired of people who call themselves scientists all the while taking a thoroughly glaringly obviously facile pseudo-science and elevating it to holy writ. What is it with you people, that you hold your professional integrity so cheaply?


[ Kau replies on his blog as follows: ]

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A person by the name of Pat Frank on WUWT responded to this post by saying this. He claims that there is no physical theory backing up proxy reconstructions, that paleoclimate variables thus obtained are not physically real and that paleoclimatologists are guilty of “statistical hokum” by scaling a measurement to a trend and calling it temperature. This post is motivated by the aforementioned accusation.
First of all, let me start by pointing out the irony of this situation. Fred Singer (who is confused with Patrick Michaels by the WUWT commenter – get your facts straight… Oh wait…) was the person to claim that proxies do not show 20th century warming. He used this (false) hypothesis to claim that global warming was not happening. Therefore, it is clear that he puts faith in proxy reconstructions as he uses them to argue his point. Now, we have another denier claiming that proxy reconstructions have no physical meaning, which would nullify what Singer said in the first place! Oh the irony… In any case, let me bring you some scientific snippets (aka truth) on the topic.
Understanding Proxies
As you are all aware, a paleoclimate proxy is a tool that is used to infer geophysical variables from the past. Generalizing this concept, a proxy could be anything that reveals past information. For example, wet grass in your front lawn on a clear, cloudless, sunny morning tells you that it rained the night before. Despite not seeing or hearing the rain yourself, believing that it rained the night before is not a long shot. The fact that the previous night was a cloudy one can be inferred too. It is logical to subscribe to this stance because we have seen the grass become wet and seen clouds in the sky when it rains. But how can we be so sure that rain caused the grass to be wet? (What if it was a neighbor who accidentally watered your lawn? What if the grass was wet because a pack of dogs urinated all over your lawn last night?) There are ways to test this hypothesis, physically and statistically (Is the grass in the backyard wet too? What about the other houses in the neighbourhood? How likely is it that a pack of dogs could urinate uniformly over all the grass in the neighbourhood?) The philosophy behind proxy based reconstructions, just like geology, is rooted in uniformitarianism – the present is the key to the past. A chemical/physical measurement on a proxy variable (say, stable oxygen isotopes on a coral head that has grown for centuries) reveals a significant amount of information about past geophysical parameters as long as we know how the variable is affected by the relevant geophysical process (eg. the controls of temperature, salinity on the isotopes). Different proxy variables respond to different physical parameters and this can be tested, verified and validated by experiment. This procedure is rooted in physics and the scientific method.
The Physics of Proxies: Foraminifera & Stable Isotopes
Let me focus on a proxy that I am familiar with and well within my realms as a researcher to talk about: oxygen-18 isotopes in the calcium carbonate shells of planktic foraminifera. Foraminifera are small organisms that secrete calcium carbonate shells and live in the ocean. Oxygen-18, is a stable isotope (doesn’t undergo radioactive decay) of the more abundant oxygen-16 and contains two more neutrons than the latter (ie the atomic mass is more). The change in the ratio of 18O/16O in any system undergoing a physical/chemical process is termed as isotopic fractionation. We utilize mass spectrometers to measure this ratio of 18O/16O in the calcium carbonate of the small shells (reported as δ18O ‰ relative to a standard). We are sure of pinning down this measurement up to a very high precision (error ≈0.05‰ – an order of magnitude less than 0.05%, mind you).
Nobel laureate Harold Urey, in 1947, explained the behavior of these stable isotopes (18O) and their departure in chemical and physical properties from the more abundant isotope (16O), arising from a difference in atomic mass in his landmark paper, The Thermodynamic Properties of Isotopic Substances (Journal of the Chemical Society, 1947). He discovered that temperature is the dominant control on isotopic fractionation.
As a simple analogy, consider the oxygen you are breathing in right now – it is not pure 16O2. It is a mixture of the molecules 18O-16O, 18O-18O & 16O-16O – quantified by a certain 18O/16O ratio or δ18O. If you isolated it (closed system) and subjected it to a physical process, say liquefaction, isotope fractionation would occur. You would have a δ18O for the oxygen vapor and a different δ18O value for the liquid oxygen (similar to elementary vapor-gas equilibria studies).  Now, suppose you wanted to obtain different ratios for the vapor and liquid? How can this be achieved? Urey discovered that by increasing the temperature of the system, preferentially, lighter isotopes in the liquid phase would tend to go into gas phase and hence the liquid would be more enriched in δ18O and the gas would be depleted in δ18O (or more enriched with 16O). Of course, one could also change the ratio by introducing a stream of pure 18O-18O vapor or liquid, but then, the system would no longer be closed.
Amazingly, Urey predicted that paleotemperatures may be teased out of stable isotopic measurements of old carbonates utilizing this same principle. In the 50s, his student, Cesare Emiliani, carried out isotopic experiments on foraminifera shells and established quantifiable controls for this proxy in terms of a physical transfer function. When the CaCO3 is deposited by these creatures, the resultant δ18O is a function of the temperature at the time of fractionation. However since the system is not closed, the δ18O of seawater must also factor in – i.e. how much 18O is available for the organism in the first place? Foraminiferal δ18O is a function of temperature and the δ18O of the seawater at the time that it was deposited:
δ18Oforam = f(Temperatureseawater , δ18Oseawater)
In other words ONLY a change in temperature or a change in seawater δ18O can alter the δ18O ratio of foraminiferal calcite. If temperature and seawater δ18O stayed constant through time, the measured δ18O of would be constant too. This is not the case. Therefore, when we measure isotopes on foraminifera shells in a marine sediment core, and we see that they are not the same, we can infer that there had to have been a change in sea temperature or sea water δ18O (which is related to sea water salinity and ice volume). There is no doubt about this.

Since then, there have been thousands of experiments (laboratory based, culture experiments, sediment traps) to accurately quantify these estimates and to pin down uncertainties – 60 years is a long time! Even though quantitative estimates are refined every now and then due to progress in mass spectrometry and understanding the biology of these creatures, qualitative inference (trends, variability) of foraminiferal proxy records from as far backas the 50s still holds true (Milankovitch cycles, ice ages etc.)

In summary, a measurement in a geological artifact (speleothem isotopes, fossil content, paleosols composition, tree-rings width, ice-core bubble makeup etc.) known to respond to a climatic parameter (temperature, humidity, precipitation, pCOetc.) in the present is utilized as a proxy for the past. These proxy measurements are independently verified and statistically validated by robust methods of comparison with instrumental data and should have a sound physical reason as to why they change with aforementioned climate parameter (correlation does not imply causation); only then are proxy reconstructions and their inherent quantitative and qualitative implications accepted by the community. Nobody merely matches trends and principal components of empirical orthogonal functions to a random measurement in an unknown fossil as was accused.

The Physics of Proxies: The Literature
There are plenty of articles in the literature that describe the physical basis of each proxy in great detail. Here I have provided a (few) links to articles in the literature as an example of the scientific scrutiny through which a proxy is put through before it is used for reconstructing geophysical parameters. Note: I have only included a few proxies off the top of my head. Feel free to include your favourites in the comments.

 

Take Home Message

Climatic proxies (including stable isotopes, trace metals, organic biomarkers) are based on sound, well-established, well understood thermodynamic, physical principles. With respect to isotopic reconstructions, whatever I have just explained in this post has been known for over 65 years! Stable isotopes play a huge role in the natural science world today. These principles are even used for oil exploration and in the petroleum industry! It is a shame that deniers cannot even perform a cursory google search before making nonsensical, non-scientific claims. Granted, there are proxies such as faunal assemblages where the mechanistic relationship of species diversity could be related to more than one parameter thereby complicating transfer functions and there are (new) proxies such as Tex86 paleothermometry where biological constraints aren’t fully understood. However, the real strength of proxies lies in how reproducible and repeatable the measurements are. So, you have reconstructed sub-annual sea surface temperatures from a coral head, what does another coral from another colony indicate? Ok, you have estimated paleotemperatures from isotopes in a marine core, how do Tex86 measurements from the same core correlate with those?
To state that paleoclimatologists don’t understand the fidelity of proxies is to be in denial. In fact, paleoclimatologists themselves are most critical of proxy measurements and their transferral into reconstructed variables. With advancing scientific progress in terms of instrumentation and new analytical techniques, new proxies are being developed as we speak. Harry Elderfield has an amusing graph regarding the confidence of newly proposed proxies:
 
Nobody is more critical of new proxies than paleoclimatologists/paleoceanographers themselves.
Taken from Elderfield, GCA (2002)
We paleoclimatologists are well within our right as scientists to state that proxies do indeed show a 20th century warming and this is with sound physical reasoning and not mere ‘statistical hokum’.

Mr Frank continues at Watts:

Michael Tobis, apologies for the Singer-Michaels mix-up.

You wrote, “this is an attack on the whole idea of proxies, which doesn’t directly respond to Singer’s claims that there is no proxy evidence,…

Michael, if the “proxies” are not proxies, then there is no proxy evidence. That’s pretty basic, and if you don’t get that, there’s no point talking further.

You say that, “the corals [produce] credible and globally coherent ENSO records,” but that’s not the point is it. The point is whether corals produce physical temperature records.

Corals respond to, e.g., temperature, precipitation, nutrient flux, and predation. How does anyone extract physically valid degrees centigrade from that? And yet, proxy temperature trends are authoritatively published with ordinates showing resolutions of 0.2 C. Those plots are scientifically meaningless. Worse, they reflect either disingenuousness or incompetence. There is no other choice. And honestly, I don’t think the answer is disingenuousness.

You asked, “Pat, is it your claim that there is no such thing as paleoclimate evidence?” Evidence of what, Michael? Warmer-wetter/cooler-drier? Or degrees centigrade? The degrees may be there, but we won’t know until there’s a physical theory with which to derive them. Or do you deny that?

You asked, “Is it your claim that there is no science without equations reducible to physics?” I claim there is no science without a falsifiable theory. Physics has them. Chemistry has them. Biology has them. Geology has them. Climate modeling does not. Neither does proxy temperature. It’s good to keep your science straight, Michael. And it’s neither naive nor solipsistic to pay attention to what is science and what most assuredly is not. Proxy thermometry is not science.

What MDs do is grounded in Biology. What engineers do is grounded in Physics. Nothing in either profession makes sense without the backing of their foundational science. One might argue empirical rules of thumb, but I promise you won’t make that case.

I’ve argued the proxy case at Steve McIntyre’s CA. Rob Wilson, a proxy professional, took issue. He had no good defense. Neither will your cadre. It’s all just associational arguments decorated with numerical filters and statistical arcana.

Proceed with your digging, Michael. The verdict won’t change.

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The referenced discussion at CA contains the following summary from Pat Frank:

Metabolic theory applied to trees certainly predicts temperature limited growth, but not quantitatively. There are no known metrics derived from trees that can be cranked through a biophysical theory to produce a growth temperature.

This quantitative theory plain does not exist, and no statistical methodology can ever produce a physically meaningful metric where there is no physical theory.

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[It's far from clear what that actually means, short of "there is no such thing as a proxy", or "nananana I am not listening".

Some other, somewhat more reasonable, or at least at-first-glance reasonable-sounding complaints from naysayers appear on that CA thread.  This one from Eschenbach,  for instance, one of the more coherent of the naysayers.

They seem to be obsessed with tree rings over on that thread, though, as is their usual MO.

Those who are new to the climate blogs be warned: any engagement with the tree ring obsession of McIntyre et al is likely to be a bottomless pit. This is the original red herring and they are still flinging it around. My sense is that, like Frank's clueless claim bolded above, it all boils down to denial, pure and simple. But I've never had the patience for it, since in my view tree rings are unimportant.

If someone else wants to write an informed tree ring piece, though, we're interested.

-mt]


Images: Coral cores used as temperature proxies. Main page pic from Flickr user Derek Keats is in Creative Commons CC BY-SA 2.0

 

(borehole link)

Comments:

  1. There are several others not listed here.

    Paleoclimate proxy perspective on Caribbean climate since the year 1751: Evidence of cooler temperatures and multidecadal variability. 2008. Kilbourne et al. Paleoceanography. doi:10.1029/2008PA001598

    Assessing between-colony oxygen isotope variability in the coral
    Porites lobata at Clipperton Atoll. 1999. Linsley et al. Coral Reefs. 18:13-27.

    Reconstructing twentieth-century sea surface temperature variability in the southwest Pacific: A replication study using multiple coral Sr/Ca records from New Caledonia. 2007. DeLong et al. Paleoceongraphy. dpi: 10.1029/2007PA001444

    Late 20th century warming and freshening in the central tropical Pacific. 2009. Nurhati et al. GRL. dpi: 10.1029/2009GL040270

    • Pat Frank replies on WUWT:

      ==

      Michael Tobis says, “Since Heartland is happy to pay people to say things about science that just aren’t true,…,” with the link pointing to a blog supposing that Patrick Michaels is so very dead wrong to be skeptical of non-tree-ring temperature proxies.

      Well, Michael, presumably you can point us to the physical theory that will extract a physically valid temperature from a diatom shell, or a spleothem, a coral band, a sedimentary varve, or an ice-core ring. Physically valid is not just scale-it-to-a-measurement-trend-and-call-it-temperature statistical hokum. It’s not just we-can-measure-deuterium-and-18-O and never mind about the possible monsoon shifts or rainings out that are hiding behind the curtain. And it’s not just the ad hoc and tendentious assignment of temperature to the PC1 of a proxy qualitatively judged to be temperature limiting.

      Where’s the falsifiable physical theory, Mike? Where are the physical equations that will transform a spleothem (ice core ring, coral band, varve, etc.) into a temperature? If you don’t have them (and you don’t), then Patrick Michaels is correct, Heartland is innocent of any wrong-doing, your champion is wrong, and so are you. Proxy so-called temperatures are not physically real. They have no physical meaning.

      I am so tired of people who call themselves scientists all the while taking a thoroughly glaringly obviously facile pseudo-science and elevating it to holy writ. What is it with you people, that you hold your professional integrity so cheaply?

      ===

      I would point out that 1) it was Singer, not to my knowledge Michaels and 2) this is an attack on the whole idea of proxies, which doesn't directly respond to Singer's false claims that there is no proxy evidence. (updated Feb 19) evidence of warming among the proxies.

      But that all said, the absurd attack on the whole concept is nevertheless worthy of a reply. (Unlike Kau and Chris, I am no expert on proxies, though I probably know more than them about statistics, which may turn out to be relevant). The results I have seen from corals are compelling in their capacity to reproduce a realistic and globally coherent ENSO signal, I can say that much. And I do know from my conversation with these guys that McIntyre celebrates coral records when they show a result that please him.

      But I hope that the experts will show up to say more about their specific proxies and how they are validated.

  2. Mr. Frank and his friends at WUWT could start with a little reading, I suppose, before spouting off. Here is a starter set:

    McCrea, J. M., 1950, On the isotopic chemistry of carbonates and a paleotemperature scale, Jour. Chem. Physics, 18, 849-857

    Epstein, S., Buchsbaum, R., Lowenstam, H., and Urey, H. C., 1951, Carbonate-water isotopic temperature scale, Geol. Soc. America Bull., 62, 417-426 (yeah, THAT Urey, http://www.nobelprize.org/nobel_prizes/chemistry/laureates/1934/urey-bio.html)

    Craig, H., 1961, Isotopic variations in meteoric waters, Science, 133, 1702-1703.

    Lea, D. W., Mashiotta, T. A. and H. J. Spero, 1999, Controls on magnesium and strontium uptake in planktonic foraminifera determined by live culturing, Geochim. Cosmochim. Acta, 63(16), 2369-2379.

    Rosenthal, Y., G. P. Lohmann, K. C. Lohmann, and R. M. Sherrell, 2000, Incorporation and preservation of Mg in Globigerinoides sacculifer: Implications for reconstructing the temperature and O-18/O-16 of seawater, Paleoceanography, 15, 135–145.

    ... Look, I could go on and on like this. Scientists have spent generations figuring out these physical, chemical, and biological relationships, and as graduate students earth scientists spend years getting up to speed just so they can then make a new contribution to some aspect of the field. The least these vocal critics could do is spend a minuscule amount of time getting themselves up to speed.

  3. @MT: Thanks for pointing out that comment. Here is a post on my blog that addresses 'Mr. Pat Frank's ignorance: http://paleowave.blogspot.com/2012/02/physical-basis-of-proxy-development.html

    @Kevin: You beat me to it!

  4. Wholesale character assassination much? Typical of the whole schmear machine that it attributes to the people it attacks its own characteristics.

  5. People who find Pat Frank's know-nothingism amusing may be further entertained by my previous run-in with him.

    He actually has published his view that (admittedly I am paraphrasing) climate as a phenomenon is entirely immune to science, and "therefore" the best estimate of sensitivity is that there isn't one.

    Watts seems to be promoting the hypothesis as well, these days.

    I remain unable to understand the syllogism. Put simply, even if we know nothing about the boat, why does that imply we can rock it as much as we want?

    So far as I can see, that argument is just stupid.

    But I try to stay as open-minded as I can. On the other hand, I have recently picked up a quote from Paul Hummer: "I always like to think I have an open mind. It's hard to test sometimes because I often have conversations with idiots."

  6. A funny thing is, that if you only accept temperature measurement based on first principles, neither liquid-in-glass nor semiconductor thermometers provide it...

  7. Posted at: http://planet3.org/2012/02/21/singers-proxy-argument-refuted/

    Kau and Dr. Anchukaitis, it was interesting that you each took recourse to stable isotope proxies in constructing your replies to the point about the lack of science in proxy paleo-thermometry. Your reply is irrelevant to the point I was making, as will be shown.

    But your comments provide an opportunity to discuss O18 as applied to proxy temperature reconstruction, and especially to paleotemperatures. I’ve gone through a representative set of O18 papers to evaluate the temperature resolution of the method; something that I will show is thoroughly ignored in paleoproxy temperature reconstructions.

    Let’s start with the classic: J. M. McCrea (1950) "On the Isotopic Chemistry of Carbonates and a Paleotemperature Scale" J. Chem. Phys. 18, 849-857. McCrae studied the dO18 in waters from East Orleans, MA, on the Atlantic side of Cape Cod and at Palm Beach, Florida. He wrote this:

    “The respective salinities of 36.7 and 32.2%o make it not surprising that there is a difference in the oxygen composition of the calcium carbonate obtained from the two waters at the same temperature. (bold added)"

    As you know, salinity affects evaporation and/or may reflect an influx (or lack) of fresh water (by precipitation, riverine, or runoff). Evaporation and fresh water fluxes can affect marine O16/O18 ratios, so that waters of the same temperature may have differing O18 fractions.

    From McCrae’s Figure 5, and his T:dO18 relationship for 36.7%o and 32.2%o salinity: waters that contain the same 18O %o, can produce a different calculated temperature of 3.3 C, with the error caused by disparate salinity.

    That means if one generates a paleotemperature by applying a specific dO18:T relationship to paleocarbonates, and one does not know the paleosalinity, the derived paleotemperature can be mistaken by as much as 3 C.

    This shows the effect of historically invisible confounding influences on T:dO18 proxy reconstructions, and explicitly refutes your claim, Kau, that, “ONLY a change in temperature or a change in seawater δ18O can alter the δ18O ratio of foraminiferal calcite. If temperature and seawater δ18O stayed constant through time, the measured δ18O of would be constant too.

    Further than that, though, it was straightforward to take McCrae’s data for Cape Cod and Florida in his Table X, replot it, and determine the methodological point scatter due to systematic error. Here are the fitted equations I obtained:
    Florida: dO18%o = 1.57*(10^4/T)-53.9, r^2=0.994,
    Cape Cod: dO18%o = 1.64*(10^4/T)-57.4, r^2=0.995,
    where T is in Kelvins. These equations are virtually identical to McCrae’s.

    From those plots one can use the fit residuals to evaluate the point scatter due to systematic error in the method itself. These errors were (+/-)1 C for the Florida data and (+/-)1.5 C for the Cape Cod data.

    Have you ever done such a thing, Kau? It’s something a professional in the field should have done while investigating the resolution of the method s/he’s using.

    Your claim about the stability of foraminiferal dO18 ratios also shows that you’re unfamiliar with the work of Bemis, et al., 1998, which discusses the artifacts introduced into foraminiferal dO18 by photosynthetic symbionts. See below.

    The rms average measurement error in McCrae’s method, of (+/-)1.8 C, emerged under ideal laboratory conditions, where the water temperature was independently determined and the marine O18 fraction was directly measured.

    These are direct methodological systematic errors that should be propagated into any proxy reconstruction of temperature. However, they are invariably neglected. I’ll give an example below.

    Another methodological classic: James R. O'Neil, Robert N. Clayton, and Toshiko K. Mayeda (1969) "Oxygen Isotope Fractionation in Divalent Metal Carbonates" J. Chem. Phys. 51(12), 5547-5558.

    Figure 1 gives the measured relationship between temperature and dO18 in calcium, strontium, and barium carbonates, over the range 0-500 C. Focusing on the calcium data as paleoproxy relevant, the replotted data yielded the fitted equation: 1000*ln-alpha = 2.78*(10^6/T)-3.35, r^2=0.9996, where alpha is a dO18 fractionation factor. My fitted equation again is virtually identical to the published equation.

    Over the whole 0-500 C range, the point scatter about the fit yielded an estimate of average systematic error in T =(+/-)29 C.

    More relevant to SST’s, I evaluated point scatter in the 0-200 C data separately, getting the fitted equation: 1000*ln-alpha = 2.74*(10^6/T)-2.77, r^2=0.99999. This yielded a systematic error in T = (+/-)5.6 C, which would be approximately relevant to a proxy T:dO18 study.

    These systematic errors again accrued under ideal laboratory conditions.

    Next paper: Bemis, B. E., H. J. Spero, J. Bijma, and D. W. Lea (1998), Reevaluation of the oxygen isotopic composition of planktonic foraminifera: Experimental results and revised paleotemperature equations, Paleoceanography, 13(2), 150–160.

    This paper is particularly valuable because it reviews the earlier equations used to model the T:dO18 relationship. In discussing previous models, they note (p. 150) that, “Although most of these temperature:d18O relationships appear to be similar, temperature reconstructions can differ by as much as 2 C when ambient temperature varies from 15 to 25 C."

    That “2 C” reveals a higher level of systematic error that appears as variations among the different temperature reconstruction equations. This error should be included as part of the reported uncertainty whenever any one of these methods is used to determine a paleotemperature

    These methodological variations are due to confounding factors such as salinity and, as it turns out, the activity of photosynthetic foraminiferal symbionts.

    Bemis, et al., discuss this problem on page 152: "Non-equilibrium d18O values in planktonic foraminifera have never been adequately explained. Recently, laboratory experiments with live foraminifera have demonstrated that the photosynthetic activity of algal symbionts and the carbonate ion concentration ([CO32-]) of seawater also affect shell d18O values. In these cases an increase in symbiont photosynthetic activity or [CO32-] results in a decrease in shell d18O values. Given the inconsistent SST reconstructions obtained using existing paleotemperature equations and the recently identified parameters controlling shell d18O values, there is a clear need to reexamine the temperature:d18O relationships for planktonic foraminifera."

    Bemis, et al.’s comment again refutes your above-noted “ONLY” point, Kau.

    Bemis, et al., evaluated the effect of foraminiferal photosynthesis on T:dO18 under different light intensities. Using the same methods as noted above, I evaluated the methodological systematic error in the ambient high light (HL) and low light (LL) T:dO18 data, shown in their Figure 1.

    These were: HL 1-sigma T error = (+/-)1.0 C; LL error = (+/-)1.4 C.

    When the inter-methodological (+/-)2 C noted by Bemis, et al., is added as the rms to the average (+/-)1.25 C measurement error from the work of McCrae 1950 and Bemis 1998, the combined 1-sigma error in determined T =(+/-)sqrt(1.25^2+2^2)=(+/-)2.4 C.

    That (+/-)2.4 C is the minimal reportable methodological error in any dO18 proxy paleotemperature reconstruction, apart from invisible environmental confounding effects such as monsoon shifts.

    That minimum of error is already 3x larger than the commonly accepted centennial climate warming, and makes T:dO18 proxies entirely unable to determine whether the present warming is in any way historically or paleontologically unusual in rate or magnitude.

    Another standards paper: Kim, Sang-Tae; O'Neil, James R.; Hillaire-Marcel, Claude; Mucci, Alfonso (2007) Oxygen isotope fractionation between synthetic aragonite and water: Influence of temperature and Mg2+ concentration" Geochimica et Cosmochimica Acta 71(19) 4704-4715

    From the error width of the equation shown in Figure 5, the uncertainty in calculated T in the center of their data range, at 1000*ln-alpha = 30.00 is (296.74-292.06) = 4.68 C =>(+/-)2.3 C.

    Another standards paper: Hong-Chun Li, Lowell D. Stott, and Douglas E. Hammond (1997) "Temperature and Salinity Effects on O^18 Fractionation for Rapidly Precipitated Carbonates: Laboratory Experiments with Alkaline Lake Water" Episodes 20(3), 193-198. Episodes is here, but no content is available.

    Laboratory precipitation of calcite: the residuals from the linear fit to plotted T:dO18 data from Table 1 yielded a systematic 1-sigma error in temperature = (+/-)2.2 C.

    Likewise, Gerald M. Friedman (1998) "Temperature and salinity effects on 18O fractionation for rapidly precipitated carbonates: Laboratory experiments with alkaline lake water —Perspective" Episodes 21:97–98

    Laboratory precipitation of aragonite: the residuals from the linear fit to plotted T:dO18 data digitized from Figure 2 yielded a systematic 1-sigma error = in temperature (+/-)1.1 C.

    Let’s summarize:

    Study______________(+/-)1-sigma systematic uncertainty in T
    McCrae_______________(+/-)1.8 C
    O’Neil________________(+/-)5.6 C
    Bemis________________(+/-)1.7 C
    Bemis________________(+/-)2 C (inter-methodological)
    Kim__________________(+/-)2.3 C
    Li____________________(+/-)2.2 C
    Friedman______________(+/-)1.1 C

    These are all laboratory studies, done under controlled conditions with waters of known salinity and pH. In total, these results demonstrate that significant systematic uncertainties exist in derived 18O temperatures due to methodological inaccuracy.

    These show that a methodological uncertainty of at least (+/-)2 C should be propagated into any T:dO18 proxy reconstruction of paleotemperature. This uncertainty is in addition to the higher level inter-methodological uncertainty of another (+/-)2 C that apparently stems from historically confounding environmental variables.

    Now let’s look at Keigwin’s justly famous Sargasso Sea dO18 proxy temperature reconstruction: (1996) “The Little Ice Age and Medieval Warm Period in the Sargasso Sea” Science 274, 1503-1508 This isn’t meant as a general criticism, however, the reconstructed Sargasso Sea paleotemperature rests on Globigerinoides ruber calcite. G. ruber has photosynthetic symbionts, which induces T:dO18 artifacts as mentioned by Bemis, et al. To his credit, Keigwin attempted to account for this by applying an average G. ruber correction. But corrections of an average bias are valid only when the error envelope is normal, i.e., typically when the error is random. Subtracting the average bias of a systematic error does not remove the over all uncertainty, and may even increase the total error. Keigwin also assumed an average salinity of 36.5%o throughout, which may or may not be valid.

    More to the point, no temperature errors are reported. Keigwin wrote of apparent changes in paleotemperature of 1 C or 1.5 C, implying a temperature resolution with errors smaller than these values.

    However, we’ve seen above that the T:dO18 methodological systematic errors alone amount to about (+/-)2.4 C, with confounding artifacts of paleo-variations in salinity, photosynthesis, and meteoric water being invisible but perhaps of analogous magnitude in any reconstruction of paleotemperatures.

    In summary, Kau, both you and Kevin have completely neglected the uncertainties that accrue due to methodological errors and inaccuracies. This neglect is rife throughout the climatological literature dealing with recent climate warming. See here (calculations here), here, and here (~1 Mb pdf downloads), for some of my work demonstrating the pervasiveness of this neglect.

    It’s true that the T:dO18 relationship is soundly based in physics. However, it is not true that the relationship has produced a reliable high-resolution proxy for paleotemperatures. You’re supposed to be working exactly on this stuff, Kau, why don’t you know the resolution limits of the method you’re using?

    Kevin is a dendroclimatologist, though, and so maybe wasn’t aware of the significant methodological limits to the resolution of T:dO18 temperature reconstructions.

    My next post will discuss the standard proxy paleotemperature reconstructions, and show exactly why they are not science.

    • Pat, I am no expert in this field at all, but you appear to be confounding the issue of absolute temperature determination with the calculation of temperature *anomalies* - differences from one point in time to another. It seems unlikely, for example, that the salinity of a particular ocean location will change dramatically from one period to another unless the two time periods are separated by tens of millions of years (through moving continents) or there's some extraordinary temporary event (such as the emptying of a large glacial lake) just before one of the two measuring points.

      Random or periodic changes in salinity (for example) would have no effect on temperature measurements through this mechanism as long as individual measurements correspond to a long enough interval.

      But if you firmly hold that you have a significant conclusion on this somewhat esoteric topic, the place to have that conclusion tested is in the published scientific literature - that's what peer review is all about, to provide a mechanism for an adjudicated evaluation and judgment of your argument by experts. You won't get that here, unfortunately, or anywhere else on a blog that I'm aware of.

  8. Now onto the standard proxy paleotemperature reconstructions. I’ve gone through a representative set of seven high-status studies, looking for evidence of science. That is, whether any of them make use of physical theory.

    Executive summary: none of them are physically valid. None of them yield a temperature.

    Before proceeding, I need to insert a short discussion of your claim, Kau, that proxy thermometry relies on the same principle of uniformitarianism as Geology.

    The uniformitarianism of Geology – the modern version, anyway – is that the physical processes affecting the morphology of Earth are the same today as they have been throughout geological history. Therefore, the same physical theories apply to the past as to the present. So far, that hypothesis has been fully borne out.

    However, that is not the sort of uniformitarianism that is brought to bear in proxy thermometry. In tree ring thermometry, there is the explicit assumption that tree growth correlating with recent temperatures also correlate with past temperatures. This is not an assumption of uniform process. It’s an assumption of uniform conditions and uniform response.

    It’s as though Geology claimed that, e.g., the flow of the Colorado River was identical in all past times to what we observe it to be today. That assumption is prima facie unreasonable.

    The same assumption is far too often applied in T:dO18 proxy thermometry. The conditions of carbonate deposition, as opposed to the physical process, are assumed to be unchanging so that dO18 reflects only delta-T. This assumption is clearly unwarranted.

    So, your equation of principle is misplaced. You’re using the same word, uniformitarianism, but the meaning is different. The word doesn’t describe the same state in Geology and Paleothermometry. Your usage is misleading and wrong.

    That said, here we go; proxythermometry:

    1. Thomas J. Crowley and Thomas S. Lowery (2000) "How Warm Was the Medieval Warm Period?" Ambio Vol. 29(1), 51-55.

    Fifteen proxies: three were 18-O, 8 tree-ring, the Central England temperature record., and 3 of other provenance.

    Among the O18 proxies were Keigwin’s Sargasso Sea proxy, GISP 2 dO18, and the Dunde Ice cap dO18 series.

    Among the physically valid series: dO18 and CET series, there was complete and utter neglect of the physical uncertainty in the derived temperatures. Without any physically valid uncertainty limits, the physically valid series have no meaning.
    There is no physically valid way to turn tree rings into temperature. The theory does not exist, and there are no physically viable relationships between temperature and tree ring widths or densities. Tree rings are converted to temperature numbers using strictly statistical and numerical methods that have no grounding in science.
    All fifteen series were numerically adjusted to a common scale (Figure 1), appended to the measurement record (Figure 4) and granted a resolution of 0.05 C.
    Physical content: minimal. Physical validity: none. Temperature meaning of the final composite: none.

    2. Timothy J. Osborn and Keith R. Briffa (2006) The Spatial Extent of 20th-Century Warmth in the Context of the Past 1200 Years Science 311, 841-844

    Fourteen proxies, 11 of them tree rings. One dO-18 ice core (W. Greenland). The ice core dO18 was used with neglect of any uncertainty in temperature.

    Proxies were normalized, scaled into the measurement record, and published with a resolution of 0.05 C (Figure 4).

    Physical uncertainty in T: none.
    Physical meaning of the 0.05 C divisions: none.
    Physical temperature meaning of the composite: none.

    3. Michael E. Mann, Zhihua Zhang, Malcolm K. Hughes, Raymond S. Bradley, Sonya K. Miller, Scott Rutherford, and Fenbiao Ni (2006) Proxy-based reconstructions of hemispheric and global surface temperature variations over the past two millennia PNAS 105(36), 13252-13257.

    A large number of proxies of multiple lengths and provenances, statistically correlated with local temperature during a "calibration period," adjusted to equal standard deviation, scaled into the instrumental record, and published with a resolution of 0.1 C (Figure 3).

    Physical uncertainty in T: none.
    Physical meaning of the 0.1 C divisions: none.
    Physical temperature meaning of the composite: none.

    4. Rosanne D’Arrigo, Rob Wilson, Gordon Jacoby (2006) "On the long-term context for late twentieth century warming" J. Geophys. Res. 111 D03103 (1-12)

    Tree ring series from 66 sites, variance adjusted, scaled into the instrumental record and published with a resolution of 0.2 C (Figure 5 C).

    Physically valid temperature uncertainties: none
    Physical meaning of the 0.2 C divisions: none.
    Physical meaning of tree-ring temperatures: none available.
    Physical temperature meaning of the composite: none.

    5.Anders Moberg, Dmitry M. Sonechkin, Karin Holmgren, Nina M. Datsenko and Wibjörn Karlén (2005) "Highly variable Northern Hemisphere temperatures reconstructed from low- and high-resolution proxy data" Nature 433, 613-617

    Eighteen proxies: Two d-O18 SSTs (Sargasso and Caribbean Seas foraminiferal d-O18, and one stalagmite d-O18 (Soylegrotta, Norway), seven tree ring series. Plus other composites.

    The proxies were processed, combined, variance adjusted and intensity scaled to the instrumental record over the calibration period, and published with a resolution of 0.2 C (Figure 2 D).

    Physical uncertainties propagated from the dO18 proxies into the final composite? No.
    Physical meaning of the 0.2 C divisions: none.
    Physical temperature meaning of the composite: none.

    6. B.H. Luckman, K.R. Briffa, P.D. Jones and F.H. Schweingruber (1997) "Tree-ring based reconstruction of summer temperatures at the Columbia Icefield, Alberta, Canada, AD 1073-1983" The Holocene 7, 375-389

    Sixty-three regional tree ring series, plus 38 fossilwood series; used a pre-existent numerical (not physical) calibration function to convert tree rings to temperature, appended to the instrumental record, and published at 0.5 C resolution (Figure 10).

    Any physically valid methodology? No.
    Temperature meaning of the proxies: none.
    Physical temperature meaning of the composite: none.

    These six studies are typical, and representative of the entire field. Proxy thermometry as commonly practiced is a scientific charade.

    7. Michael E. Mann, Scott Rutherford, Eugene Wahl, and Caspar Ammann (2005) "Testing the Fidelity of Methods Used in Proxy-Based Reconstructions of Past Climate" J. Climate 18, 4097-4107

    This is, in part, a methodological review of the recommended ways to produce a proxy paleotemperature made by the premier practitioners in the field:

    Method 1: “The composite-plus-scale (CPS) method, "a dozen proxy series, each of which is assumed to represent a linear combination of local temperature variations and an additive “noise” component, are composited (typically at decadal resolution;...) and scaled against an instrumental hemispheric mean temperature series during an overlapping “calibration” interval to form a hemispheric reconstruction. (my bold)"

    Method 2, Climate field reconstruction (CFR): "Our implementation of the CFR approach makes use of the regularized expectation maximization (RegEM) method of Schneider (2001), which has been applied to CFR in several recent studies. The method is similar to principal component analysis (PCA)-based approaches but employs an iterative estimate of data covariances to make more complete use of the available information . As in Rutherford et al. (2005), we tested (i) straight application of RegEM, (ii) a “hybrid frequency-domain calibration” approach that employs separate calibrations of high (shorter than 20-yr period) and low frequency (longer than 20-yr period) components of the annual mean data that are subsequently composited to form a single reconstruction, and (iii) a “stepwise” version of RegEM in which the reconstruction itself is increasingly used in calibrating successively older segments. (my bold)"

    CPS: Assumed temperature correlation; statistical scaling into the instrumental record; methodological correlation = causation. Physical validity: none. Scientific content: none.

    CFR: Principal component (PC) analysis is a numerical method devoid of intrinsic physical meaning. Principal components are numerically, not physically, orthogonal. Numerical PCs are typically composites of multiple physical signals of unknown magnitude. They have no singular physical meaning. Quantitative physical meaning cannot be assigned to PCs by reference to subjective judgments of ‘temperature dependence.’

    Scaling the PCs into the temperature record is merely another method of a scientifically invalid and assumed correlation = causation error.

    ‘Correlation = causation is possibly the most naive error possible in science, and serves as the basis of the entire field of tree ring proxy thermometry.

    Proxy thermometry as ubiquitously practiced: composites are made that rely entirely on qualitative judgments of temperature sensitivity plus numerical scaling, statistical calibrations and normalizations, and/or CPS or CFR methodologies.

    Statistical methods: 100%.
    Physical methods: nearly zero (stable isotopes excepted).
    Physical meaning of the numerically scaled composites: zero.

    By the way, Michael Mann’s “climate field:” a term misusing concepts from classical and quantum physics. It’s calculated to seem to mean something, but doesn’t mean anything. It has no basis in climate physics.

    • Pat, there is a long history of using statistical methods in science to eke out the complex causal relationships in systems. Almost the entire field of chemistry (other than quantum chemistry calculations) can be summed up as "statistical methods: 100%", "physical methods: nearly zero". That does not mean the entire physical meaning of the field of chemistry is zero, as your argument would claim. Far from it.

      The same is true in physics - "phenomenology" is widely used - even in particle physics that ought to be closest to first principles. It is only in extraordinarily rare cases that any sort of closed-form formula can be found to express the behavior of one variable of a physical system in terms of other causative variables. That does not make a statistical phenomenology approach any less physically valid - far from it. As long as there is a real causative physical relationship known, and you have a good reason to believe you have accounted for all the other important variables, statistically-measured phenomenology is almost the only way we know anything for sure about the world.

      I think your approach would deny "physical meaning" to most of engineering as well. Hardly an auspicious argument to pin your hat on.

  9. Michael, your immune to science paraphrase is so wrong I am led to surmise you never read the Skeptic article you're criticizing.

    About climate sensitivity, I was there when you fled Steve McIntyre's blog after he challenged you to produce a derivation of the standard version of it.

    Regarding your boat argument, where's the valid evidence that we're rocking it at all?

  10. I think I shall coin a word for the anti-climatology crowd. It is agnotropism. They don't just profess ignorance. They seek to defend and expand ignorance. They consider ignorance their friend.

    It is possible to take an agnotropic approach to the literature, celebrating every source of noise without paying attention to how the noise is constrained, celebrating every disagreement while ignoring how the disagreements are settled, confounding every discipline rather than understanding where the boundaries are useful and why.

    Kau or other paleo people may or may not pick up the thread, but regardless, readers should not be fooled.

    I am familiar with Mr Frank's M.O. from our previous run-in. He quotes chapter and verse to prove that we don't know what we are talking about. But he proves only that HE doesn't know what we are talking about and that if we follow his approach we will learn nothing.

    Typically, scientists seek paths to extract knowledge. Paths to obscure knowledge are easy to find and can be developed by amateurs. The question is why they do this.

    • It's not my turf, P. Frank.

      I wasted enough time on you when you wandered into areas where I'm an actual expert to have much expectation that this might prove fruitful.

      Maybe somebody else will take it up. You can be sure I'll let Kau know next time I see him.

  11. Your turf or not, Michael, you chose to answer a serious post with insults. You could have responded intelligently, but didn't. After all, you invited me here.

    Your ethics also pretty much failed the test in our conversation about my Skeptic article at your personal blog site. You closed that off with an insult, too, after being unable to carry your position.

    Likewise here -- your comments appear to show that you have no respect for, or understanding of, the meaning and consequences of measurement accuracy and its lack.

    I left a heads-up at Kau's blog, by the way, but it didn't make the light of day. Moderator intervention, I guess.

    • You have a point. I rather foolishly did invite you over here.

      But this obviously isn't the spirit of inquiry. This is debate in the high school debating club sense. (Whoever thought to teach that skill to children instead of teaching reasoning skills deserves a special circle in hell. I am sorry you are among its victims.)

      My motivation is to keep the site interesting, honest, pleasant and engaging. If you try to engage in conversation, you are welcome here, whether we agree or not.

      If you are trying to score points, you have come to the wrong place. We are trying to think, here, together.

      It's true, I did invite you here. But the idea is to engage in discourse. It seems you prefer to substitute barratry. Converse and you are welcome to stay. Continue to wield references like a broadsword, and your contribution is nil.

      So, on the matter at hand:

      I think Arthur's point is compelling. We are not looking for T, we are looking for dT at a specific specimen. Note that biases will cancel out in this case.

      I've seen the coral guys' stuff. It's impressive. You can pick out ENSO cycles coherently at sites at opposite ends of the Pacific without much of a struggle.

      I have no interest in your wall of text and reference-weapons if you can't actually explain yourself.

      So. 1) Is there 4 per mil variance at a particular coral specimen on coral time scales?

      2) Explain to me how corals can extract a spatiotemporally coherent El Nino/La Nina signal resolving individual events, if there is 3 degrees of slop.

      3) When did you start studying corals? Is it a sheer coincidence that Kau picked the one corner of paleoclimatology that you are especially expert on? Or did you in fact just start collecting papers on the subject last week?

      If it's the latter, how much faith should I put into your reading of the papers? On what basis? What coral experts have you consulted?

    • Michael, given the analytical content of my posts, it's inconceivable how you can surmise that, "It seems you prefer to substitute barratry." That accusation is false on the obvious evidence.

      As I pointed out to Arthur, systematic errors do not cancel unless the error is known to be constant through the data set. The dO18 systematic measurement errors do not fall into that category, by the analytical evidence given in my post and in the associated references.

      By the way, neither do the systematic measurement errors in the surface air temperature record. So far as they are known, they're not constant and not Gaussian.

      Your questions about corals and ENSO might be relevant if you could show that the variations in corals are due entirely to the effects of temperature.

      I have explained myself thoroughly by demonstrating the analytical errors present in published dO18 measurements. More than that is hardly necessary, because the errors establish the point that proxy dO18 is presently and clearly incapable of resolving even (+/-)1 C.

      That is as true of the modern coral record as it is of the paleo-record, because both records use the same analytical methods and calibration equations to determine dO18.

      Apart from that, the proxy composites use the dO18 records in a non-physical way, jettisoning their original meaning. They're combined with other proxies using statistical methods and the composite is assigned to temperature by numerical scaling. It's not science.

  12. Arthur, I'm a professional experimental chemist. It is emphatically not true that Chemistry is statistics apart from "quantum chemistry calculations."

    Those calculations take their meaning from atomic theory; a falsifiable theory that has successfully passed extremely vigorous testing for more than a century, and that underlies the entire field.

    Everything I do is physical methods, and that means everything from weighing materials to spectroscopy. All of those operations take their meaning from physical theory. None of it is statistics.

    Statistical Thermodynamics, which plays such a huge part in elucidating atomic energetics, is grounded in Physics and is statistical only in analytical methodology.

    Statistics as such has a part to play in error estimation, assessing observational reliability, and, e.g., in the mathematical expression of Thermodynamics and Statistical Mechanics. But statistics as such does not provide the interpretative meaning of any branch of science.

    Physical meaning is given by physical theory. Modern engineering participates fully in that.

    In your argument about phenomenology in Physics, you have neglected the central point that any such phenomena are given meaning strictly by reference to an overarching and falsifiable physical theory. You go on to a serious misunderstanding of the point about temperature proxies, in particular tree ring proxies: there is no physical theory to give them any meaning, even in principle.

    There is no such theory of tree growth. Tree rings are empty of temperature meaning in the absence of that theory. There is no physical basis at all for normalizing them to the temperature record. The entire field is purely correlation = causation, falsely represented as science. And that makes it pseudo-science.

    • No, there's no claim of causation at all. If two signals are correlated, then each signal contains information about the other. Claiming otherwise is just silly.

    • And if two signals are merely associated, neither contains any information about the other.

      How does one distinguish association from correlation, Michael?

      • whuh?

        I have to defer to an old bon mot by Piet Hein here.

        You at least have to state your confusion clearly enough that there's something there to refute.

    • Tree rings and temperature, Michael. How does one demonstrate physical correlation rather than mere association?

      Statistical methods will not make that distinction.

      • What does "association" mean?

        If two series are correlated, each contains information about the other.

        Can you accept that? I can't imagine how you can't, as what I said is pretty much a tautology.

    • Pat Frank - spectroscopy is a perfect example of what I mean by phenomenology and statistics lying at the heart of chemistry - at least extending what I understand as the same argument you are applying to paleoclimatology. For the most part atomic and molecular spectra cannot be computed from any underlying physical theory because solving the quantum mechanical problems involved is too hard. We do have physically-based arguments that give an approximate view of the relevance of different energy scales so we know there should be rotational and vibrational transitions with their own energies and adorning any electronic transitions, and their should be other dependencies on for example magnetic fields, pressure, etc.

      That allows complex spectra to be understood through a process of parametrization - but each of those parameters (governing the gaps between different energy levels of the same type) cannot be obtained from an underlying theory, but must be found through measurements, for which statistics applies just as it does for any of these paleoclimate temperature proxies.

      I thought the whole point of this post was discussing non-tree-ring proxies and yet you insist on returning to tree rings, for which you assert "there is no such theory of tree growth". Well, there is plenty of literature on "plant growth theory" - do you claim that all such biological analysis is somehow wrong, because, why? It's not as well-founded as chemistry?

      Your claims are far-reaching and in the end seem to rest on no solid foundation whatsoever.

    • Michael, you wrote, "If two series are correlated, each contains information about the other."

      Not necessarily. They could each vary with an independent third agent and have no causal relationship with one another.

      Correlation is a statistical property of multiple number series. Causation reflects a dynamical physical relationship between two observables.

      In my Skeptic paper, for example, I pointed out Udny Yule's famous 0.95 correlation between mortality rates and Church of
      England marriages. Does that high correlation imply a binary causal interrelationship?

      Statistical false alarms are a well-known trap: Spurious correlations

    • Arthur, you're quite wrong in claiming that spectra cannot be calculated using quantum mechanics.

      Electron paramagnetic resonance (EPR) spectra have been regularly calculated since the 1960's. These days, physics-based freeware is readily available. QM as expressed in density functional theory is used to calculate UV-visible electronic spectra: for example.

      Density functional theory employs the same QM theory in calculations of x-ray absorption spectra (XAS). XAS is analogous to electronic absorption spectra, but at x-ray energies. Here's an example. It's thoroughly physics-based. A colleague of mine regularly uses DFT in this manner, and we expect to publish the calculated x-ray spectrum of a biologically important molecule in the near future, as part of the outcome of a joint project.

      Your claim about quantum chemistry being statistic-based couldn't be more wrong.

      My original point at WUWT was in reference to a claim posted there by Michael, which in turn pointed to this very post about Singer being refuted, which itself makes reference to tree ring proxies.

      When I made my reply at WUWT that statistical scaling can't produce a temperature, Michael posted my comment here. Kau and Kevin elected to defend proxythermometry strictly by reference to the dO18 stable isotope proxy.

      So, one might say they attempted to limit the debate to the best possible (for them) arena.

      Didn't work, though apparently you fell for the ploy.

      [ Eye of the beholder, like so much else in this half-mad world. -mt ]

    • Pat Frank - I didn't say spectra could not be calculated using quantum methods. Those calculations are just not the main focus of spectroscopy in chemistry, and it was essentially impossible before DFT methods were introduced about 20 years ago to the computational chemistry community (and with the advent of faster and faster computers the calculations became more feasible). You'll note my original comment stated chemistry was largely phenomenology "other than quantum chemistry calculations" - maybe quantum chemistry is more prevalent now than it was back when I worked in the field, but I don't believe even now it's what spectroscopists do most of the time - they make measurements and parametrize simple models, they don't work all the time from basic physical principles.

      And even DFT is an approximation with a lot of parameters that come from statistical fits of one sort or another (to theoretical calculations rather than to measurements - but the ultimate test selecting which functionals to use is in comparison to experiment). Core electrons are factored out with "pseudopotentials" for instance.

      In fact, I was involved in one of the early papers in this field with Ken Jordan:
      P. Nachtigall, K. D. Jordan, A. Smith, and H. Jonsson, J. Chem. Phys. 104, 148 (1996) "Investigation of the reliability of density functional methods: Reaction and activation energies for Si–Si bond cleavage and H2 elimination from silanes"

      where we compared density functional and cluster calculations. One of the interesting side-notes there was, my background being in physics I was initially using just the Kohn-Sham exchange-correlation function in the software we had worked on, and when we tried to compare numbers under the same conditions with output from Jordan's "Gaussian" code there was a significant discrepancy. Tracking it down it turned out the DFT code in Gaussian had used the wrong equation from the original 1965 Kohn-Sham paper - people had been using the wrong DFT functional for several years (no wonder there was at that time a widespread feeling among chemists that DFT didn't work well!)

      Anyway, no need for a long story - suffice to say I'm quite aware of what quantum chemistry is, and I don't believe I ever stated it was "statistic-based". But it is the only significant part of chemistry that is really founded in physics, and quantum chemistry isn't (or wasn't the last time I did any chemistry) most of what chemists do.

      And even there there is significant (computational) phenomenology involved (pseudopotentials! exchange-correlation functionals!) How do you calculate error-bars on your energy level calculations? And by the way, did you know that DFT is much better at finding energy level differences than absolute energies (systematic errors vanish when you take the difference).

      Michael Mann's approach (even back in 1998) to finding error bars in paleoclimate reconstructions is exactly the same approach that is used in many physical systems where there is a known physical relationship between variables that cannot be expressed in a closed mathematical form: Monte Carlo methods, i.e. statistics.

      Statistics, used properly, is a very powerful collection of techniques applicable across all fields of science. If you insist on dismissing paleoclimatology based on that argument, you dismiss along with it most of physics, chemistry, engineering, biology, etc. etc. I suppose it could be a self-consistent stance, but it's rather idiosyncratic. Reminds me of those mathematical physicists who struggle to define quantum theory in rigorous terms while the rest of us go merrily on our way ignoring the various mathematical subtleties and complications that make no difference to reality.

    • #12, Arthur, O-81 is measured using mass spectrometry. I assumed you knew that. Otherwise on what grounds could you claim the measurement is "exceedingly precise"? But it seems you didn't know and were winging your O-18 comments, just as you have very evidently been winging your badly misconstrued description of Chemistry and spectroscopy.

      As I already noted, my comments about accuracy were in the context of T:dO-18, not dO-18 analysis itself. Absent a real point, you're raising a diversion. I wouldn't assert large errors in O-18 determinations in any case, because I did O18 analysis during my post-doc and am familiar wit it. I was looking for O18 hydrogen peroxide uptake by the four-copper oxidase, Laccase.

      We assessed the results using O-18 dioxygen mass spec. The peaks of dioxygen O17-O17 and O16-O18 fraction are convolved at M/e=34 in experimental mass spectra. At the time, there was no general way to resolve the fractions. In the course of that work, working as a Chemist, I derived a thermodynamically valid expression to separate the convolved M/e=34 mass fractions in our mass spectra. A general theory-based solution, Arthur, not a parametrized simple model.

      You wrote that salinity varies directly with temperature, making salinity a direct proxy for temperature. You're wrong. Marine salinity in any one area also varies with meteoric water influx, the intensity of upwelling, surface wind-speed, wave-mixing, and the flux of fresh water run-off, all of which can vary with climate and often non-linearly. Go ahead and figure out a way to extract a pure temperature signal from salinity, and good luck to you.

      About this, "So I’m not sure you really have any case here at all, I tend to agree with you but only concerning the sureness of your understanding of the case. You've never actually engaged the case.

      Your uniformly unsuccessful attempts at mounting a debate have now gone off into non-issues. There's no real point of continuing.

      By the way, my reply to your #11 never made it into light here, but you can find it elsewhere.

    • Pat - you seem to have posted this as a reply on the wrong comment. I note that in your original comment you stated (addressed to me):

      most of my post on the dO18 proxy concerned experimental errors determining dO18 under controlled laboratory conditions. Those errors will also be present during use of the same methods to determine dO18 in fossil carbonates.

      to which I asked what I thought was a simple question:

      there should be very little error in “determining dO18″ – isotopic measurements are exceedingly precise. Perhaps you want to revise and state precisely what it is you are talking about?

      (note that mass spectra are only one of several ways to do isotopic analysis - I'm not familiar with the field sufficiently to know what's most commonly used).

      In your responses you have repeated the statement:

      my comments about accuracy were in the context of T:dO-18, not dO-18 analysis itself

      which is perhaps a clarification, but you have not walked back or clearly restated your original claim that you were mostly talking about "experimental errors determining dO18 under controlled laboratory conditions". Determining dO18 is a different thing than determining temperature based on dO18. Your two statements are to me clearly in conflict with one another. If you choose not to clearly restate the first, as you have with at least 3 opportunities so far, then it strongly appears to me you are deliberately making statements that are not founded in reality.

      As to your response on chemistry and spectroscopy over at WUWT (no idea what happened to your comment here, it must have been a browser problem, it's not in the comments database here at all) - you cite "valence bond theory, [...] molecular orbital theory, [...] crystal field theory, ligand field theory, self-consistent field and X-alpha method" - none of those are based on fundamental physics, they are all phenomenological theories that work quite well for chemists, but they are not directly derived from underlying physical theory except through very rough approximations and analogies. There is no mathematical expression of "valence bond theory" based on fundamental physics that allows you to calculate the energy levels of different bond configurations, excited states, etc - unless you go to direct quantum chemistry calculations (with DFT as an approximation).

      Paleoclimate analysis is little different from valence bond theory in its status as a scientifically valid but phenomenologically-based approach rather than something derived from first principles.

  13. Arthur, most of my post on the dO18 proxy concerned experimental errors determining dO18 under controlled laboratory conditions. Those errors will also be present during use of the same methods to determine dO18 in fossil carbonates.

    Calculating anomalies from absolute temperatures does not subtract away systematic errors, unless it is known the error is constant. The dO18 measurement errors do not behave as constants -- note the different magnitude of systematic error between the two determinations of McCrae, for example.

    Systematic errors propagate as their root-mean-square, which means that the uncertainty of an anomaly is greater than the uncertainty of the absolute temperatures used to calculate it.

    Apart from that, salinity and dO18 can change when monsoon tracks change due to fluctuations in climate. Such changes can last for a century or more. Monsoon changes mean changed inputs of meteoric water into the marine layer, with consequent changes in marine dO18.

    Foraminiferal or molluscan calcite dO18 can thus change with no change in SST, leading to mistaken derivations of T when a standard method is applied across the climatological boundary. The magnitude of that uncertainty can be estimated -- by measuring modern the variations in dO18 in areas known to have been through monsoon variations, for example -- and should be applied as a general uncertainty to any dO18 paleo-proxy.

    My estimates of dO18 systematic error are very straight-forward, Arthur, and come right out of, e.g., Bevington and Robinson, "Data Reduction and Error Analysis for the Physical Sciences." They hardly need peer-review to establish validity. There's nothing new in them except, apparently, that they've never been applied to dO18 measurements in the field of proxy paleo-temperature.

    But that's not altogether a surprise. Complete neglect of measurement error is pervasive throughout the entire field of AGW-climatology.

    Measurement error is one of those unpleasant gritty details of experimental science that prevents people from making grand sweeping pronouncements. And we can't have that when the world's at stake, can we.

    Thanks for your polite and thoughtful engagement.

    • "Systematic errors propagate as their root-mean-square, which means that the uncertainty of an anomaly is greater than the uncertainty of the absolute temperatures used to calculate it."

      Whoa, that's just seriously broken.

    • I demonstrated that point analytically here (1 Mb pdf download), under Section 2.

      The point that systematic error propagates as sqrt[(sum-over-scatter)^2/(N-1)] -- where N is the number of measurements -- follows from the fact that a degree of freedom is lost through the use of the mean measurement in calculating the systematic scatter. This is standard stuff.

      When an anomaly calculated using normal means and data that are contaminated with systematic error, the error in the anomaly is (+/-)sqrt[(error in normal)^2+(error in the measurement)^2].

      • You missed the "presuming uncorrelated error" part. Obviously. Which matters. Obviously.

        See, here is the evidence. You are not discussing anything at all.

        Either you are posturing, or blithering, or both. But you aren't engaging, which is exactly what I experienced when you tried to make points about stuff I am deeply familiar with.

        Presenting me with a wall of references in an unfamiliar topic is filibustering, not conversing.

        I would like you to convince me that, despite all odds, you really are an expert on the coral proxies you choose to dismiss out of hand. Failing that, I would like you to explain why a random selection of superficial information from the literature from somebody who's been thinking about it for a week should motivate me to dig up all those papers and figure them out. I'm not going to be quick to have somebody who's demonstrably wasted lots of other people's time waste my time.

        And in response you go around making elementary statistical errors in a tone of condescending pride.

        I'm singularly unimpressed.

    • Pat Frank - you claim that you were discussing "experimental errors determining dO18 under controlled laboratory conditions." but there should be very little error in "determining dO18" - isotopic measurements are exceedingly precise. Perhaps you want to revise and state precisely what it is you are talking about? Because, despite the flurry of words, the basics of what you are stating make no sense at all.

    • And regarding the RMS error issue Michael describes - this is exactly what I was getting at in my earlier comment. Taking a difference between two measurements made under the same conditions removes many sources of systematic error that would have been an issue with the single measurement. This is just as true for temperature proxies as for physical thermometers. The difference over time of temperature measured at a consistent location has much lower systematic error than the use of that single location's temperature as a proxy for the overall temperature of the region.

      Do you acknowledge that systematic errors are reduced using anomaly methods, or do you insist on asserting otherwise? Your argument appears to rest almost completely on this issue, if I understand what you're going on about in these many comments here.

    • I searched this page for "presuming uncorrelated error," Michael. It turns up for the first time in the same comment wherein you imply I missed it as part of the prior discussion.

      But it wasn't part of the prior discussion. You just invented it. I was discussing systematic error which is apparently present in the dO18 calibration experiments and is non-random. As part of the calibration experiments, that systematic error will propagate into any dO18 proxy reconstruction.

      That's very obviously important -- in fact, it's central -- and you have notably failed to recognize that or to consider it. And now I see that you don't want to discuss it at all.

      Fine. I'm tired of your manufactured indignation, anyway.

      You have my email address. If Kau or Kevin, or someone else decides to engage the systematic measurement error that turned up in the basic dO18 calibration papers, you can let me know and I'll drop by.

      [ What are we to do. We've identified your "central" point, refuting an entire branch of study that occupies dozens of scientists, a few of them of my personal acquaintance, based on a casual perusal of a few papers. We have also identified that this point appears to have an elementary error about the difference between bias and noise. You continue to weasel around about this basic point in a way that makes us think you've never done any observational science. Perhaps, charitably you are better as an experimentalist tha you are as an observationalist or a theoretician, but then you should limit your comments to experimental sciences. -mt ]

    • Arthur, I demonstrated above that the dO18 calibration experiments are, in fact, not "exceedingly precise."

      If you can't grasp that from the copious evidence provided, you've no business engaging the debate.

      [ Leaving aside that we are now going around in circles on an elementary point...

      Debate. Exactly. How boring to "debate".

      The spirit of science is to work backwards. If you have no idea how to do that, which apparently you don't, you can make no positive contribution. Please go back to Kloor's or Curry's where such "debates" are considered constructive for some reason. -mt ]

    • Arthur, systematic error subtracts away only when it is constant.

      Systematic error is clearly not constant in the dO18 calibrations assessed above. Surface air temperatures measured at a single location are known to show non-constant systematic errors over time because of variations in solar heating and wind-speed effects.

      These problems are discussed in published studies, for example, of which you are clearly unaware.

      As I mentioned to Michael, the conversations here have been unproductive. Best wishes for your future studies, Arthur. Be sure to then apply yourself assiduously.

    • Pat Frank - the examples of uncertainty you provided were uncertainty in derivation of *temperature* from dO18, not uncertainty in the dO18 measurement itself. Or did I miss something? Where did you ever show that the dO18 itself was subject to high uncertainties? Please provide a citation (just one is plenty).

      And you are the one using condescension and personal attacks here. I'm surprised after all your accusations against Michael Tobis.

    • #9 Arthur, I will presume you understand the obvious, that dO-18 proxy temperature reconstructions provide the context of my posts.

      That being the case, controlled laboratory conditions necessarily refers to the full proxy methodology, and those include the originating chemical methods.

      Your restriction of the meaning of controlled laboratory conditions to mass spectral O-18 measurement is then a sign that, at best, you have read my posts carelessly.

    • Michael, concerning the material aspects of your editorial insertion to comment #6: the "perusal" was hardly "casual," as it included recovering the data, reproducing the published empirical equations, and showing evidence of dO-18:T measurement error that should be propagated into a proxy temperature reconstruction.

      I have done no weaseling around the issue of noise and bias. It's an elementary of error analysis that noise and systematic error vary differently with number of measurements. Systematic error does not diminish as 1/sqrtN because it is not known to be random. It's also elementary that subtracting an average systematic bias does no necessary good when systematic error is not known to be constant.

      The test of McRae's work showed that the average bias varied with the two experiments. In fact, I've analyzed McRae's work further, along with Bemis, 1997, and others, and can show that empirical point scatter behaves as systematic error. I'll probably submit a post on that elsewhere.

      The result is that systematic error varies with each dO-18 experiment. There is no constant bias. There is no anomaly method to reduce the methodological error.

      But why belabor this. Here's a nice basic discussion. Consult the sections under systematic error and propagation of errors. It's all rms.

    • Pat Frank #10 - I didn't use the words "mass spectral" so I'm not sure why you interpret my words that way. But I did ask you for a specific citation on why you think there would be substantial errors in dO18 measurement, and you point back again to the uncertainties in full dO18-temperature analysis. Those are two different things, unless I'm really misinterpreting all this.

      That is, (1) there is dO18 measurement, which I claim should be fairly precise, but you stated has large uncertainties, and then there is (2) derivation of temperature from dO18 values, where you have indeed pointed out that there could be a number of possibly confounding factors in that analysis if other variables than temperature are not controlled.

      Now, reading Kaustubh's response to you below, it seems that you may have misrepresented that too - that is, the issue of "salinity" (a factor that is in fact specifically mentioned in the original post above - did you actually read that carefully?) is in itself a proxy for temperature in these analyses - changes in salinity in the real ocean are closely related to changes in water temperature at the surface. So the dO18 analysis in this system correlates to temperature based on physical causative relations both directly through temperature effects and indirectly through salinity effects; the resulting statistical relationship is highly significant as Michael has pointed out in its accurate accounting of ENSO events.

      So I'm not sure you really have any case here at all, in the end. But surely with your expertise you can write a simple explanation that clarifies your actual meaning here.

  14. Mr. Pat Frank is very good in his attempt to sell a crumbling house by directing attention towards the matching window frames and wall colour, despite the fact that the ceiling is missing. Hopefully, the buyer does his/her research.

    For example, he says, "If one does not know the paleosalinity, the derived paleotemperature can be mistaken by as much as 3 C. This shows the effect of historically invisible confounding influences on T:dO18 proxy reconstructions, and explicitly refutes your claim, Kau, that, “ONLY a change in temperature or a change in seawater δ18O can alter the δ18O ratio of foraminiferal calcite. If temperature and seawater δ18O stayed constant through time, the measured δ18O of would be constant too.” "

    If Mr. Pat Frank actually had any scientific knowledge of the field of stable isotopes and paleoceanography, he would already know that the paleosalinity of seawater, is actually inferred from the δ18O of the seawater! SALINITY (in strict physical oceanography terms - in PSU), mediates the amount of δ18O of seawater and ONLY the δ18O of seawater parameter along with temperature can physically change the stable oxygen isotopes of foraminifera. I was being physically explicit when I said foram δ18O = f(T,δ18O of seawater) - denying this is denying physics; however, δ18O of seawater IS SALINITY, but this relationship changes spatially. In summary, Mr. Frank actually becomes an arm waving paleoclimatologist (people who he really loathes) when he says that foram δ18O is a direct function of salinity (PSU).

    In any case, unfortunately, I do not have the time in the near future to set about correcting some of the many concepts that Mr. Frank has so poorly understood.

    Unfortunately, I am too busy doing science... fake science. I left my family, friends and hometown from two oceans apart, to come to Texas to indulge in fake science... on a whim; furthermore to a department where the person in the lab next to me performs perfectly valid petrological research, which I'm sure Mr. Pat Frank has no issues with.

    I like what Douglas Hofstadter had to say about Ray Kurzweil - "It’s as if you took a lot of very good food and some dog excrement and blended it all up so that you can't possibly figure out what's good or bad. It's an intimate mixture of rubbish and good ideas, and it's very hard to disentangle the two, because these are smart people; they're not stupid."

    Mr. Pat Frank, you are not stupid - you are a smart person.

    • Kaustubh, we can agree that dO-18 in shell calcite is a function of marine temperature and salinity.

      We can also agree that when constructing paleo-temperatures from fossil calcite, direct knowledge of paleo-marine temperature and salinity is not in hand.

      Therefore, one does not know whether any detected change in fossil dO-18 is due to a change in paleo-temperature, or in paleo-salinity, or both.

      But it gets more complicated. Bemis, 1997 discuss the non-equilibrium values of dO-18 in foraminifera, and relate that to impacts of variable symbiont photosynthesis and over-all marine [CO3(2-)]. Photosynthetic activity can vary with both cloudiness and turbidity, as well as nutrient flux.

      Temperature, salinity, photosynthesis, and [CO3(2-)] now represent four variables that enter into foraminiferal calcite dO-18. How does one then isolate a physically clean temperature signal from fossil foram calcite?

      Apart from that, however, the accuracy of a dO-18 measurement depends on more than mass spectrometry. It also depends on the chemical methods used to liberate CO2 from fossil calcite. For example: how much of the O-18 in the CO2 exchanges with O-16 in the water used to process the calcite.

      These variables can impact a dO-18 paleo-temperature reconstruction in unknown ways, and are responsible for the point scatter one sees in the experimental data. Therefore, any paleo-temperature reconstructed from fossil calcite must acknowledge the uncertainty due to the real possibility of confounding environmental variables that are currently invisible to analysis.

      Figure 2 in Bemis, 1997 displays the lines for 10 independent empirical dO-18 paleo-temperature prediction equations. The variation between the lines is far greater than the uncertainty due to measurement scatter about the mean line.

      Bemis Figure 2 shows that a single marine temperature can produce a spread in dO-18 of about 0.8%o. Conversely a predictive spread of about 3.5 C can follow from a single dO-18 value. And this is with known temperatures.

      The empirical spread displayed in Bemis, et al., Figure 2 implies an uncertainty of about (+/-)1.75 C in any reconstructed dO-18 temperature, just based on the spread of the standard empirical equations. This inter-equational uncertainty is in addition to the uncertainty within each equation itself due to the systematic point scatter I described above.

      As the internal measurement errors and the external inter-equational uncertainties stem from independent sets of systematic errors, they combine as the rms: (+/-)sqrt[measurement error)^2+(inter-equational spread)^2] = sqrt[(1.25)^2+(1.75)^2]=(+/-)2.2 C.

      All these variations are real and clearly reflect systematic errors due to unaccounted confounding variables. And those systematic errors have entered into empirical equations derived from studies where the water temperatures and salinities are known.

      I wondered whether paleo-salinity might be independently recoverable from Mg/Ca or Sr/Ca ratios. That might help resolve the confounding of temperature and salinity in fossil calcite. But apparently, that is not a current possibility. See Dodd and Crisp, Nürnberg, et al., and Takesue, et al.

      [... insulting ad hominem commentary removed - see moderated comments for the full comment along with some others from this and other posts - AS ...]


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