It is often good to focus on “The Truth” which in this post we will represent using $latex T_{true} $. We will also call this truth “the measurand”. With “The Truth” in mind, we will discuss the error in a measurement, apply that definition to define an error in a proxy reconstruction and and see if we can learn something Marcott’s Dimple.
In the figure above, we see a plot that shows “Uncertainty” in some unstated thing. Blog arguments have broken out; I think it’s worth considering how we would fill in the blank in “Uncertainty in _____”. I’ll begin with this question:
What is the measurement error in a proxy reconstruction for the surface temperature of the earth?
Let us consider the goal of such a reconstruction which is to estimate or measure the surface temperature of the earth, $latex T_{true}(t) $ which varies over time t. The proxy reconstruction is an estimate which we will represent as $latex T_{rec}(t) $. Given this definition of what we wish to measure, the error in the proxy reconstruction, $latex e_{rec} $, can be determined by applying the definition of a measurement error. That is we subtract our estimate from the thing we wish to measure.
The confidence interval for the measurement error $latex e_{rec}(t) $, is defined as the standard deviation across proxies of $latex e_{rec}(t) $ which we will represent as $latex \sigma_{e}(t) $. I claim confidence intervals based on this $latex \sigma_{e}(t) $ is the proper definition of “the measurement uncertainty” for the proxy reconstruction.
Before proceeding, it’s worth considering two example properties of confidence intervals described by $latex \sigma_{e}(t) $.
Feature 1: provided the temperature of ‘the earth’ $latex T_{true} $ is defined using a consistent baseline that is not affected choice of proxy, then the measurand, $latex T_{true}(t) $ is effectively deterministic. In this case, as long as $latex T_{rec}(t) $ from all possible proxies share a common baseline, $latex \sigma_{e}(t) = \sigma_{T_{rec}}(t) $ should be identical.
Feature 2: Since the motivation for the Marcott proxy reconstruction is to discover changes in temperatures of the earths surface over time, it is worth considering how the uncertainty intervals in (1) can be used to estimate the uncertainty in $latex \Delta T_{true} =[ T_{true}(t_{2}) – T_{true}(t_{1})] $ for an arbitrary choice of $latex t_{1} $ and $latex t_{2} $ .
Notice that if $latex T_{true} $ and $latex T_{rec} $ are both white noise, using definition of error in (1) has desirable property that the error for $latex \Delta T_{true} =[ T_{true}(t_{2}) – T_{true}(t_{1})] $ is $latex \sqrt{ [ e_{rec}^{2}(t_{2}) – e_{rec}^{2}(t_{1})] }$ Consequently, uncertainty and confidence intervals defined based on the standard deviation of these errors will exhibit this property one anticipates for uncertainty and confidence intervals of a measurement of $latex T_{true} $. (They will also share other properties one anticipates for confidence intervals of measurement uncertainties.) This means these confidence intervals are useful if we wish to make claims like that the one the one that follows:
” Global temperatures are warmer than at any time in at least 4,000 years, scientists reported Thursday, and over the coming decades are likely to surpass levels not seen on the planet since before the last ice age. ”
They are also useful if one merely wishes to know the uncertainty in when one compares the earth temperature in 1850 to the temperature at other times during the Holocene.
Other confidence intervals
Because our motive is to discuss alternate views of possible definitions of “confidence intervals for measurement uncertainty in a proxy reconstruction”, I will discuss a second set of confidence intervals discussed at some length by Nick Stokes. He seems to call these “confidence intervals [for some unstated property] of the Holocene temperature reconstruction”. (Note, I inserted the words in blue). His confidence intervals (for this unstated property) are defined as the standard deviation on $latex T_{rec, rebaselined}(t) $ which is $latex T_{rec}(t) $ from an individual reconstruction that has been rebaselined using the the mean of $latex T_{rec}(t) $ computed using reconstructed temperatures from that individual reconstruction over the baseline chosen for a particular analysis; we will denote the standard deviation for this quantity as $latex \sigma_{Trec,rb}(t) $.
For now I would like to highlight this feature of the confidence intervals for (some unstated thing): The measurand, $latex T_{true}(t) $ for the proxy reconstruction does not appear the definition. Of course, if we compute a standard deviation on $latex T_{rec, rebaselined}(t) $ we will obtain confidence intervals for $latex T_{rec, rebaselined}(t) $ which is something. So Nick is describing confidence intervals in the measurement of something.
However, it is rather difficult to use these intervals to compute the uncertainty in $latex \Delta T_{true} $ above. (We will later see that if you try to use them for that purpose, you do so incorrectly.)
The Toy Problem
I will now set up and discuss a toy problem which will show that — at least in the simplest problem the confidence intervals for $latex \sigma_{Trec,rb}(t) $ show a “dimple” in the baseline period, while confidence intervals for $latex \sigma_{e}(t) $ describing measurement uncertainty have no dimple. I’m not going to go so far as to claim that confidence intervals describing measurement errors can never have a dimple. It may be that under certain conditions they do. However, in this simple case, the dimple does not appear in confidence intervals for measurements errors.
True temperatures in ‘The Toy’
To set up the toy I will posit that the true earth temperature is measured at evenly spaced intervals $latex t_{i}$ and the measurements $latex T_{true}(t_{i}) $ are Gaussian white noise with mean 0 and standard deviation 1. The seeming contradiction that from the point of view of a proxy reconstruction the earth temperature is deterministic will be resolved by decreeing that the temperature already exists and once generated is considered “frozen”. The goal of proxy reconstruction is to figure out what those temperatures are.
We will decompose the temperature $latex T_{true}(t_{i}) $ into the mean computed during a baseline defined “N” specifically selected points in time, $latex \overline{T_{base}} $, and a residual $latex \overline{T(t_{i})} $ . The decomposition is:
Henceforth the overline $latex \overline{X} $ will be used to denote the sample average of X over whatever period is defined as the baseline for a proxy reconstruction. The subscript “base” above will communicate the same notion; its use above is redundant. (The redundancy may be helpful to those who wish to read the accompanying code.)
Note that outside the baseline $latex T(t_{i}) $ is a random variable with mean $latex -\overline{T_{base}} $ and standard deviation 1, while inside the baseline it is a random variable with a mean 0.
Proxies in ‘The Toy’
Next suppose we can obtain an estimate of $latex T_{true}(t_{i}) $ from available proxies. There are many and any individual proxy will be denoted with a subscript ‘j’. The raw proxy value of each proxy will be assumed to vary linear with true temperature as
where $latex m $ is the linear conversion constant which to simplyfy the analysis will be considered common to all proxies, and $latex W_{j} $ is Gaussian white noise with variance $latex B $ and zero mean. $latex P_{mean,j} $ as a constant which may be specific to the individual proxy. It is introduced to account for the effect of calibration biases of unknown magnitude in proxy ‘j’. For perfectly calibrated proxies, the term could be set to zero would have no effect on the value of $latex \sigma_{e}(t) $.
Let us now define the raw reconstructed proxy calibrated temperature based on a proxy ‘j’ to be
Error in the reconstruction and Uncertainty Intervals in ‘The Toy’.
With a small amount of algebra it is possible to show that the difference
$latex \displaystyle e_j{rec}(t) = T_{rec,j}(t_{i}) -[T(t_{i}) + \overline{T_{base}}] = W_{j}(t_{i}) + P_{mean,j}/m $
If we like baselines, we could define $latex T_{rec,j}(t_{i}) $ over the baseline as $latex T_{rec,j} $ and subtract write (5) above as
Recognizing that both $latex \overline{T_{base}} $ and $latex T(t_{i}) $ are unaffected by choice of proxy, j, the standard deviation of $latex e_{rec,j}(t_{i}) $ (i.e. $latex \sigma_{e}(t) $ ) over all possible proxies is unaffected by the magnitude of either. Their effect will be to shift every point in a reconstruction up or down uniformly by some unknown temperature. This is called a bias error and the standard deviation in that quantity would represent an uncertainty in the bias.
Diagnosing the contribution of $latex [P_{mean,j}/m] $ to $latex \sigma_{e}(t) $ is a bit more difficult. If all proxies responses are similar to a perfectly calibrated laboratory thermometers and the true surface temperature of the earth was known, then we would anticipate that $latex [P_{mean,j}/m] $ would be effectively deterministic for a proxy reconstruction. (Specifically, the analyst creating the reconstruction could subtract out value at the “true” baseline temperature for the earth and it the term could be forced to zero for every proxy.) So the the term would make no contribution to $latex \sigma_{e}(t) $.
However, if a thermometer is more like single “treenometer” or the true surface temperature of the earth can never be known, then $latex [P_{mean,j}/m] $ may include sizable random component that corresponds to different calibration errors both for true thermometers and “treenometers”. The magnitude of that calibration error will depend both on the noisiness of the ‘treenometer’ itself (i.e. the magnitude of “B” for the proxy), the number of data points used to calibrate the individual ‘treenometer and the uncertainty in the true temperature of the earth.
However, the effect of $latex P_{mean,j}/m $ is irrelevant to the question of “The Dimple”. So in the (not yet written part II) of this discussion, I will show graphs of the uncertainty computed with $latex P_{mean,j}/m $ set to a deterministic value. This decision means that I will be finding the
Before moving on, let’s consider some features of confidence intervals based on (5) or (6) . In ‘The Toy’ problem neither $latex P_{mean,j}/m $ nor the standard deviation of $latex W_{j}(t_{i}) $ are functions of time, therefor the $latex \sigma_{e}(t) $ is not a function of time. So $latex \sigma_{e}(t) $ will contain no dimple in this problem.
Nick’s uncertainty intervals in the toy.
Finally, it’s useful to examine the properties of Nick’s confidence intervals for some unstated thing. Recall his confidence intervals are defined as the standard deviation of rebaselined reconstructions. Using the overbar terminology that means his he is taking the standard deviation of:
If we take the standard deviation of (7) to obtain $latex \sigma_{Trec,rb}(t_{i}) $ we will find that both terms on the right hand side contribute to this standard deviation. In this case, $latex \sigma_{Trec,rb}(t_{i}) $ is a function of time. For points inside the baseline, $latex W_{j}(t_{i})$ and $latex \overline{ W_{j} } $ are positively correlated and $latex \sigma_{Trec,rb}(t_{i}) $ will be smaller than the variance of $latex W_{j}(t_{i})$. For points outside the baseline, the two noise terms are uncorrelated; the computed variance will be larger than $latex W_{j}(t_{i})$.
——–
From this we can identify a differen measurement error which is
If we take the standard deviation of (8) to obtain $latex \sigma_{Trec,rb}(t_{i}) $ we will find that the two terms on the right hand side contribute to this standard deviation. In this case, $latex \sigma_{Trec,rb}(t_{i}) $ is a function of time. For points inside the baseline, $latex W_{j}(t_{i})$ and $latex \overline{ W_{j} } $ are positively correlated and $latex \sigma_{Trec,rb}(t_{i}) $ will be smaller than the variance of $latex W_{j}(t_{i})$. For points outside the baseline, the two noise terms are uncorrelated; the computed variance will be larger than $latex W_{j}(t_{i})$.
This is the origin of the dimple which does appear in the sorts of confidence intervals Nick is computing but does not appear in confidence intervals describing measurement errors of absolute temperatures.
Nick will be happy to know that I now see a “measurement error” because it is expressed relative to a measurand! (Whether this measurement error is properly interpreted when these are compared to temperatures in the thermometer record or projections I cannot say because we now have two types of measurement errors but which is most easily used when patching to a thermometer record I don’t yet know.)
Before continuing on to the exciting plots (to appear in Part II), I think it’s also worth noting that $latex P_{mean,j}/m $ does not appear in (7 or 8).
This means that whatever (7) is supposed to account for, it does not capture the effect of calibration bias in proxies on the uncertainty in measurement errors in proxy reconstructions. For this reason alone, whatever the confidence intervals might be what they are not is confidence intervals that can be used to compute the uncertainty in $latex \Delta T_{true} =[ T_{true}(t_{2}) – T_{true}(t_{1})] $ .
I don’t know if confidence intervals computed the way Nick is computing confidence intervals were applied to estimate the uncertainty in $latex \Delta T_{true} $ in Marcott. But if the claims about temperature differences relative to those in the thermometer record made in Marcott are based on that sort of confidence intervals, those claims would be based on misinterpreting what confidence intervals computed the “Nick” way describe. Remedying this mistake would require computing confidence intervals for the error in the reconstruction. A proper estimate would require capturing the effect of the calibration uncertainties described by $latex P_{mean,j}/m $.
Summary: Part I
Since I’m going to be showing graphs in separate posts it’s useful to summarize the main points in this post:
- The uncertainty intervals computed using (1) correspond to the uncertainty in the error in a reconstruction. These are useful if you wish to determine the uncertainty in the difference in the temperatures at two different times in the earth’s history. Learning this difference seems to be the goal of a proxy reconstruction, so these confidence intervals are useful and describe the uncertainty in the measurand of interest. These uncertainty intervals will not show “The Dimple”. I call these proper “measurement uncertainties” for a proxy reconstruction because they can be used to estimate the uncertainty in the measurand of interest (i.e. the changes in the temperature of the earth.)
- The uncertainty intervals computed using the method discussed by Nick in his blog post
are notmay not be useful if we wish to estimate the uncertainty in the difference in the temperatures at two different times in the earth’s history when one of those times lies outside the range of the proxy reconstruction. If we base claims about the statistical significance of differences in temperature on that sort of confidence interval, your conclusions will have no legitimate foundation and — unless we are sufficiently luck– our claims will be incorrect. These confidence intervals will show “The Dimple”. - Computation of the two sets of confidence intervals share some features. In certain limits, the quantitive difference between the two will be imperceptible and conclusions based on the “Nick” type intervals be nearly identical to those made with proper uncertainty intervals. This happens only when both the following are true: The proxy reconstruction used a baseline of sufficiently long duration to make “The Dimple” so small as to be imperceptible and the proxies calibration is perfect. However, the fact that “The Dimple” appears is sufficient evidence to demonstrate this goal has not been achieved.
- I have no idea whether Marcott’s claims about the uncertainty in temperature changes relative to the thermometer record were based on uncertainty intervals computed as in the top figure in this post. I know those uncertainty intervals are described, but not having read the paper, I don’t know if those uncertainty intervals were used without modification to estimate the uncertainty in difference in the earth’s temperature at different points in time nor do I know whether those uncertainty intervals were places around the mean reconstructions in their figure of the reconstruction. (If they were, that choice would be misleading.) Because I don’t know whether they did these things, I cannot say whether how Marcott might have used confidence intervals computed the “Nick” way, I can’t say whether what they did was “right” or “wrong”. I can say nevertheless say that if they used that sort of confidence interval to compute the uncertainty interval for temperature difference at different times on earth or if the used slapped those sorts of confidence intervals around the mean reconstruction and represented that as the uncertainty in the measurement of the earth temperature, that would be misleading to the point of being incorrect.
Upcoming: Graphs showing “The Dimple” as it appears in “Nick-type” confidence intervals if the temperature series and the proxy noise are Gaussian white noise. Afterwards, graphs showing the relative size of confidence intervals using selected values chosen to highlight qualitative effects of interest which may not correspond to values relevant to Marcott. Those of you who like math and have been reading Marcott can suggest reasonable values for the random componenent of $latex P_{mean,j}/m $, and the noise in the proxy reconstruction and so forth.
Teaser graph
I’m still trying to get my head around this idea, which Nick says is used by everyone in the field. Is that true, by the way? It just seems completely nuts. Just to give an example, isn’t there a vast dependence on exactly where you decided to set as your baseline point? If you happened to pick a time with little variance, you won’t move things much. If it had a lot of variance, you are artificially introducing a big spread everywhere, right into the twentieth century. I don’t get how this can be a good idea. I know Nick will answer that we aren’t discussing what you think we are, but I no clue why what he thinks he’s discussing makes any sense.
MikeR–
Which idea? Rebaselining is used by everyone in the field.
Nevertheless, Nicks’ confidence intervals do not describe uncertainty in the proxy reconstruction as a measurement of earth’s temperature during the period of the reconstruction.
Based on the other thread, it appears he thinks the blank in
““Uncertainty in _____â€.
should be filled in with “who cares? Uncertainty is just the output of a mathematical process”.
Of course, if that’s the case, we can’t begin to guess what questions can be answered using his confidence intervals. As far as he will answer, his confidence intervals just seem to be some sort of generic confidence intervals. I don’t dispute they are confidence intervals for something. (Heck, I even know what they are confidence intervals for. Oddly, I suspect he does too. And the difficulty is that those intervals are quite obviously not the confidence interval for the uncertainty in the reconstruction.)
But maybe I misunderstand him.
Shouldn’t every proxy that shows a dropping temperature in the 20th century have an uncertainty of infinity?
And then every proxy of the same type, whether it goes up or down, should also have an uncertainty of infinity?
Lucia,
“His confidence intervals (for this unstated property) “
I say over and over, it is for the anomaly mean. A well defined set of numbers that can actually be calculated.
But you want confidence intervals for T_true, the temperature of the Earth. You can’t have confidence intervals without a number. What is it? The Earth is festooned with thermometers and satellites. So what was the true temperature for 2012. 12°C? 14°C?
ps if you want evidence that people do think about the uncertainty of anomalies, it’s here.
This sounds a lot like a kind of dimensional analysis.
Bruce–
I’m going to move your comment because it is OT for this thread.
Examine equation (3). Your question relates to how we would determine the magnitude of ‘m’ and Pmean,j. In ‘This Toy’ these quantities merely claimed to exist and we will say they are random variables with some particular distribution. If you want to criticize any particular choice of proxy in Marcott, you are going to have to find a thread where where the choice of proxies is discussed. I’m going to put your comment on the most recent open thread.
Nick
That’s not what you seemed to communicate on the other thread where you wrote “Lucia,
It’s late here, but I’ll just offer one more thing. I don’t think CI’s belong to things. They belong to calculation processes.” .
Now you seem to be saying the “thing” the CIs belong to is the “anomaly mean”. This remains indefinite. But at least we are getting close enough that I can ask you whether by “anomaly mean” you mean:
1) The anomaly for the earth temperature as it actually existed during proxy reconstruction period? or
2) The anomaly for the mean of all proxy reconstructions?
3) Something else?
Because the earth temperature as it actually existed during the proxy reconstruction period is the measurand in a proxy reconstruction. Nothing else is.
The mean of all proxy reconstructions is not “the” or even “a” measurand. Each proxy reconstruction and even the mean of all proxy reconstructions is an estimate of the measurand. All measurement errors and uncertainties are defined relative to the difference between the estimate and the measurand.
This is precisely why people like me, Carrick and others keep saying that the uncertainty intervals you are spending a lot of time on are not measurement uncertainties. Because they have nothing to do with the measureand.
However measurement uncertainty is defined it needs to be defined to describe the uncertainty in the difference between the estimate and the measurand.
@Nick: When you say uncertainty (as reflected by confidence intervals) is associated with a procedure and not an object or particular data, I agree.
So my question then is what is the procedure that you’re thinking of. It’s not taking a mean, since taking a mean introduces no uncertainty. It’s not calculating anomalies, since that introduces no uncertainty. So where (what procedure) is the uncertainty coming from?
I’ve seen you say things like “The individual proxies are set to a base period of 4500-5500BP. That’s when the CIs are determined.” But I haven’t seen any indication of the actual procedure that generates the uncertainties upon which your CI’s depend. I may have missed something, of course.
I think that’s where Lucia’s going, though from a different philosophical direction. She’s come up with a procedure that generates meaningful uncertainty in the context of Marcott: uncertainty in the temperature of the Earth at time $t$, given (interpolated) information in proxies at time $t$.
Nick:
…but is still a useless quantity, unless it’s relatable to temperature. Seriously, take a baseline shift of temperature, and we are no longer talking temperature???
You’re a smart guy, I thought you understood the concept of relative versus absolute measurements.
If you knew the value from theory, you wouldn’t have to measure it.
The whole friggin’ point is, it is a measurable.
If I were Marcott, at this point, I would say “Stop defending me; I am trying to characterize temperature not fictitious variables.”
Can I ask a really simple question?
I understood that we could work out the variance of a normally distributed population, we have, with relative ease. Does one not one use a jack-knife procedure whereby one drops the n to establish the relationship between variance and population size ?
Wayne,
“It’s not taking a mean, since taking a mean introduces no uncertainty. It’s not calculating anomalies, since that introduces no uncertainty.”
A mean has uncertainty, which it inherits from the things you added. In fact, recon is basically taking a mean and the uncertainty of the recon is the uncertainty of the mean.
Calculating an anomaly introduces an uncertainty, because it subtracts an uncertain mean. That’s actually why the dimple. If you subtract the mean of some faraway time, then its randomness is uncorrelated and just adds variance. But if you subtract a mean of numbers that include that time spot, then it’s correlated, generally positively. That means you take away some of the uncertainty.
Carrick,
“If you knew the value from theory, you wouldn’t have to measure it.
The whole friggin’ point is, it is a measurable.”
I’m not asking about theory. I’m asking what’s the number. A very practical question. If it’s measurable, someone must be measuring it. Somewhere there would be a number. That’s what measurements are. What is it? Where?
Maybe I can serve as a useful idiot. I don’t have much of a clue about what the controversy is here. It seems that most are concerned about the uncertainty of measurements and Nick is concerned about the uncertainty of adding up and dividing some set of numbers to get the anomaly mean, whatever that is. It seems to me that the former is more important and interesting than the latter. But what do I know?
Nick, let’s pretend that you were curious about the height of sixth graders in your town and you decided to do some research. You get yourself a stick that you judged to be about 5 feet long and went around soliciting sixth graders to stand next to your stick. You eyeballed the subjects height relative to the stick and you took note of the anomaly (?). Is that kinda of a valid analogy to the temperature proxy foolishness? Anyway, you take your data (guesses) and you calculate your anomaly mean. Why would the uncertainty of your calculations be more interesting than the uncertainty inherent in your measurement tools and method?
Nick
The number that describes what?
My method of computing uncertainty intervals give the “number” that permits us to find the ±95% confidence intervals that the temperature anomaly falls inside the reconstruction. Yours don’t. See text at bottom of teaser graph.
Nick,
Could you provide an answer to my question in lucia (Comment #112023)?
Nick
You persist in leaving out important detail.
The uncertainty in the mean of all possible reconstruction using all possible proxies is certainly the uncertainty in the mean of the reconstruction. It would be useful if you include the details “of the reconstruction”.
What it is not is the uncertainty the reconstruction as an estimate of earth’s temperature.
The latter is an interesting, useful and important quantity (and has no dimple). It needs to be quantified if you want to know how close your proxy reconstruction is to the thing you want to measure: That is the earth temperature.
The former quantity which you seem to want to discuss at length is practically useless.
Lucia,
“Could you provide an answer to my question in lucia (Comment #112023)?”
3) Something else. It’s the mean of the proxy anomalies.
But I wish someone would answer my question.
“It needs to be quantified if you want to know how close your proxy reconstruction is to the thing you want to measure: That is the earth temperature. “
What is the earth’s temperature? In 2012, say, with all the info we have? If it’s the measurand, who measured it? Did they just not think to do it?
And the other very basic question, if you don’t have numbers, how can you get a CI?
Nick
Do you mean “what is the numerical value”? We don’t know that value. But we can compute the uncertainty in the proxy estimate despite this. The fact that we don’t know it is entirely irrelevant to computing standard deviation in the difference between the proxy estimate and the earth’s temperature.
I’ll answer that with a question: If you don’t know the number that represents the earth’s temperature, how can you compute the temperature anomaly for the earth’s temperature?
In fact, you and I both know that not knowing the number for the earth’s temperature is not an impediment to computing the anomaly.
As it happens, not knowing the number for the earth’s temperature is also not an impediment to computing the uncertainty in a proxy reconstruction relative to the unknown number that represents the earth’s temperature. Just as the temperature anomaly can be computed without knowing the number that represents the temperature of the earth in absolute unites, the uncertainty in the proxy reconstruction relative to that unknown number can also be computed. (I can’t help wondering why you who are constantly explaining that not knowing the number that corresponds to the earth’s real temperature are asking what you are asking.)
As for the answer to the question you asked: Read my post. The method is explained.
Nick Stokes, “What is the earth’s temperature?” Which one? See that is where the absolute values that came with the proxies could be helpful. When you switch proxy reconstructions to anomaly you can only look for correlations. Making the baseline 4500 to 5000 BP means you exaggerate differences at the point you want to get more information about. Since it is pretty obvious that the hemispheres respond differently, as in non-linear, you would want to “try” different baseline periods.
Hmm? Non-linear times series analysis, what a novel thought.
Nick:
I’m not going to spend anymore time discussing this with you, sorry. I don’t see this as being fruitful time spent for either of us.
Lucia,
“As it happens, not knowing the number for the earth’s temperature is also not an impediment to computing the uncertainty in a proxy reconstruction relative to the unknown number that represents the earth’s temperature. “
I disagree. If we could do a proxy recon of earth’s temperature in 5000 BP, we could surely do one for 2012, with all the proxies we now have (thermometers, AVHRR etc). But we can’t. There are just no numbers of any kind.
But there are plenty of anomalies. As I mentioned in my first post, both GISS and NOAA explain why it’s this way.
Nick –
If you want to know the earth’s temperature in 2012, consult this page, where they give instructions: “It is possible to develop an absolute temperature series for any area selected, using the absolute file, and then add this to a regional average in anomalies calculated from the gridded data.”
HaroldW,
Yes, of course you can do that. But you are adding an anomaly mean, with CI’s calculated accordingly. Subsequently adding it to a local mean doesn’t change anything there. They all say something like that. Here’s GISS:
“Q. What do I do if I need absolute SATs, not anomalies ?
A. In 99.9% of the cases you’ll find that anomalies are exactly what you need, not absolute temperatures. In the remaining cases, you have to pick one of the available climatologies and add the anomalies (with respect to the proper base period) to it. For the global mean, the most trusted models produce a value of roughly 14°C, i.e. 57.2°F, but it may easily be anywhere between 56 and 58°F and regionally, let alone locally, the situation is even worse.”
Note, BTW, that they say you’ll need to use a modelled climatology. Not exactly a “measurable”.
Nick, I had missed the link to your blog, so my questions were ill-informed. I can’t seem to post to your blog (preview, actually), so I’ll ask here. Two questions now: 1) do I understand the toy example with the dimple, and 2) do I understand the process you’re describing.
1. I ran some R code, below, to recreate the dimple as best as I can understand it. The depth of the dimple appears to be directly related to the amount of correlation in the series, which would directly affect the calculation of the SE of the mean that you subtract in order to create an anomaly series. Is the dimple perhaps due to ignoring the SE of the mean? (At least in the toy.)
Is the following R code correct?
set.seed (14587)
foo <- replicate (100, arima.sim (list (ar=c(0.8), sd=1), 110))
foo.sd <- apply (t(foo), 1, function (x) sd (x[50:51]))
foo2 <- apply (t(foo), 1, function (x) x - mean (x[50:51]))
# The depth of the dimple depends on the AR coefficient...
matplot (foo2, type="l")
lines (apply (foo, 1, sd), type="l", col="red", lwd=3)
lines (apply (foo2, 1, sd), type="l", lwd=3)
abline (h=0, col="white")
# SE of the mean is normally sd / sqrt (n), but that's for the case of
# no autocorrelation. In our case, it's 0.8 I believe, so:
summary (((1 + 0.8) / (1 - 0.8)) * foo.sd / sqrt (2))
summary (apply (foo, 1, sd))
summary (apply (foo2, 1, sd))
2. Do the proxies start the process as anomalies, or are they made into anomalies? If they start as anomalies, how are their formulas calculated in the first place? It would seem to me that proxies wouldn’t be linear across their range so you’d have to know something about the rough range of temperatures you’re talking about in the first place. Or is this not correct?
HaroldW, the reason they break it down this way also follows from measurement theory.
The absolute temperature of the Earth has a larger uncertainty than the relative temperature (pinned to a proper baseline).
Thus if you present numbers as absolute quantities, the uncertainty associated with a temperature difference $latex T_2 – T_1$ becomes artificially inflated if you make naive assumptions about their respective errors. By breaking it down, it allows you to compute the correct uncertainty much more easily.
I should note that $latex T_2 – T_1$, with $latex T_1, T_2$ expressed in absolute numbers, actually has the same uncertainty computed properly as it does if you use anomalized numbers, it’s the uncertainty computed with the assumption that the errors in $latex T_1, T_2$ that gives an erroneously large value.
So the problem is the violation of the precept of ordinary errors in quadrature. I’ve encountered a similar problem in other areas as a grad student.
Basically if you perform the error analysis, and allow the quantities to have an uncertainty, the error of the difference really is
$latex \sigma_{1-2} = \sigma_1^2 + \sigma_2^2 – 2 \rho_{12}\sigma_1\sigma_2$
Hopefully the quantities are obvious, other than $latex \rho_{12}$, which is the correlation coefficient between the measurement uncertainties $latex T_1$ and $latex T_2$.
If the errors are exactly correlated, you get
$latex \sigma_{1-2} = | \sigma_1 – \sigma_2|$,
uncorrelated
$latex \sigma_{1-2} = \sqrt{\sigma_1^2+ \sigma_2}$,
and anti-correlated ($latex \rho_{12} = -1)$,
$latex \sigma_{1-2} = \sigma_1 + \sigma_2$.
Similar formulas can be derived for the product and division of the quantities.
Nick:
Be careful, you’re starting to sound like a WUWT commenter now. Wait did somebody hijack your account. >.<
A thermometer works based on a model, so does practically any other sensor.
Carefully designed sensors are modeled to reduce the influence of confounding factors (e.g., pyroelectric effect when you are trying to measure piezoelectric effect).
And of course anomalized global mean temperature is computed from a model. The fact a model is employed as part the measurement process has absolutely nothing to do with whether the quantity is measurable.
[Noticed too late I had a typo in my generalization of the quadrature formula. It should read
$latex \sigma_{1-2}^2 = \sigma_1^2 + \sigma_2^2 …$ ]
Wayne,
On your R code, yes, I think it’s correct for calculating the anomalies for plotting. I think the Quenouille correction should have a sqrt. The foo.sd stuff doesn’t look right; in fact it looks like you’re taking the sd of just two numbers. But I might have the dimensions wrong.
But my dimple expt wasn’t a Monte Carlo. it’s based on theoretical AR(1). In fact, I’ve posted an analytic solution.
The proxies are made into anomalies at an early stage, but after conversion to T. For Marcott it is stage 4. Basically, anomalies are needed to do any averaging across proxies.
Nick
Huh? First, I have no idea what you mean about not being able to do a proxy recon of the earth’s temperature. Thermometers located at a particular point on the earth can be considered “proxies” for the mean temperature of the earth. — quite good ones compared to treenometers in fact. NOAA, GISTEmp and HadCrut could all be considered “proxy reconstructions”. That said we tend to use the word “proxy” for something other than thermometer. We can certainly estimate the uncertainty of the earth’s temperature based on thermometers if we wish. And we can also estimate the uncertainty in changes in the earth’s temperature if we wish.
But beyond that, even if it is true we can’t do whatever it is you recognize as a proxy reconstruction for 2012 is utterly irrelevant to determining whether we can estimate the uncertainty in the a proxy reconstruction relative to the earth temperature in proxies reconstructions we can construct. And we can.
HaroldW–
Note that my errors in (1) and the uncertainties based on them are still temperature differences. That is a reason we never need to know the absolute temperature of the earth to estimate the uncertainty intervals for the errors.
Lucia, Pmeanj looks like tons of fun. Sirce et al have one sub-polar reconstruction with two cores, one at 470 meters and the other at 2650 meters, with “SST” diverging about 4C in interesting spikes on occasion. It seems like the “bugs” tend to drift more around the deeper “SST” cores near convergence zones. That would be Rapid 21-3K core which on Nick’s Marcott proxy viewer looks surprisingly mild mannered. So should Pmeanj be for the actually proxy or the milquetoast version?
Lucia,
“while inside the baseline it is a random variable with a mean 0.”
This doesn’t look right. The mean over the baseline should be 0, but not individual points.
“I don’t know if confidence intervals computed the way Nick is computing confidence intervals were applied to estimate the uncertainty in ΔT_{true} in Marcott.”
Marcott et al don’t compute that – like everyone else they compute the anomaly mean. Their y axis in Fig 1 (the famous one) is clearly labelled “Temperature anomaly”. And the blue CI’s are on that diagram. It’s not hard to work out that they are meant to be CI’s of the temperature anomaly. That’s why I can’t understand your insistence that there ius some mystery about what I am computing. It is those lines (in a toy version) which are also the curves in your pic above. They are unlabelled only because you are showing Steve M’s replot.
And yes, I think they did compute them this way. There is a layer of complexity with Monte Carlo re calibration uncertainty etc, but I don’t think it changes anything.
” But if they claims about temperature differences made in Marcott are based on that sort of confidence intervals,”
No, they aren’t. They are based on Fig 3, where a distribution of Holocene temperatures is histogrammed. Variance from here is a component, but they also experiment with adding noise to compensate for lack of high freq resolution.
In Eq 4 you define what you call a raw reconstructed temperature. It isn’t; it carries a j suffix. It is a proxy calibrated temp. Reconstruction happens when you combine proxies.
This is the key problem – you haven’t said anything about this step, and it’s the one that requires anomaly. You’ve written a whole lot about true temp with no indication as to how you can get it. As I’ve said ad nauseam, I don’t believe you can. I’m none the wiser.
I’ve no idea what is happening in (6); is there meant to be a j on the left? It looks like you treat e as a post-recon error, but no indication of how you put it together.
Nick
Random variable with mean zero means that the mean over the baseline is zero but the individual points are not necessarily zero. So, while you start with “That doesn’t look right, as far as I can tell, I described it as having precisely the properties you say it ought to have.
I know their graph is a temperature anomaly. You seem hung up on believing that I am not talking about anomalies. Anomalies are just a shift.
1) The earth’s temperature can be represented as an anomaly. This anomaly can be (a) relative to its own mean temperature during a baseline.
2) Each temperature estimate from an individual proxy reconstruction can be represented as an anomaly. The temperature estimate be turned into an anomaly relative to the its own mean temperature during a baseline
3) The temperature estimate from the mean of all possible proxy reconstructions using an infinite number of proxies “j” can be represented as an anomaly.
There are other choices for temperature anomaly– because people can actually use the proxy reconstruction to compute the shirt for the earth temperatures and vice-versa. But (1) – (3) are most common. But that still leaves “the anomaly” ambiguous.
So, with respect to this:
If you think it’s obvious, why don’t you say which of the three temperature anomalies above are supposed to fall inside those CI’s? Because “the (definite article) anomaly is not enough to tell me which on you think falls in there.
In a previous comment you seemed to say it’s (3). If so, those would be called “stupid meaniningless CI’s. But if (1) is supposed to fall in there, at least for now, I think those CI’s are wrong, though there may be some way in which the algebra can be made to work out. (I’m willing to be persuaded I’m wrong and I’m going to be doing some montecarlo on the toy to compute rejection rates. )
Uhmm.. I assume you mean anomalies right? 🙂
Anyway, the temperatures in that histogram are computed how? Displaying the seam set of numbers in a histogram vs. in a time series isn’t material. If the confidence intervals around the mean proxy reconstruction don’t represent confidence intervals for the earth’s temperature but instead contain the spread for another proxy reconstruction, then reorganizing that data into a histogram isn’t going to reveal much of anything about the spread of earth temperatures during the holocene.
Ok. I’ll edit to call it a it a ‘proxy calibrated temp’. We can then average over a bunch of them. If you average over a bunch of them. Other than terminology, I’m not seeing how this is material to the discussion of the measurement uncertainty.
I don’t see how this is a problem. Even if I didn’t write a paragraph explaining that this equation can easily be viewed as computing the proxy values based on anomalies, it can be. I didn’t think it was worth wasting the paragraph because it’s rather obvious. On the right hand side, Pij=(mTij + Wij) is exactly what you would write if you wrote your equation based on an anomaly during the chose period. That makes (mTbase +Pmean,j a term that permits you to shift from calibration from one one baseline to another. But most people would define their proxy values such that (mTbase +Pmean,j ~0 based on whatever data they use to create their calibration curve. But non one can force the term to exactly zero because there is calibration error. (Well… of course someone can do an analysis forcing the term to zero. But then one can’t explore the effect of calibration error on uncertainties in proxy reconstructions.)
I wrote (4) in terms of real temperatures of the earth, not the anomaly. But once again, it really doesn’t matter. Doing so would make equations (5) and (6) identical because the mean reconstructed temperature in the baseline would be zero. I wrote (4) the way I did precisely to show that it doesn’t matter. Either you use anomalies in (4) and then (5) and (6) are automatically identical or you use raw temperature in (4) and you get the exact same result for the uncertainty in the proxy reconstruction.
If you think there is a specific problem caused by my including this term in (3) or (4) please elaborate. Because I think this representation is perfectly consistent with the common practice of using anomalies in proxy reconstructions.
Lucia: I’d like your emphasis on understanding the error in the difference between reconstructed temperatures. Absolute temperature is usually meaningless, we are usually interested in climate CHANGE. When we look at reconstructions that cover the last two millennia, we often want to know was the MWP definitely cooler or warmer than today, or does the 95% confidence interval around the difference include zero. Or how much cooler was it during the LIA than today?
When we want to calculate climate sensitivity from paleoclimatology data, we need to know the confidence interval about the actual temperature difference, not the reconstructed temperature difference. Your approach is the one that will provide the confidence interval that is relevant to this problem.
As Carrick notes above, if the uncertainties in two measurements are correlated, then the uncertainty in the difference is not always the uncertainties added in quadrature. In the case of Marcott’s alkenone proxies, when proxy measurement are converted to temperatures via a linear relationship (T = m*P + b), the uncertainty that b (the y-intercept) contributes to T at one time point appears to be correlated with the uncertainty it contributes at all other times points.
Lucia,
I don’t get your first part of the toy problem at all. You’ve let T_true be, AFAICS, “frozen” white noise. I assume that’s just a way of generating a set of numbers – would it matter if it was red noise, for example?
But the confusion is that following (2) I’d expect T to be “frozen” too. It’s just algebra. But then you say it has a mean, zero in the base range.
I think your toy problem is quite complicated, and it would be better to take the temps as given rather than bring in the proxy calibration formulae. But I don’t get (3) at all. It’s normal to assume that proxy value goes with local temp. But you’ve made it go with global. And (4) seems very odd. What kind of proxy value do you have in mind? d18O say. It would be strange to consider a simple multiple of that as temperature.
The problem with (5) is that on the left you have e(t), no j. On the far right, you have W_j(t)+P_j. That implies that W_j has the same time variability for all proxies. But it’s supposed to be white noise.
“Anomalies are just a shift. “
No, there’s a vital difference when you reconstruct. Each curve is relative to its own base average. So there’s no way you can unshift once you’ve combined them. The anomaly mean isn’t just the “true temp” shifted. That’s why I think it is so important that you spell out your combination process.
I’m just totally lost. I guess I’ll have to wait.
Wayne2,
I’ve posted my own R code for the second post. I’ve also added a section explaining how the stochastic equation I analyzed relates to a recon, and showed the result.
I have now done a Marcott emulation in the style of Loehle and McCulloch 2008 here. I have calculated the confidence intervals in the same way as L&M – ie as standard error of the weighted mean across proxies. I do not do the Monte Carlo, and so there is a lot less smoothing. My CI’s are quite comparable – narrower in the central region, and broader back beyond about 7000BP.
As a result I am convinced that they have included between proxy variation in steps 5-6 of their stack reduction, and that there is no major omission in their CI calculation. I have included the R code.
And yes, there is a dimple. The method I used is equivalent to the method I used in the dimple posts. It produces exactly the CI’s oof the thing plotted – the anomaly mean reconstruction, as indicated in the Marcott plot on which my result is superimposed.
Yes. it’s just a way of generating numbers. I don’t think it would make any difference to the algebra in this post if it was red. (Actually, I don’t think it would make any difference at all. )
It is frozen. Frozen means they don’t change when you pick a new proxy. So, they are deterministic in the sense of not varying in the problem at hand.
But even if something is not random, you can still compute an average. The average over the data points inside the base range is 0. If you have an infinitely long series, the average over the data points outside will be -Tbase. So there is no contradiction between something being frozen and computing a mean or average over data points. (You treat data records from a station– say Ohare– as ‘frozen’ and compute things like the mean for 1921 all the time. This is entirely similar.)
The temps are “given”. They are given as soon as you generate them. I generate them using a white noise generator– but that doesn’t change that they are given. How is this ‘complicated’? The measurand has to come from somewhere and you do have to write it down.
I’ve simplified out geography. There is no local or global. There is only one point. So, if you want to think of those as local temp, feel free to do so.
What’s odd about it? I don’t even know why you are asking about d180. If the relationship between the proxy value and temperature is linear, then you can convert using a linear conversion– to within a constant. (If you pick m=1, then the P’s are just Trec’s and we they are just what’s in your posts. So I really don’t see why you think this is odd.)
Typo. Sorry. Let me go fix that. The e’s do have ‘j’s.
Yes. That’s how I thought the spaghetti related to the average of the spaghetti. I still don’t know see you saying anything about how the spread in the spaghetti relates to confidence intervals on measurement uncertainty in the measurand (i.e. the earth temperatures or earth temperature anomalies– which ever you prefer.)
Frank
Agreed. but my toy is using white noise to start out with something as simple as possible. After I can confirm this is getting me proper rejection rates for the ‘measurand’ in the montecarlo of the toy, I might move on to more complicated noise.
Lucia,
“But even if something is not random, you can still compute an average. The average over the data points inside the base range is 0.”
I really don’t get this. T(t_{i}) is deterministic. How can it have an average different to the number itself? And you didn’t say the average in the base range was zero. You said:
“Note that outside the baseline T(t_{i}) is a random variable with mean -\overline{T_{base}} and standard deviation 1, while inside the baseline it is a random variable with a mean 0.”
Sounds like you’re talking about the time points there.
“I’ve simplified out geography.”
More than geography. You’ve assumed that all proxies are reading the same temperature. They provide no information. The only variation is white noise.
“to within a constant”
But where is it?
This would be the extra terms in (3) you seem to not like. As I said, they capture our ability to define things on whatever baseline we like but more importantly capture the uncertainty in the calibration of the proxies.
It’s this calibration error that makes the main difference between my confidence intervals (5 or 6) and yours (7). Of course, there is also the issue of the dimple which arises because your are confidence intervals in “repeated temperatures from proxies”. While mine is a confidence intervals in “the difference between the temperature from a proxy and the true temperature.”
Lucia,
“I still don’t know see you saying anything about how the spread in the spaghetti relates to confidence intervals on measurement uncertainty in the measurand “
The recon is really just a mean. And the CI I use is the standard error of the mean. Pretty orthodox. Variation across proxies is taken to be independent.
from
http://www.moyhu.blogspot.com.au/2013/04/confidence-intervals-match-marcott-et-al.html
All you seem to be saying here are:
1) If Loehle and McCulloch 2008 did something then it must be the right way and
2) That you think the bias errors “must have been” included.
But that’s not so. It’s always possible for someone to fail to include something. Even Loehle and McCulloch.
Anyway:
You can never drive bias error in a calibration to zero by any method.
Lucia
Me:“More than geography.”
OK, I see better what is happening. But I think it would be less confusing if you merged 3 and 4, eliminating the P on the left. It doesn’t seem to me to have the meaning of a proxy value. That’s why I asked about D18O.
Nick–
You can’t eliminate the P on the right of 3. There is always a non-zero random component related to calibration uncertainty. Always no amount of anomalizing, shifting, shuffling around algebra can eliminate this.
Lucia,
I think I see a bit more. I don’t think your initial anomaly decomposition of T helps. If you combine 3 and 4 you have in effect
T_ij = t_i+P_j+W_ij
you can do a LS fit for t and P. This is what I do in TempLS.
You don’t have an explicit base period, and you probably won’t get a dimple. But you still have an arbitrary constant, because you can add any number to t and subtract from P.
Oh– I see what you mean by what you think would be ‘clearer’. You think it might have been clearer if I never discussed the actual magnitude of the proxies themselves. I think it helps clarify why the we really do need to Pmean,j term on the right hand side and I think its best to say something that emphasizes that the proxy values must– when you get right down to it– be related to real earth temperatures.
But if you prefer to skip that and just immediately write an equation for raw proxy calibrated temperatures, that’s fine. It makes no difference in the outcome.
Lucia,
“You think it might have been clearer if I never discussed the actual magnitude of the proxies themselves.”
Well, yes. You’ve assumed you know m. It’s the dame as if the proxies were just thermometers scaled in °F.
Lucia
Suggest including in your graphs each of the components of uncertainty shown on p 53 Figure D.2 — Graphical illustration of values, error, and uncertainty
Guide to the expression of uncertainty in measurement. JCGM 100:2008 Corrected version 2010.
While statistical Type A errors are generally covered, international guidelines recommend including Type B errors evaluated through scientific judgment. e.g., the effects of Inverting proxies, errors statistical models, contamination etc., etc., etc.
combined
Of course you can do an LS Fit. Ordinarily, for a proxy ‘j’ you have a set of Q temperature (or temperature anomalies) and proxy value pairs:: $latex (P_{j,k}, T_{k}) $ When you do the LS fit, you get parameters You’ll get a LS Fit of the fomr
$latex \displaystyle P_{j} = m_{j} T + b_{j} $
Then, if we assume the slope m is known perfectly ( which I have assumed here because it turns out not to matter to the problem that concerns us) the individual proxy values in
$latex (P_{j}, T_{k}) $
are $latex \displaystyle P_{j,k} = m_{j} T_{k} + b_{j} +W_{j,k} + V_{j} $
where the final two terms are ‘noise’ terms and describe scatter around the fit and the uncertainty in the intercept respectively.
You can relate $latex b_{j} +V_{j} $ to the $latex P_{j}(t_{i})/m $ in my equation. The exact form of the relation depends on whether you want to do the fit to temperature anomalies on a pre-selected baseline or whether you want to do the fit to the first and then rebaseline. I wrote out (4) generally so you can make the choice at a later step in the analysis.
I’m not sure what you are trying to say. My algebra assume an explicit base periods is selected so the math assumes the base period is explicit. Also, I do get a dimple in the standard deviation of the left hand side of (7) just as you and Marcot get a dimple in your equivalent of (7) and I get one for the same reason.
It’s that (7) doesn’t describe the same as (5) [ or (6) which is really the same thing)] and the standard deviation of the of the left hand side of that doesn’t have a dimple.
Nick, Thanks for your replies and code. One question from your reply: “On your R code, yes, I think it’s correct for calculating the anomalies for plotting. I think the Quenouille correction should have a sqrt.”
Yep, I left off the sqrt, which hit me this morning when I woke up. Still, it seems to me that the dimple is proportional to the Quenouille correction which may be coincidence or may be by-definition, but at first blush couldn’t that mean that the dimple is a failure to compensate fully?
Nick==
Actually, I haven’t assumed I know m. I’ve assumed m exists. There is a difference.
It’s similar to defining temperature anomalies for the earth. To define those you assume the earth temperature exists. You don’t need to know them. You certainly don’t need to know them to write down the variable in an algebraic relation.
Lucia,
If I follow your argument correctly (and I am not sure I do), then the presence of a dimple in the uncertainty limits strongly suggests that Marcott et al ignore the contribution of uncertainty in the calibration of the proxy to temperature, and so overstate the certainty (narrow the uncertainty limits) in the alkenone based reconstructed temperature. Do I have that right?
.
Steve Mc’s several posts on widespread ‘divergence’ between alkenone based temperature reconstructions and thermometer based estimates since the industrial revolution may make the entire question of Marcott’s hockey stick moot, especially if a specific cause for that divergence can be proven. My guess: greater availability of dissolved CO2 in surface water, due to rising atmospheric CO2, is mimicking the effect of lower water temperature on alkenone composition, since lower water temperature also increases dissolved CO2 at constant CO2 concentration in the atmosphere.
Nick: Is it possible to post on your blog? I’ve tried as Anonymous and as Name & URL, and in both cases what I post (or attempt to preview even) simply disappears. Here’s my question from your code:
In your Anomalize step, you calculate the mean for the baseline, “y=y-mean(y[-25:25+250])”, but I don’t see the SE of this mean (which will require a Quenouille correction because of correlation, I believe) saved or used elsewhere. I’ll have to admit I can’t follow all of the calculations in the next section, so maybe it’s in there, but it’s not obvious to me.
Any guidance on that?
Nick
ARGG!!
So, you mean the CI’s represent the spread in the difference between one reconstruction and an alternate one you might have obtained if you had different proxies.
Do you understand that this is not the confidence intervals for the difference between the reconstruction and the earth temperature you are trying to reconstruct? Do you understand that the two different things can have different magnitudes?
Please answer yes or no. And if you think they can’t have different magnitudes, explain why.
Because I keep asking you which they are because you don’t seem to understand there are two different things. The confidence intervals that describes [uncertainty in difference between what you want to measure(i.e. the earth temperature) and the estimate of what you want to measure] is more important than the confidence interval that describes [ the uncertainty in the difference individual estimates and the mean of all possible estimates].
Instead of diving into linear algebra, could you engage this point? Do you see that the two things are conceptually different?
Nick
I am talking time points. the baseline is a period of time.
Actually, I do find it challenging to explain this clearly. That’s why I tried to introduce the word “frozen”.
The problem with communicating T_i is that it has elements of ‘random’, but it is frozen from the point of view of computing the proxy.
What I mean is this: Suppose we have a shit wad of points in time and we pick a baseline. Ideally, these would be infinite, but I can’t do that
> N_tot=10000;
> numBaseline=3;
> baseline_rows=ceiling(N_tot/2) + seq( -floor(numBaseline/2),+floor(numBaseline/2));baseline_rows
[1] 4999 5000 5001
# create something to pick out rows outside baseline. throws an error but works.
not_baseline_rows=c(1:N_tot)!=baseline_rows;#not_baseline_rows;
Now I’m going to create temperatures:
> # create raw temperatures: Mean 0.
> T=rnorm(N_tot)
> # compute the baseline value.
> T_base=mean(T[baseline])
> # rebaseline the raw temperatures. These are now anomalies.
> T_rebaselined=T-T_base
>
> # The mean of anomlaies inside the baseline is 0.
> mean(T_rebaselined[baseline])
[1] 0
>
> # The mean outside the baseline can be compared to the baseline.
> # The will be very close and would be equal if N_tot->infinity.
> mean(T_rebaselined[not_baseline_rows]); T_base
[1] -0.3684584
[1] 0.3740359
With respect to this
All proxies reading the same temperature is a direct consequence of simplying the geometry. If there is only one point, and all proxies are measuring that point, and we are merely trying to reconstruct the temperature history of that point, then all proxies are responding to the same temperature. But because they are measurements, for various readings, the temperature recorded by the proxy differs from that at the point.
Their readings at time t_i provide information about the temperature at that single point at time t_i. The goal of the reconstruction is to determine that temperature at time t_i (and all the rest.) (Feel free to read that as temperture anomaly since that’s just a matter of shifting.)
That means they provide information about the thing we are trying to measure.
In equation (4). We could pull the constants out of 4 and put them in 3 if that’s what you prefer. Or we could split them all up assign some to (4) and some to (3). But that’s just a matter of organizing the equations. When you combine (3) and (4) — which is inevitable during the process of creating the reconstruction, the constants appear in the equation for the raw proxy calibrated temperature just as they must.
Re “simplifying out the geography”
Since anomalies are being compared, doesn’t that assume all locations vary by similar amounts?
The temperature gradients from the equator to the poles are not uniform, and they change with time / climate, thus invalidating that assumption.
e.g. see images temperature gradient
Doesn’t that raise the issue of how the variation in temperature gradient over time impacts the average temperature?
SteveF
Yes. I haven’t found a way to keep the dimple and not have ignored that contribution in the confidence intervals they place around their reconstruction. There might be a way and I may think of it over time.
I don’t know if that contribution is large or small, but I do know that I can only explore the effect if I don’t just set the term to zero before starting algebraic or numerical processing.
There is a sense in which the dimple can result in uncertainty being over or under estimated though.
No. The fact that I simplify to a point in my toy problem doesn’t raise any issue. It merely means this toy cannot be used to learn anything about hos that might affect the uncertainty in a reconstruction. Toys are intended to assume away the issues not under consideration and include those being considered.
David L. Hagen–
I have no idea how you wish me to use Figure D.2.
Lucia,
“No. The fact that I simplify to a point….”
.
This was answering David Hagen, I think, not me, though the questions are for sure related.
Hhhhmmm… Algebra error in (7). It’s updated. (I’m going to slap in some text. I might not look pretty!)
I concluded there are two types of correct measurement errors! So, Nicks are “right” and mine are “right”. The look different and plot differently. Both have some pesky properties inconvenient properties (specifically shared correlation in errors even in the toy problem where things are white noise.)
I’m not sure which one “works” better if we start having proxies that need to be patched or if we want to create a histogram of anomalies.
Wayne2 #112073
Sorry about the commenting trouble. I’m not sure what the problem is; there’s nothing in the spam filter.
You’re right that I’ve just used a OLS mean se.
Nick: “You’re right that I’ve just used a OLS mean se.”
I think I’m missing something, since that sentence doesn’t seem to be addressed to what I’m thinking about…
I’m saying that you have a time series (with some associated amount of uncertainty from its measurement/calculation) that is an input to the Anomalization Process. This time series is also auto-correlated.
You then take a portion of the time series, the baseline, and calculate its mean and subtract this mean from all points, creating an anomaly series. Three things I think of:
1. There is an SE associated with the mean of the baseline. The mean of your baseline has uncertainty associated with it, which is based on the SD of the baseline points. This SE will be inflated by a Quenouille correction because the time series is autocorrelated.
2. There is an uncertainty involved in the value of each point in the original time series, and this uncertainty needs to be carried forward.
3. Because of the autocorrelation of the time series — not just during the baseline but also outside of it — your baseline’s mean value will be correlated with the time series in a dimple shape: highly correlated with the baseline data and less so as you sweep your Anomalization across the time series away from the baseline.
It seems to me that the SD’s and CI’s of your Anomalized series has to account for all three of these points.
But in your calculations I can’t see that you carry them forward. That’s my question: am I not understanding the code and you are carrying them forward, or are you just throwing some of them away and only looking at variation between anomaly series (for each proxy), or perhaps something else?
And it seems to me that the dimple is an artifact of not carrying forward (or perhaps the term might be “compensating for”) some combination of #1 and #3, above.
Is this making any sense?
Wayne
Nick doesn’t need to do anything specific. This just falls out. The width of his bands are the uncertainty intervals for the left hand side of what I show with equation 8. The correlation you are discussing is the correlation in the noise terms W. Whatever that correlation is, it is.
If the noise was white, you’d get a a divot. If the noise has long term autocorrelation, it will sort of curve out smoothly. Nothing needs to be “done”.
David–
This is “A Toy”. What systematic effects? What incomplete definition? What remaning error? What systematic effects?
Lucia, OK, that’s the beauty of understanding the equations.
For my part, seeing that the amount of autocorrelation controls the depth and width of the divot makes me think that it’s a missed sliding-Quenouille-like-correction that’s leaving the divot. (That is, the CI isn’t actually going down in the divot, we’re simply not compensating for the effects of a couple levels of autocorrelation — the original time series with itself, and the anomaly time series with the baseline mean.) I’ll bang my head against the equations a bit more.
Wayne–
The confidence intervals for “the thing” the ones with divots apply to really truly have a divot or dimple in the center.
I said above that I’ve concluded that both Nick’s and my confidence intervals apply to measurement errors but they apply to them in different ways. They aren’t interchangable some are easier to use in some circumstances and not others.
One of the pesky things about Nicks “with divot” CI’s is that if the only information you have is those confidence intervals, you can never easy to compute the uncertainty in the change in temperature from time 1 to time 2 unless one point is inside the baseline and one outside. For all other cases, you have to back out the portion of the CI”s that is represents the confidence intervals for our estimate of the baseline temperature in the reconstruction. (This is related to the issue that causes the divot.)
One of the pesky things about mine is that if the term corresponding to uncertainty in the calibration of the proxies is large, you have to back that out when computing the uncertainty in the change in temperature from time 1 to time 2.
So they both have a pesky feature but which pesky feature is different.
Lucia,
“I said above that I’ve concluded that both Nick’s and my confidence intervals apply to measurement errors but they apply to them in different ways. They aren’t interchangable some are easier to use in some circumstances and not others. “
Yes, I agree with that. I’ve thought about it a bit with TempLS, which I think works like what you are doing, but with instrumental. You let the offsets associated with proxies be variables along with the desired temperature. You have a lot more equations than unknowns (not counting noise W), so there’s some sort of least squares solution.
But although there are many equations over i,j, there’s one short. You could always add a number to the T’s and subtract from the P’s. You need one more equation to pin that down. You could prescribe one of the T’s to be zero. Or the average over a period, including the total. And that’s equivalent to taking an anomaly.
But that way has a big advantage. It’s working on the aggregate, so you can choose an anomaly condition without worrying about whether all proxies have data.
I’m planning to run Marcott through TempLS some time today. The only delay is that TempLS is set up to deal with monthly variation, and I have to make a version without that. The result should be spike-free 🙂
Nick, “You could prescribe one of the T’s to be zero. Or the average over a period, including the total. And that’s equivalent to taking an anomaly.”
That makes more sense. The most recent proxy data point should be the one with the most accurate date and temperature unless the noted otherwise by the compiler.
Re: lucia (Apr 13 07:37),
(Lucia, your combined equation at the link is missing a set of parentheses before the division by $latex m $, FWIW…)
I’m wondering if my head-model of uncertainty is too complex, or if the measurement uncertainty discussed here is actually a simplification and minimization of reality.
I think my question is this: when discussing measurement error for various $latex T_rec $ of $latex T_true $, does that by definition include all forms of data, parameter and model uncertainty?
It seems to me that several assumptions may be hiding in the background, and I don’t know enough stats to state them clearly. Are we assuming truly random measurement error? Are we assuming zero or at least known, constant systemic error? Are we assuming models and parameters are 100% correct?
What I see when I step back and squint is a bunch of calculations relating to a large pile of data measurements that are assumed to have some real world relationship to temperature. Yet even my digital thermometer at home, while providing repeatable numbers in a test, is not guaranteed to provide consistent results within or between measurement sessions. It is +/- 2F, +/- at least one least-digit.
It seems to me that much of this discussion tosses all of that uncertainty away by going with whatever data numbers we happen to have pulled during our measurement sessions. And no I don’t think anomalies addresses this, because again, two measures both carry that same uncertainty, and subtracting one from the other doesn’t eliminate anything unless one assumes the uncertainties cancel out which seems a very dangerous assumption!
I hope you can address this in the course of this presentation. Thanks!
Hmmm… time for a $latex latex $ lesson. Chapter 3 here is helpful.
If super or subscript is more than one character, use braces T_{true} $latex T_{true} $.
+/- is \pm $latex A \pm B $
Pete
Nick’s got a nice post up on his TempLS method, and integrating Lucia’s error analysis method.
Re: lucia (Apr 14 09:57),
Now I better understand why it is a “toy” 🙂
Clearly, many proxies either are known to not fit this, or have unresolved “divergence”, and/or linearity is imposed via an empirical model which has poorly characterized uncertainties.
That’s being demonstrated for a growing number of proxies. I look forward to what Pat Frank and Paul Dennis are considering as a project in this regard.
As you say, $latex Pmean_j $ is “a” systemic error for a proxy. A nice simple constant. Good as a beginning point!
So am I understanding correctly that this implies, for this toy analysis, we are assuming things like a standard deviation that can be correctly calculated in the normal way, with sufficient sample size, normally (?) distributed population, with statistical independence between all samples (heh), etc…? They seem like very reasonable assumptions for a toy beginning analysis… hopefully nobody will take the toy and claim that this is a fully explicated analysis. Those assumptions (or anything remotely like them) are humongous, and light years away from reality…
I will repeat my caveat: I am only dangerous enough to look for things like this. I don’t know how to wield the weapons 😀
@Nick:
“The Earth is festooned with thermometers and satellites. So what was the true temperature for 2012. 12°C? 14°C?”
Absolute surface temperature has never been defined uniformly, ever. That’s why we use anomalies.
Re: Nick Stokes (Apr 13 18:13),
Nick, if you let offsets be variables, you’re probably doing something like what is known in statistics as random effects, which I’ve discussed from time to time at Climate Audit.
You would find it worthwhile to consult some of the texts as it looks to me like you may be re-inventing the wheel. tHERE are many useful diagnostics in the R random effects packages.
At one time, I’d implemented tree ring chronologies in random effects; also one of Hansen’s routines in random effects and had done this sort of exercise on Marcott. The data doesn’t meet the assumptions so it’s hard to tell what it means.
Steve,
Well, I googled for advice; Andrew Gelman told me not to worry, but cited my squash playing statistician colleague, Geoff Robinson, who had lots to say. So I’ll ask him.
But there is an underlying uncertainty. In my most recent implementation I used biglm. There’s a spurious dof in that formulation in that an arbitrary constant can be added to the time function and subtracted from the proxy offsets. That has to be resolved with some extra condition equivalent to anomaly setting.
So I found that when no intercept is specified, biglm gave me a sensible answer to the Marcott recon, with CI’s (se) similar to Marcott, and which I have found in other ways. But it had a big offset, which the anomaly condition takes care of. If I allowed an intercept, I got essentially the same numbers without the offset, which went into the intercept. But the se is about three times larger. I assume it includes some of the uncertainty of splitting that offset between the intercept and the coefficients.
I have been a little slow on the draw but in doing some simulations based on the Marcott proxy and reconstructions series , their Monte Carlo estimates of the CIs and RomanM’s critique, I think that as RomanM indicated the Marcott Monte Carlo is not very informative and in error. I think basically that the errors in the proxy to temperature calibrations are simply too large (standard deviations of 1.5 degrees C) to provide much useful information on variations in a reconstruction where 0.1 degrees are critical to the reconstruction conclusion. Roman concentrated on the Marcott calculation of the 2 proxy calibration error estimates but at the same time warned about the use of a linear extrapolation of the proxy temperatures.
In my simulations I can obtain the CIs Marcott found by assuming a calibration error of 1.5 degrees C for all proxies (which is close to a number of published errors and that calculated by RomanM for the alkenones), using a random proxy coverage of 11 years out of 1000 years of reconstruction per proxy for 73 proxies and putting data into 20 year bins by linearly extrapolating the scattered data points.
My first problem with the Marcott CI estimation is that the linear interpolation would appear to add points or degrees of freedom where there are none and thus produces deflated CIs. Using all the combined proxy points over the entire reconstruction time provide data points for about 70 percent of the years with a few years having multiple data points. If I were to take these combined proxy data points as coming from a single series and having a variance that is largely from the calibration error I would have a series with 95% CIs of +/- 3 degrees C.
If I had 73 proxies covering all the years and I took 20 year bins (without linear extrapolation) I should have a 95% CIs of (3/73^(1/2))/20^(1/2) and that is essentially what I got with a Monte Carlo simulation. If you do the linear extrapolation of 11 points per proxy for each 1000 years for 73 proxies you obtain a higher number for the CIs. That higher number must be related to artificial variance produced by putting extended trends in the series from linear extrapolation. It becomes from this exercise clear why Marcott was able to state that his CI calculations are insensitive to the size of the bins: the extrapolation effect was large compared to the differences in average more or less data points from the series.
Without extrapolation and using 20 year bins I obtain a series sd=0.039 from a Monte Carlo which is in perfect agreement with the calculated value.
Without extrapolation and using 10 year bins I obtain a series sd=0.054 from a Monte Carlo which is again in perfect agreement with the calculated value.
With a linear extrapolation and using 20 year bins I obtain a series sd=0.23.
With a linear extrapolation and using 10 year bins I obtain a series sd=0.24.
Kenneth F,
” (standard deviations of 1.5 degrees C)”
Have you checked that yourself? It’s a number that comes mostly from Roman’s bogus E term. But in any case, it would largely subtract out after taking anomalies.
I agree that the apparent creation of dof by interpolation is a problem. It’s OK for the mean, but creates highly autocorrelated noise.
Nick
On Clive Best’s analysis – http://clivebest.com/blog/?p=4857 – he gets SEs larger than the Marcott SEs too , but without the use of monte carlo simulations and interpolations.
Nick:
It’s a bit ironic and perhaps even silly that a term *you* don’t understand the purpose of is “bogus.”
All I’m saying.
Nick Stokes (Comment #112127)
Please go through the arithmetic in showing how a measurement uncertainty (calibration/measurement error) will subtract out in an anomaly. The error is not in the same direction or of the same scale at each data point. Subtracting a constant from each data point leaves the same differences between data points.
The literature indicates that most of the marine proxies are going to have a calibration and measurement error in the neighborhood of one standard deviation of 1.0 to 1.7 degrees C.
http://home.badc.rl.ac.uk/mjuckes/mitrie_files/docs/mitrie_sediment_marine.pdf
“The standard error of the SST estimate using the surface sediment calibration is about 1 to 1.5ºC. In some
cases, the method may be limited due to the lack of sufficient organic material contained in the sediments.”
http://doi.pangaea.de/10.1594/PANGAEA.67009
“Using our North Atlantic data set, we have produced multivariate temperature calibrations incorporating all major features of the alkenone and alkenoate data set. Predicted temperatures using multivariate calibrations are largely unbiased, with a standard error of approximately ±1°C over the entire data range. In contrast, simpler calibration models cannot adequately incorporate regional diversity and nonlinear trends with temperature. Our results indicate that calibrations based upon single variables, such as Uk37, can be strongly biased by unknown systematic errors arising from natural variability in the biosynthetic response of the source organisms to growth temperature. Multivariate temperature calibration can be expected to give more precise estimates of Integrated Production Temperatures (IPT) in the sedimentary record over a wider range of paleoenvironmental conditions, when derived using a calibration data set incorporating a similar range of natural variability in biosynthetic response.”
http://www.ldeo.columbia.edu/~peter/Resources/Seminar/readings/Herbert_AlkReview_Treatise%2701.pdf
“In any event, the third-order polynomial fit of water-column U37 to in situ temperatures improves the r2 value to 0.97 as compared to the r2 value of 0.96 for a linear fit, and reduces the standard error of estimate from 1.4 degrees C to 1.2 degrees C.”
From the Marcott SI we have:
“c. TEX86 – We applied the calibration suggested by the original authors and the uncertainty from the global core top calibration of Kim et al. (13) (± 1.7°C, 1σ).
d. Chironomids – We used the average root mean squared error (± 1.7°C, 1σ) from six studies (70-75) and treated it as the 1σ uncertainty for all of the temperature measurements.
e. Pollen – The uncertainty follows Seppä et al. (53) (± 1.0°C) and was treated as 1σ.”
Diogenes,
Yes, his uncertainties are larger, but not hugely. I commented at one stage that interpolation is the right thing to do in terms of calculating the mean. Otherwise the proxies that report infrequently are greatly underweighted.
However, I think something does have to be done about the effect on uncertainty. As KF noted, the interpolates aren’t independent variables. The uncertainty imputed to them is about right in magnitude, but it’s highly correlated.
In a way, Clive understates the effect on CI, because of the low weight he assigns to the proxies that create the problem.
I’m writing a post on this.
Carrick,
“All I’m saying.”
Well, a little more. You must have used published regression-derived calibrations many times, with uncertainties in slope and intercept. Have you ever found it necessary to add in an extra term based on the spread of the original experimenter’s residuals?
Kenneth,
Assuming that you use the same calibration formula for all time for the proxy sequence, then the intercept will subtract out. You subtract its average over the base period (it’s constant) and it’s gone. The same is true for the slope uncertainty multiplied by the mean temp. There’s not much left.
Nick
Uhmm.. in application? Sure. It depends what one is trying to estimate.
Nick, I would and do.
Suppose you have two sources of measurement error in temperature, one of these is due to high-frequency measurement noise (e.g., shot-noise in a thermistor) and the second is an offset calibration error in measurement,so like RomanM’s “E” this is an error source that is (approximately) constant through out the measurements. One model would be:
$latex T_{measured} = T_{true} + \epsilon_1 + \epsilon_2$.
I’d include both errors when reporting results, but report them as separate errors. One convention is:
$latex T \pm \sigma_1 \pm \sigma_2$.
I’d call the first error source “random error” and the second “systematic error”.
For a laboratory measurement, we can usually read $latex \sigma_2$ off of a chart. RomanM is using Müller. For Marcott’s case, $latex \sigma_2$ corresponds to the measurement error associated with the quantity $latex T(t) – T_{baseline}(t)$.
What I wouldn’t do is including the systematic error in the uncertainty interval intended to show time varying effects. If I’m interpreting Clive’s work correctly, is what he’s (erroneously) done. [$latex \sigma_2$ just moves the curve up and down. ]
And of course this is still wrong:
This is a case of you not knowing that you don’t know, and we do know that you don’t know. This is where I see the irony here. At the least be a bit circumspect when you are tilting at wind mills.
And that was plenty more than I was planning on saying.
Carrick,
“econd is an offset calibration error in measurement,so like RomanM’s “E—
That’s not what Roman’s E is. He already has a calibration slope and intercept error. He says that E is a neasure of the experimenter’s spread of residuals.
It’s like an original sin. The calibration people could do a zillion experiments, get the regression coefficient errors down to almost nothing. But of course, their residuals don’t go to zero. Nor does E – in fact it barely improves as they do more experiments.
Anyway, I’d really like to see that table you read from that has the errors in the two coefficients and then something independent as well.
“And of course this is still wrong:”
Wrong? It’s just arithmetic. The intercept of the calibration formula is constant, even if uncertain. Subtract its average, over any range, and it’s gone.
Nick, the calibration/measurement error is applied to each and every data point in the reconstruction. There is nothing in that error that is constant and thus would cancel on anomalizing. An uncertainty of +/- 3 degrees C for calibration/measurement is applied to each data point. If there were a constant in that uncertainty it would not be an uncertainty.
If you think you are correct it would be easy for you to show what is constant in the uncertainty.
Kenneth,
I don’t believe Marcott et al did that. Lines 48-50 of the SH:
“For each Mg/Ca record we applied the calibration that was used by the original authors. The uncertainty was added to the “A†and “B†coefficients (1s “a†and “bâ€) following a random draw from a normal distribution.”
Line 22 “This study includes 73 records…”
It seems very odd to me to change the calibration for each time step. Do you have some reference for your claim?
Nick Stokes (Comment #112141)
Each data point has a measurement error and that error is applied in my Monte Carlo simulations by using a normal distribution with an sd=1.5. Who said anything about changing the calibration? Did you read my post where I gave links to references on the measurement error attributed to these proxies? If Marcott’s calculations use a significantly smaller measurement error for Mg/Ca and alkenones proxies he is going against the literature.
Nick,
The Mg/Ca ratio has to be determined for each slice in the core. There is a random error associated with that determination that is independent of the calibration error for Mg/Ca vs T. Unless you use the entire slice for the determination, there’s sampling error for the aliquot of the slice you use. Then there’s the precision and accuracy of the determination itself. If it’s done by ICP-OES, it’s extremely difficult to achieve precision and accuracy better than 1% for each element and then you take the ratio. Think of it as reading between the lines of a liquid in glass thermometer. Even if the calibration error is zero and it’s perfectly linear, there’s still a measurement error for individual readings that doesn’t go away when you convert to anomaly. And you don’t get to take multiple readings and average them.
DeWitt,
Of course there is measurement error, and would be if you didn’t have to worry about calibration. What I haven’t seen is anyone with concrete examples of Roman’s E, where you add in an error term from whoever did the calibration (extra to the regression coefficient uncertainties). The measurement error in recons like Marcott’s is included in the estimate from the variation of different proxies reporting what is supposed to be the same thing.
Kenneth,
Yes, I did look at your first link in detail – it was quite informative. But in that section you quoted from, they said:
“The precision (±1 std) of the temperature determination is better than 0.3ºC.”
and later
“The standard error of the SST estimate using the surface sediment calibration is about 1 to 1.5ºC.”
Now I think it’s pretty clear that the first is a reference to the calibration, and the second includes all the other issues that arise in relating to SST (drift, core issues, reservoir effect estimation etc). In fact, in the second, I think they must be referring to the scatter of multiple experiments, like the proxies of Marcott.
If Marcott has included the variation of his own proxies in the CI’s, then it would not make sense to include someone else’s. It’s true that what you quoted suggests that he used such a figure for some of the less common ones like TEX86. Perhaps regression coef errors were unavailable. But Roman is saying that he didn’t for UK37.
Nick, your argument is that the 0.05 error in UK37 measurements is fully captured in the errors in the slope/constant of the regression? Let’s test that.
err = function() { rnorm(1,mean=0,sd=1) }
uk37temp = function(uk, Ea=err(), Eb=err(), Em=err()) {
((uk + (0.050*Em)) – (0.044 + (0.016*Ea))) / (0.033 + (0.001*Eb));
}
No measurement error:
> sd(sapply(rep(0.4351,100000),uk37temp,Em=0))
[1] 0.605281
No regression error:
> sd(sapply(rep(0.4351,100000),uk37temp,Ea=0,Eb=0))
[1] 1.517146
All errors:
> sd(sapply(rep(0.4351,100000),uk37temp))
[1] 1.633726
mt,
No, that’s not my argument. My argument is that the regression coefficients, with their uncertainty, tell us all that they can about the dependence of UK37 on T. Of course it will vary with other things, some deemed random, So there will be a larger total error in any given set of experiments.
My argument is that .05 represents those other errors in Muller’s experiments. The corresponding errors in Marcott’s data would be captured by the between proxy variation, to which the temperature calibration uncertainty only should be added.
As I’ve said above and elsewhere, that depends on your interpretation of what Marcott actually did in steps 5 and 6. The description suggests that they included Monte Carlo variation in their sd, and ignored the between proxy variation. For that to work, they would indeed have to provide a measurement error from somewhere else. Else they could have included the total sum of squares from the two stages, which would include between proxy variation. Then any other estimate of measurement error would be redundant.
I had convinced myself that the latter is what they did, on the basis of some quantitative reasons. I’m less convinced now, partly because as KF noted, they have included total variation of Tex 86 etc, which would be inconsistent, and partly because interpretation 2 gives trouble with proper treatment of interpolation, which version 1 mostly avoids.
Nick Stokes (Comment #112135)
April 16th, 2013 at 7:00 pm
“However, I think something does have to be done about the effect on uncertainty. As KF noted, the interpolates aren’t independent variables.The uncertainty imputed to them is about right in magnitude, but it’s highly correlated.”
Nick, as I previously pointed out with my own Monte Carlo results, the interpolation does not only create degrees of freedom where there are none but it also puts an artifact into the CI calculation whereby the lengthy trends it puts into the series can overwhelm the variabilty reduction expected from the bin size used. Marcott points out the insensitivity of CIs computed to bin size he just did not understand what caused it.
“The uncertainty imputed to them is about right in magnitude, but it’s highly correlated.”
That just a nice way of saying that Marcott committed an elementary error of averaging data and using it as independent. It should never get to the point of an autocorrelation correction.
You say that something should be done about the Marcott calculation and interpolation. What would you suggest?
I don’t think Nick is fairly representing RomanM’s arguments. RomanM can defend himself if he sees fit, but—being more realistic than me—he probably won’t.
Again the fundamental problem Nick is having is in the definition of measurement error. It’s defined in terms of the difference between the measured and the true value of the quantity.
Using measurement variability to estimate the error only captures the portion of the measurement error associated with the response of the proxy to the external driver. It doesn’t tell you anything about how the mean of an unlimited set of measurements deviates from the true temperature, which I would call systematic error.
I admit I haven’t looked at Müller to see if RomanM is interpreting him properly, but this is a red herring on Nick’s part. The question is whether you need to include “E” or not, and I believe you do.
I’ll give an example from my discipline.
Suppose I take a of measurement of the response of a microphone to broad band noise. I can estimate the spectrum of the signal by splitting the signal into a series of windows, compute the discrete Fourier transform for each window, then look at the variability between windows to get an estimate of the internal noise in the measurement with frequency.
However, that ignores the fact that the sensor doesn’t uniformly respond with frequency. To correct for this I need to measure the transfer function, which is the ratio of the output signal to the input signal.
To estimate this, I introduce a second “standard” microphone and take simultaneous measurements with the same noise field. By taking the ratio of the “test” microphone compared to the standard, I can produce an estimate of the frequency response of the microphone.
This transfer function is a measure of the systematic error associated with the non-uniform frequency response of the sensor.
Because it’s a systematic effect, I can correct for it (equalize the sensor response).
What happens to my error bars when I do this? If the errors are associated with e.g. electronic noise instrumentation amplifier), when I scale the sensor response to produce a flat response with frequency, my uncertainty ends up scaling too in the region where the sensor response is non-uniform… in exactly the way that RomanM described with his error term.
By the way there are other systematic corrections I haven’t brought up. Some of these can be measured accurately, others can only be estimated or bounded. In the case of bounded error, you get an additional inflation of uncertainty that varies with frequency.
Note however that the systematic error typically varies smoothly with frequency (has no “peaks”). So if you wanted to estimate the likelihood that a particular spectral peak is not noise, by comparing against neighboring frequencies, you don’t just add the errors in quadrature to estimate this. Typically you only need to look at measurement variability to determine that. (And that’s the objection I have with folding in this other error source in a plot of proxy reconstructed temperature with time…this gives an unrealistic portrayal of the uncertainty that e.g., 1950 is warmer than 1650.)
Beyond that, in this argument:
Nick is still conflating obtaining zero central value with zero uncertainty. This underlines that his fundamental problem is in the definition of measurement error as the difference between a measurement (or series of measurements) and the true value of a quantity. That the error doesn’t vanish (unlike the central value in this case), is just algebra plus the proper definition of measurement error.
You’d think Nick would have asked his squash buddy for advise by now.
Kenneth F,
I’ve been rethinking a few things here. As you’ll see from my previous post, I’m giving more credence to the possibility that Marcott did do as he seems to say in steps 5 and 6. And looking carefully at his description of his method, I think he got the interpolation issue right, wrt the 20 yr binning. But maybe not with the date points.
It’s a point of order. He does the perturbation of data points in steps 1 and 2, then the interpolation in step 3. So he never actually perturbs an interpolated point from a distribution. Those points inherit their variation from the data perturbations; this is carried through to step 6, and then the resulting variation is observed in summing over the 1000. This should work out right.
There is an analogous problem with the date points. There are only a few of them; the age models change, as do then the dates of data points. He shows sd’s for these, and so I suspect these are treated as independently perturbed.
Nick, Carrick, et al: One approach is to ask how the analysis would have turned out if: a) Muller had been able to sample an “infinitely” large number of sites before constructing his calibration curve or b) researchers applying Muller’s calibration to their core samples could measure lipid ratios an “infinitely” large number of times.
In the case of foraminifera, which can be growth under reproducible conditions in a laboratory, a single organism can be analyzed and the amount of dO18 incorporated into each organism is slight different. One can’t reduce the gap between the curved 95% confidence intervals beyond a certain point no matter how many sample one analyzes and how carefully the analysis is done. The situation in the field is even worse because laboratory experiments show dO18 incorporation also changes with the salinity of the growth medium, light and the O18 in the water, all factors that could vary in the field. The same is presumably true for alkenone proxies; there is an innately variable relationship between temperature and lipid unsaturation. When one moves from the lab to the ocean, the number of uncontrolled variables in this relationship increases (especially horizontal drift), widening the 95% confidence interval. Muller’s calibration curve was constructed in the field, so it should include all sources of variability (present today).
If you ignore the uncertainty in the y-intercept, you appear to be replacing the proper curved 95% confidence intervals around the linear regression with confidence intervals that are straight lines with different slopes, going through a single point. This can’t be right.
This looks reasonable: y = ax + b +/- E
This looks reasonable: y = (a+/-da)x + (b+/-db)
This looks wrong: y = (a+/-da)x + (b+/-db) + E
This looks reasonable: x = [(y+/-dy) – (b+/-db)]/(a+/-da)
This looks reasonable: x = [(y+/-dy) – b -/+ E]/a
where E comes from the residuals of the calibration curve AND dy is the uncertainty when measuring alkenone ratios in core samples.
Carrick,
I think the problem is that E has been described as a calibration issue. It isn’t. It may have a role as an estimate of the scatter of data points (“measurement error”) if you choose not to use the internally observed values. If the majority interpretation of Marcott’s statement of method is correct, that’s what they did.
One issue about measurement error is, what are you measuring and why? The figures KF has quoted are the errors in estimating SST. But it’s not clear to me why that is relevant (we don’t even seem to know, SST where? And that may be a good part of the uncertainty, but in fact we don’t care). With surface temp, for example, we use SST as a proxy for air temp. There’s systematic error there, but we don’t attempt to estimate it. We proceed on the basis that the anomaly in SST represents the anomaly in SAT, and use it directly in estimating what we are really trying to measure, which is global mean anomaly.
To put it another way, we want to relate core readings to global SAT. There are systematic errors between core and local SST, and then systematic errors between local SST and global. If you estimate from within-model variation, you get the lot. If you just use SST error, you only get part.
“You’d think Nick would have asked his squash buddy for advise by now.”
Ah, I’m emeritus now. I go in Fridays. I’ll see him today.
Frank,
“This looks reasonable: y = ax + b +/- E
This looks reasonable: y = (a+/-da)x + (b+/-db)”
But they are inconsistent. As you say, with infinite replications, da and db go to zero. But E doesn’t change.
I think the association of E with calibration has been unhelpful.
Nick, see if you can get your squash buddy to look at the problem (e.g., RomanM’s post), without prejudicing him. Maybe just say you weren’t clear where “E” came from…
There’s the question of the relevance of the form, then there’s a question about the execution.
I also think there’s no question that you need multiple error terms that sum when you are trying to Monte Carlo data. One error term for each error source. The only question is whether RomanM’s analysis is an improvement or not.
I think there is no question that Marcott’s dimple is an error. I think he just didn’t notice that feature or he would have corrected it himself. These things happen.
My interest in seeing the dimple artifact was piqued so I asked Lucia what she thought & so we have this post. Hopefully she’ll get the follow-up posts published soon.
Carrick,
“Nick, see if you can get your squash buddy to look at the problem “
I went in to the office today and found he was away for another fortnight – so it will take a while.
Marcott’s dimple is a consequence of his anomaly definition – there’s even an analytic form here (for Ar(1)).
The dimple in uncertainty is a consequence of Marcott’s erroneous uncertainty calculation. Nobody disputes the variance is smaller during the baseline period (not even James Hansen, if you remember that paper).
Getting the uncertainty error computed correctly was why I asked Lucia for her opinion on this.
Here’s my prediction:
I expect Marcott will not defend the dimple in uncertainty, now that the wart in his results has been pointed out to him. (That there is a dimple doesn’t change very much, so it’s a “wart”.)
The measurement error in the Marcott CI calculations is critical to the result- given that it had been correctly performed – and that error is the uncertainty that is to be applied to every data point/measurement and from whatever source.
In order to get a better idea of the magnitude of that uncertainty I used the 6 pairs of proxies from the Marcott reconstruction and assumed that, since those pairs are coincidentally located, the temperatures should be the same. Given that assumption I took difference of the millennial means for each pair for millenniums BP 1 through 12 and retained 54 differences that met the criteria of having at least 3 readings for the millennium and over 500 years difference between the maximum and minimum dates for the proxy data points.
I then did a Monte Carlo on a simulation of the randomly selected data points from a 1000 point series assuming a normal distribution with various standard deviations (which represented the measurement error) and a mean=0. I finally binned the results for the observed and Monte Carlo result that fell into 5 bins corresponding to the Monte Carlo probabilities. I then did a chi square test comparing the bin counts. I find, using in the Monte Carlo, 5 or 10 data points per millennium and standard deviations from 0.5 to 2.0, that indeed a standard deviation around 1.5 provided the best chi square fit.
Reply to Nick Stokes (Comment #112162)
da and db absolutely do not go to zero if one uses an infinite number of samples to develop a calibration curve. That’s like saying that the standard deviation of a sample shrinks as more replicates are run, when it’s the standard deviation of the mean that shrinks. There is an inherent variability in the relationship between temperature and alkenone ratios that can’t be reduced by increasing the number of samples. The 95% confidence interval for the linear regression is analogous to 2 standard deviations about the mean.
Frank (Comment #112176)
“da and db absolutely do not go to zero if one uses an infinite number of samples to develop a calibration curve. That’s like saying that the standard deviation of a sample shrinks as more replicates are run, when it’s the standard deviation of the mean that shrinks.”
Yes, it is like saying that, because they are means. Weighted means for slope, but they have the same property that the error reduces roughly as the square root of sample size. Yes, there is inherent variability; the function of the regression is to separate that from the temperature dependence, which it does with increasing success as sample size increases.
Nick Stokes (Comment #112177)
As you use more samples to improve the accuracy of your calibration curve, the uncertainty in the coefficients a and b improves, just like the uncertainty in the mean improves. But when 95% confidence intervals for the REGRESSION that are placed around a linear regression with y = (a+da)x + (b+db), da and db do not indefinitely shrink with the number of samples, just like the standard deviation of a population doesn’t shrink as you test more samples from that population. (More samples give you a better idea about the population mean and the population standard deviation, but they do not make the population standard deviation approach zero. If the first few samples are tight, more samples can increase your estimate of the population standard deviation.) da and bb are NOT confidence intervals for the coefficients a and b, they are the “standard deviation” in the relationship between x and y. If you have a large number of points, 5% of them will be expected to lie inside the 95% confidence interval and 5% would lie outside.
I have done some more iterations with my Monte Carlo simulations of the Marcott 6 coincidentally located proxies using various measurement errors for the paired proxies. The chi square test scores in comparing the observed and simulated probabilities of the occurrence of differences between millennial means for paired proxies showed that the best scores were attained when one of the paired proxies had a 1 standard deviation measurement error of 1.5 degrees C and the other an error of 2.0 degrees C for 1 standard deviation. I assumed the average coverage for the proxies was 10 data points per millennium.
@Frank: Is this something like the difference between a Confidence Interval and a Tolerance Interval? (http://en.wikipedia.org/wiki/Tolerance_interval)
“The tolerance interval differs from a confidence interval in that the confidence interval bounds a single-valued population parameter (the mean or the variance, for example) with some confidence, while the tolerance interval bounds the range of data values that includes a specific proportion of the population. Whereas a confidence interval’s size is entirely due to sampling error, and will approach a zero-width interval at the true population parameter as sample size increases, a tolerance interval’s size is due partly to sampling error and partly to actual variance in the population, and will approach the population’s probability interval as sample size increases.”
In my previous calculations I have neglected the effects on variation of randomly drawing temperatures from a millennium period of time from a time trending temperature series that is located in the ocean and has a time averaged sample covering 10 years. In order to determine what these effects might be I took a the differences between 2 simulated the millennial means of two time series with a sd= 0.11 which I assumed approximated an ocean location for a sample time average over 10 years and a mean=0 with a millennial trends of 0.3 for one Monte Carlo run and 0.6 degrees C per millennium for another Monte Carlo run.
The 95% CIs were +/-0.12 and +/-0.17 degrees C respectively for 0.3 and 0.6 degree C millennial trends, respectively. While not negligible, these variations are small compared to estimated measurements errors.
I find it interesting that Marcott failed to address directly these issues I have raised here.
Very late to the tea party, but it is important to nail down that the Earth does not have a single temperature in any meaningful way. You can set out procedures for calculating a parameter you call the Earth’s temperature, but that is a) not unique no matter what it is and b) often not very useful. Anomalies, OTOH, are better constrained.
See Essex and McKitrick for comments on why this is the case, but ignore them on how to construct a useful anomaly. Because anomalies require a baseline you run into Nick’s take on things
Eli, do you really believe this statement that the temperature is “not unique no matter what it is “? You’re sounding like a WUWT’er now.
$latex \bar T(t) = {1\over S} \int_\theta \int_\varphi T(t, \theta,\varphi) r^2 d\theta d\varphi$,
where $latex T(t, \theta, \varphi)$ is the absolute temperature on the surface of the Earth, a theoretically well defined quantity.
Not only is it unique and well defined, it relates to quantities like $latex \sigma T^4(t)$, so the error in not knowing the absolute temperature of the Earth even has direct experimental consequences.
Nobody argues that if you are trying to understand how the time series varies over time that it’s important to anomalize it. The issue is you don’t get reduced uncertainty in the baseline period when you do. (The dimple in uncertainty is an error in Marcott’s methodology, albeit not an important one.)
Eli:
That is very interesting. If there is no single global temperature which can be computed, then how does that impact the determination of climate sensitivity.
It is my understanding that CS is the delta T based on a change in forcing – which requires computing the global temperature at two different times and subtracting them.
Are you saying that is is therefore impossible to compute CS?
Or that CS is not meaningful?
Eli,
Tea party? Odd reference.
.
Like Carrick shows, the average surface temperature most certainly does exist and is calculable, and lots of climate scientists have invested a fair amount of time and treasure doing those calculations. Of course, if it is not useful, then such a calculated number ought not have been used to frighten the public about global warming, right?
.
Sounds like Eli is positioning himself to deal with the continued slow pace of warming with a “that’s not what really matters” argument (lemme guess… you will find other ‘catastrophic’ things which you claim do matter). You are mistaken: the trend in average surface temperature does matter, and preposterous statements like your are not going to change that. Climate sensitivity is lower than the climate models predict, and all the consequent risks of warming are comparably lower. I suggest you get ahead of the stampede and start your climb-down.
SteveF,
“Like Carrick shows, the average surface temperature most certainly does exist and is calculable, and lots of climate scientists have invested a fair amount of time and treasure doing those calculations. “
Carrick has written down a Latex expression. But I don’t believe that CS’s have invested in those calculations. As I kept wearily asking above, what’s the numerical result?
Again, here are scientists from GISS and NOAA explaining why they don’t do it.
“Carrick has written down a Latex expression. But I don’t believe that CS’s have invested in those calculations. As I kept wearily asking above, what’s the numerical result?”
durr..
equation 1
http://www.scitechnol.com/GIGS/GIGS-1-103.pdf
numerical result for the land is in the paper.
Nick Stokes,
” But I don’t believe that CS’s have invested in those calculations.”
.
I would be more than a bit amused if I thought that you were only joking, but I don’t think you are. I’m not sure what you imagine the several published historical trends of ‘global average surface temperature’ are supposed to represent if not… well, the historical trend in average surface temperature. One can always count on Nick to step in and defend nonsensical rubbish like “there is no average surface temperature” when that sort of statement is made in defense of climate models which make incorrect predictions of high climate sensitivity. You should probably start your climb-down too.
Steven,
“numerical result for the land is in the paper”
Well, well, so it is:
“temperature average during the most recent decade (Jan 2000 to Dec 2009) was 10.183 ± 0.047°C, an increase of 0.893 ±0.063°C.”
But as you say, land only. Still no global figure. Still waiting…
And that brings a big issue. Carrick writes down a space integral of T and says it is “theoretically well-defined”. But again, no definition; maybe it’s existence is also theoretical. Pushed for a definition, I suppose it would be something like “average min/max air T at 5 ft above surface”. But what about the ocean – where’s the surface? And on land at least, the 5 ft is important.
I don’t know why no-one seems to have looked at the GISS/NOAA links – it sets it out very clearly. Climate scientists compute average anomalies, not temperatures. For very good reasons, which they explain.
The trend in the “global average surface temperature” does not care about the absolute temperature of the individual sites or of the earth, and the various temperature series (HadCRUT, GISTEMP, NOAA) are expressed as a weighted mean of anomalies. i.e. They are expressions of temperature change, not absolute temperatures.
Climate scientists have not invested much time, money or effort calculating “global average surface temperature” because it is of little value to them (read those links). If BEST thinks it has a good result, more power to them, but there are no names of climate scientists on that paper. I’m particularly interested in seeing that calculation when they eventually add SST, which doesn’t even measure SAT.
Nick, cce,
The fact the the calculations are based on anomalies from a base period does not change what the trends are trying to measure: the trend in global average surface temperature. Sure, there are reasons for using anomalies rather than absolute temperatures, but that makes no practical difference in the resulting trend…. a trend which is designed to accurately convey how the globally averaged surface temperature changes over time. Add an assumed absolute average temperature for the base period to the trend in anomalies and you have the globally averaged absolute surface temperature trend. A distinction without a meaningful difference.
Nick,
I don’t understand this nihilistic antagonism to absolute temperatures. Yes, it is true that one can measure temperature differences (anomalies) with more precision than the absolute temperature; this will be so whenever the measurement uncertainty is more due to bias than to random error. But to say that absolute temperatures are not computed, is to ignore files like this or this.
Or consider the top panel on AR5 WG1 Fig9.8A, which shows the unfortunate fact that the average surface temperature of models differs over a range of 2 K. And yes, it matters to models, unless they also anomalize physical constants such as the phase transition points of water inter alia.
SteveF, HaroldW,
We’re just going around in circles. Yes, you can identify trends in anomaly with trend in temperature. And differences too. And yes. models can compute average temperatures. They don’t have 5 foot above the surface sorts of issues.
But SteveF said “the average surface temperature most certainly does exist and is calculableâ€
and the fact is that it is not calculated (except from models). And the elementary proof is, no-one can produce a measured number.
The relevance is to the argument above is the objection that dimples meant that the “real CI†wasn’t being calculated. But if you can’t measure the average temperature, you can’t find a CI for it. But you can find a CI for the anomaly.
Re: Nick Stokes (Apr 23 05:30),
And we’re back to square one again. The problem is still that the CI for the anomaly may lead to an incorrect conclusion about the true variability of the surface temperature.
Nick, ““temperature average during the most recent decade (Jan 2000 to Dec 2009) was 10.183 ± 0.047°C, an increase of 0.893 ±0.063°C.—
That sounds almost too good to be true. The “surface” temperature record also has a dimple, actually, dimples depending on the source.
I have noticed of late that much of the analyses of well-publicized papers, such as Marcott et al, tend to get off into areas that almost appear niggling and particularly when compared to analysis issues that can have a far greater impact on the conclusions of the paper. All observers can readily see that the Marcott dimple in the CIs is an artifact of anomaly baseline period and that fact has to be taken into account when viewing CIs on anomalies. Why does this discussion here have to continue in a lawyerly fashion?
The bigger issues here are the overwhelmingly large uncertainties presented by the measurement errors, the Marcott Monte Carlo where the degrees of freedom are inflated by using linear interpolations, the artifact in uncertainty that placing long trends in the series through interpolation and the effects of time averaging on the marine sediment samples measured for the proxies in the Marcott reconstruction.
Nick:
The uncertainty in the absolute temperature is higher, which is why you look at the relative temperature for studying the time course of temperature series, since the common (correlated) error subtracts out. That’s understandable from measurement theory too.
Of course it’s been measured, and is necessary to measure, otherwise you can’t compare climate models that contain nonlinearities with the reconstructed temperature series.
Anyway, if you really understood the foundations of empirical science, you’d understand that all that is needed is the demonstration that the quantity can be related to a theoretical one, not whether that the measurement of that quantity comes on top in some bizarre popularity contest.
You don’t even have to “look” at a physical quantity for it to exist. Presumably physical measurables are present before humans invent the language to describe them and the methods to measure them.
The fact I can write down an equation that has an exact interpretation tells you the quantity is well-defined. That’s what “well-defined” means. (Well defined though doesn’t always mean “easy to measure”.)
“Climate scientists compute average anomalies, not temperatures. For very good reasons, which they explain.”
I’ve read those and found they are rubbish. let’s have a look
‘Why use temperature anomalies (departure from average) and not absolute temperature measurements?
Absolute estimates of global average surface temperature are difficult to compile for several reasons. Some regions have few temperature measurement stations (e.g., the Sahara Desert) and interpolation must be made over large, data-sparse regions. In mountainous areas, most observations come from the inhabited valleys, so the effect of elevation on a region’s average temperature must be considered as well.
########
Anomalies do not help you with spatially sparse data in any way shape or form. Neither do they help you with not sampling at high altitude. Titivihey help you when you decide to use certain methods ( like CAM or RSM) which are sensitive to things like station drop out. One always needs to interpolate working with anomalies doesnt make that easier and the altitude effect is well understood. For example we explain 95% of the variance in temperature by fitting the temperature to altitude and latitude. So they are talking gibberish.
Carrick
That can’t be true. You are just being silly.
The better view is to believe that temperature did not exist before thermometry was invented. Similarly, food calories did not exist prior to the invention of the bomb calorimeter. Weight also did not exist until after the invention of scales. Also, I’m not speeding if my speedometer is broken and a cop isn’t there to measure the speed of my car. As you can see, I am so totally with Nick on this one. 😉
Neo-Berkeleyianism? Esse est mensurati.
Nick,
How is the difficulty in making a measurement proof of impossibility of anything? Your take on all this is very strange to those who actually make measurements.
I have linked a histogram showing the proxy data point coverage for the baseline period used in Marcott for producing anomalies. The coverage is very sparse for most of the proxies and I am wondering what that means in terms of producing a meaningful mean for calculating anomalies. Of course this is a major disadvantage of using anomalies in that a common period that is reasonably well covered is required.
The time averaging of the samples used in calculating proxy temperatures could work to the advantage of Marcott here but none of these features of sparseness or time averaging by Marcott is discussed in any detail in the paper. I am wondering if anyone in the media is sufficiently well-prepared to ask these questions. Andrew Revkin comes to mind with his elevator interview, but I think he might depend a bit too much on tutoring from the RC crowd.
http://imageshack.us/a/img708/5220/marcottproxycoveragebas.png
Lucia, your reply came across a little like Valley Girl and remember to be is to be perceived.
Kenneth–
I don’t often resort to irony in comments. Loss of tone of voice sometimes makes it difficult to tell that irony is being used.
It would be one thing if Nick merely said those are confidence intervals for anomalies relative to that particular time and that applying them to find those confidence interval for any other question is rather complicated (which it is), but to say things like
“Carrick writes down a space integral of T and says it is “theoretically well-definedâ€. But again, no definition; maybe it’s existence is also theoretical. Pushed for a definition, I suppose it would be something like “average min/max air T at 5 ft above surfaceâ€. But what about the ocean – where’s the surface? And on land at least, the 5 ft is important.”
Carrick’s integral is a definition. Claiming it’s no definition merely shows that Nick doesn’t recognize a definition when he sees one. If he wants to quibble about whether Carrick means 5ft above some particular level– that exact same issue applies to anomalies. After all: the change in temperature 5ft above the surface is different from that 1000 ft above the surface and so on. With respect to demanding precise definitions, using anomalies doesn’t help.
The fact is: temperature anomalies cannot be defined if absolute temperature is not defined. Similarly, gauge pressure could not exist unless absolute pressure at least exists. This would be true even if there were practical difficulties making it very difficult or impossible to measure absolute pressure while it was possible to measure pressure differences. (For example: if manometers had been invented but baraometers had not been invented, that would not make the concept of ‘absolute pressure’ ill defined. The magnitude would still affect the local boiling point of water, density of gases so on.)
If any hypothetical problem with the definition of temperature of the earth on an absolute scale meant that earth temperature did not exist, or was undefined, that would mean anomalies also would not exist and would also be undefined.
As for Eli’s this ” it is important to nail down that the Earth does not have a single temperature in any meaningful way.” The earth obviously doesn’t have a ‘single’ temperature. But it can have an average over some extent, time or volume and that average is a single value. Language being what it is people will sometimes take the short cut of calling that “surface temperature”. But complaining about that is focusing on semantics. (And it’s niggling because most people know what is being claimed in context.)
In any case, any objection that the earth doesn’t have a “single” temperature can applies equally well to anomalies and absolute temperatures. Using anomalies are sometimes convenient; sometimes they are not convenient. That’s pretty much sizes it up.
With respect to computing and thinking about uncertainty intervals: if you start you refuse to introduce the existence of the earth temperature in absolute units into the analysis, you are likely to ultimately mis-use your uncertainty intervals and apply the to cases where they don’t apply. For some specific situations those intervals will be meaningful. But if you tweak the problem and you may need to extend your analysis to figure out how to fix things up to account for some feature of interest.
SteveF:
Yes, that one makes one’s head hurt.
I can get how a measurement noob might think the errors go to zero when you subtract numbers (we covered this error in reasoning in my first semester physics lab course), but it’s pure gobbledygook to try and argue that because a measurement is (slightly more) difficult to obtain, that implies nobody does it, or it can’t be done.
Lucia’s tongue in cheek comment looks perfectly valid compared to that.
I think both you and I understand the value of subtracting off a common offset when performing a calculation. One version of this is “dc subtraction” (usually the dc offset is just discarded of course).
So if all you want to do is dispose of a constant offset, just center the data before analyzing it. Simple.
If you go through the effort of anomalizing, it’s because you are specially trying to retain information about the original scale.
That is, in subtracting the measured mean temperature from 1960 to 1980, you are trying to link the residual series to the actual temperature over the period 1960 to 1980.
Otherwise by definition you aren’t referencing back to a measurable quantity, so why not just center the data and be done?
Lucia, that is a good comment, including the note about the limits of irony in technical blogs. 😀
The theoretical definition of surface (air) temperature that people decide upon depends on what we are trying to measure and how that relates to theoretical quantities.
Opposite to what lay people think, if you say something relates to a theoretical quantity, that means it is of practical use (in e.g. constraining models). Quantities that don’t directly test theories (in the broadest sense of the use of that word) are useless.
Hansen has a bit of a discussion on this, including touching on absolute temperature (but he gets a bit of it wrong, you don’t need a climatological model to compute absolute temperature from the unanomalized temperature data).
“Carrick’s integral is a definition. Claiming it’s no definition merely shows that Nick doesn’t recognize a definition when he sees one. If he wants to quibble about whether Carrick means 5ft above some particular level– that exact same issue applies to anomalies.”
Actually, it isn’t a definition. It is a surface integral of a 3D quantity. How the third dimension is to be treated is unspecified. It actually looks to me as if he meant to write a volume integral in 3D spherical but left off the dr (but included the r^2). Hard to tell, though, because S is also undefined.
But the same issue applies much less to anomalies. That’s the point of them. The temperature is different 1 ft above ground; the anomaly much less so.
People (even here) don’t seem to mind comparing anomalies in the lower trop (satellite) to surface. They match rather well. But the temperatures are very different.
Steven,
“Anomalies do not help you with spatially sparse data in any way shape or form. “
They do. They do not have rapid spatial variation. So you can hope to numerically evaluate the integrals that Carrick wants. With temperature you can’t, because you can’t possibly sample on the scale required to resolve the variability.
Kenneth, the comments you make relate to the fixed-base line anomalization method.
I suggest looking at how BEST has done it, which involves the bootstrapping method and has a nice approach for error estimation, and doesn’t rely on all series have a common overlap period. It’s a bit of overkill for instrumentation temperature reconstructions, but I think this framework could be very useful in proxy studies.
To give you a bit of where I’m going with this, consider that most correlational reconstructions use a period like 1900-1950 for “calibrating” their proxies. The reason for this, as I understand it, is the lack of good proxies that go from e.g. 1950-2000.
The problem with this method is you are mooring all of you data around a very poorly understood temperature series (relatively speaking) that is quite noisy relative to 1950-2000, and inversion procedures such as proxy temperature reconstructions amplify noise.
The big questions for me are a) how big is the offset bias outside of the calibration period in the reconstructed series and b) is the post 1950-divergence problem that we all “know” is the proxies diverging (leading to the risible defense that it’s okay to not show the data after they diverge).
I say this because if you actually look at the raw proxies post 1950, most of them have a positive trend, not a negative one, and it’s only the behavior of a few outliers that get an excessive weight that makes the series negative for this period.
Specifically, most of the tree-ring proxies used by Mann in his 2008 paper actually don’t diverge.
Figure.
Trusting fools we are for thinking Mann could get his methodology correct enough that, if a problem arose, it had to be in the raw data and not in his Rube- Goldbergesque methodology.
(And this is why you show all of the data, and why withholding adverse results is so problematic.)
Nick
I have no idea why you think “S” is undefined. I guess Carrick could add words there. Where “S” is the surface of an envelope ‘n ft’ above the solid/air or liquid/air interface. If that’s you issue, with respect to a definition you need it both for anomalies and for absolute temperatures. So presumably, that’s not your issue with respect to a definition.
This has nothing to do with whether temperature is defined. If the temperature 1 ft above the ground is not defined then the temperture anomaly 1 ft above the ground is also not defined.
I have absolutely no idea why you would think Carrick might have meant to type in a volume integral when (a) we are mostly discussing the global means surface temperature which is an area integral (b) Carrick wrote down a perfectly good surface integral and (c) defining an surface integral using a volume intergral would have just been wrong while (d) defining it with an area integral– which is what he did is perfectly right.
A surface integral is a surface integral. The r^2 is contained in there because the surface area of a sphere is is greater for a sphere with a larger diameter. r^2dr is in a volume integral… cause… area*length is a volume. The fact that r^2 appears in both doesn’t make including it in an area integral confusing!
Anyway: the earth’s surface temperature is a surface integral over a defined sruface. That definition is complete in itself. The fact that volume integrals can also exist doesn’t make an area average “not an definition”.
Oh bollocks. We are discussing a definition not the magnitude of the uncertainty one might achieve when the perfectly well defined quantity is measured. Whatever you perceive as being a problem with a definition applies to anomalies just as much as it applies to absolute temperature.
If you just want to advocate for use of anomalies– fine. Everyone agrees they can be convenient in some instances. But you need to stop trying to suggest the non-anomaly values are somehow not defined or not measureable. If the anomalies are defined and can be measured, the absolutes are at least defined. In the case of earth temperatures, they can also be measured and you can apply uncertainties to any measurements. Sometimes one way of looking at the problem is useful; sometimes another is. But forgetting or denying that the absolute temperature during the baseline periods exists is just silly.
Kenneth F #112208),
You can reasonably quantify the problem. When you take an anomaly, with iid residuals you increase the sd of most points by sqrt(1+1/N) where N is the number of data points in the anomaly base period.
I don’t think the date uncertainty smoothing helps much.
Nick,
Utter rubbish. Using anomalies does not “help” with the non-problem you raise for rapid spacial variation; each anomalization is just subtracting an average value from a specified base period from the individual measured data points. No information in the measured data is added or lost. Good grief, sometimes I think you just like to argue about minutiae.
“I have no idea why you think “S†is undefined.”
Simple. There are no words defining it. None.
Maybe it means Earth surface area. Then at least there should be a 4π in the numerator.
Maybe T is well-defined as surface temperature. Usually people speak of surface air temperature, which has a 3D aspect, but is something we can relate to. But surface temperature? The bitumen in the sun? Every leaf? And the sea – let’s not go there. Well, OK, maybe it is theoretically well defined.
Nick– No. He’s giving an example. I would assume he’s whatever surface he’s using, his intention is to match the surface you use in your temperature anomalies. If you have never defined that surface then your anomalies are undefined. If you have defined that surface, Carrick’ would be the same dang surface you use in your definition for anomalies.
Don’t try to go on about how your numerical values are not as sensitive to the precise location of the surface. Don’t go on about surfaces of leaves or lack of knowledge of the air-water interface Either you have defined the surface on which your anomalies are computed or you have not. If yours is defined so is Carrick’s. Because his is the exact same surface as the one you use.
So you give us the words you have provided to define your surface, and then we can just cut and paste those into Carrick’s definition. Then it’s done. As far as I can see any lack of definition is shared by your anomalies and Carricks absolute temperature. Why you cannot see this is a mystery beyond measure. Or it’s just Nick Stokes. Hard to say.
SteveF,
“Using anomalies does not “help†with the non-problem you raise for rapid spacial variation;”
It does. I’ve mentioned the rather remarkable fact that station temps and LT sat temps can be usefully compared once you take anomalies. Here is an anomaly map of stations last December. It’s a color map based solely on station anomalies (not averaged; there is triangle shading between stations). You can see smooth patterns extending over many hundreds of kilometres. The network of stations we have has reasonable resolution on this scale. It would be hopeless for resolving actual temperature.
Re: Nick Stokes (Apr 23 15:21),
Seriously? The π comes from the integral over φ from 0-2π
What’s actually seems to be missing is a sin(θ) term in the integral. Include that with a constant r and you get the surface area of a sphere.
Nick
Uhmmm…. If you scroll down, you will find the example integration on this page: http://www.9math.com/book/surface-integral-spherical-coordinates
Nick–
In your answer to SteveF, you persist in confusing whether a quantity is defined and measurable with whether it is easy to measure. Defined and measureable are terms of art. Neither means “easy to measure”. If the surface temperature was not defined or if it was not measureable, it couldn’t be computed from simulation data. That is: You couldn’t report the absolute values of temperature averaged over a surface from GISS Model EH or any other GCM. But they do report those.
Lucia
“Uhmmm….”
DeWitt has it right. With the sin term, which is correct, you don’t need the 4π.
Lucia,
“So you give us the words you have provided to define your surface, and then we can just cut and paste those into Carrick’s definition.”
Well, I don’t particularly need to. As I said, I’d get much the same answer using sat lower troposphere anomaly. That’s an elastic notion of surface.
But I do give attention to how to calculate the surface integral. Sparse example here. The key thing is that the nodal values should be representative for the element. And if that depended on, say, 5ft above the surface, then that should go into the definition. But it doesn’t.
DeWitt:
Oops, good catch.
I was going to write $dS(r(\theta, \varphi),\theta, \varphi)$, then ended up dumbing it down to the point it was wrong.
For geophysical applications, $\theta$ is usually latitude, going from $latex -\pi/2$ to $latex \pi/2$. With that convention, the Jacobian is $ r^2 \cos\theta$.
Okay, assuming no more brain farts, this is the corrected formula for a sphere (canceling out the $latex r^2$):
$latex \bar T(t) = {1\over 4 \pi} \int_{0}^{2\pi} d\,\varphi \int_{-\pi/2}^{\pi/2} T(t) \cos\theta.$
Geometrically, the average of a function on a given surface is just give by the integral over the surface of that function divided by the area of the surface. This average is of course a well defined quantity as long as the function is smoothly varying (as any physical variable such temperature is going to be), regardless of the practicability of directly measuring the quantity.
Bloody hell.. third try and hopefully no phone call in the middle this time:
$latex \bar T(t) = {1\over 4 \pi} \int_0^{2\pi} d\varphi \int_{-\pi/2}^{\pi/2} d\theta\; T(\varphi, \theta, t) \cos \theta.$
(Missing the $latex d\theta$ term and the arguments for T.)
Nick:
Actually it can make a huge difference in measured daytime temperature swings, but the difference for trend in mean temperature isn’t thought to be important relative to the measurement uncertainty for looking at monthly-averaged global mean temperature.
In other words, where it is defined, and how precise the definition is, depends on application—Lucia’s point.
Lower tropospheric temperature is enough different (e.g. above the boundary layer) that significant differences can be seen in e.g., ENSO temperature swings, so the range where “nothing you do matters” is pretty narrow, even for large scale, long time period phenomena.
Nick
This is nonesense. If you are arguing about whether or not what you are measuring is defined you need to be able to state the definition. Whether the numerical result is sensitive to a change of 1 ft in the definition is irrelevant. Either you’ve defined it or you haven’t. If you don’t define it because you think you don’t need to then you haven’t defined it.
It’s difficult to understand what part of this you don’t get.
If you think that’s sufficient definition to define the location surface, then just apply that definition to the specification of Carrick’s surface and be done with it. That now “is” “the” surface.
Lucia,
“This is nonesense. If you are arguing about whether or not what you are measuring is defined you need to be able to state the definition.”
Well, Carrick didn’t, and for absolute temp, he needs to. But OK, I’m happy to stick with an air surface 5 ft above ground, and an average of top 5 m at sea (or whatever engine intakes measure now)..
The various global temperature analyses are trying to measure the amount of warming or cooling of the Earth’s surface. They are not trying to estimate the absolute temperature of the surface of the earth. The former is a useful metric and is relatively easy to calculate and understand. The latter is not very useful and is very difficult to calculate and has no agreed upon definition. That’s what the climate scientists believe.
It may be easy to come up with a “theoretically well defined” solution, but that won’t get you an accurate value for the real, non-theoretical surface of the earth. For example, a third of the land surface is covered by forest. Weather stations are (or are at least supposed to be) out in the open. If you don’t correct for those differences, you are going to get a very poor representation of the temperature of a third of the land surface. But you will get a much better answer if you are interested in warming or cooling, in which case a weather station in a nearby clearing will provide a good (but not perfect) proxy for temperature change under the forest canopy. Likewise, SST is a good (not perfect) proxy for temperature change above the ocean surface.
Now, I’m not very good at math but I don’t see why the accuracy of temperature measurements and proxies (i.e. the presence of systematic bias) is important if we are interested in temperature change. If planet Tau Alpha C imposes a 100 quatloo fee to open a brokerage account, but planet Ceti Alpha 5 gives you 50 shares of the Noh-Jay Consortium just for opening an account, what does any of this have to do with the stock price of the Noh-Jay Consortium? On Tau Alpha C you have spent 100 quatloos and you own zero shares (a systematic funding bias). On Ceti Alpha 5 you have spent 0 quatloos and yet possess 50 shares (a systematic share bias). But if you invest 25 quatloos and the number of shares increases by 1, another 25 quatloos give you another share, and another 25 quatloos gives you yet another share, you know that a change in quatloos is a proxy for a change in shares. That is, additional shares of the Noh-Jay Consortium will cost you 25 quatloos per share regardless of your starting point. The biases on the two planets are irrelevent.
Nick
My points are:
a) You haven’t either.
b) And for anomalies you need to do so just as much as Carrick needs to for absolute temperatures.
If you haven’t defined something, you haven’t defined it. This idea you have that somehow not defining “doesn’t matter” is just silly.
The fact that any measurement would represent an approximation of the theoretical thing applies both to measurements of absolute and anomaly. So snide remarks about engine intakes not being located on the defined surface isn’t going to change that either. And no– your previous link showing how you create your estimate does not substitute for an actual definition. If that method of computing was the definition of the quantity you were trying to compute, Climate modelers would compute that temperature average from model data and report it.
Re: cce (Apr 24 00:22),
As was pointed out somewhere above, absolute temperature is important for climate because, for one, the phase diagram of water is defined as a function of absolute temperature, not temperature anomaly. That’s why it should be disturbing that different climate models produce global average temperatures that vary by more than 2K between models. If the absolute temperature is wrong, the water vapor pressure will also be wrong. If the water vapor pressure is wrong, calculated atmospheric emission/absorption will wrong too.
DeWitt 112233 (cool comment number 😉
Yes, that is a good point. I guess the ocean surface temperature is less problematic than land temperatures in the sense that the ocean surface temperature ought to strongly influence the rate of evaporation over the ocean, while evaporation from the land surface is a more complex function of temperature.
Lucia, I hope you do not think I did not get the irony of your reply. I got it – totally. I was attempting to use HaroldW’s: “Neo-Berkeleyianism? Esse est mensurati.” in my observation.
My Latin is nonexistent but when I figured out that mensurati refers to measurement I got the gist of Harold’s remark – totally.
Carrick, I am aware of the BEST applications that avoid using anomalies and I think it is a step forward. With BEST using many short series they could not possibly have found a common baseline for producing anomalies and thus in their case it was a necessity to do something else. Anomalies require a period of overlap with a reasonable amount of coverage. I have not gone through the simulation required to determine for the Marcott reconstruction what the uncertainty of the mean used in an anomaly does to the anomaly variations between proxies.
Kenneth–
I assumed you got it. I think Valley Girls often resort to irony.
I’m more concerned with whether they used proper anomalies to make comparisons between current temperatures and those inside the reconstruction. Their histogram shows the current temperature as a discrete line with no uncertainty band around it and then shows a histogram of temperatures in the Holocene. I do know that any comparison of current temperatures to histograms of temperature through out the entire holocene needs error bars that apply to that and the image strikes me as odd. So, for example, merely tallying up hte histogram of temperatures in their reconstruction would be wrong, padding it with error bars for the amomalies relative to the baseline would be incorrect also. But I have not looked into this issue to see if they added the extra uncertainty to account for comparing the thermometer record to the reconstruction.
Nick Stokes April 23rd, 2013 at 3:07 pm
“You can reasonably quantify the problem. When you take an anomaly, with iid residuals you increase the sd of most points by sqrt(1+1/N) where N is the number of data points in the anomaly base period.
I don’t think the date uncertainty smoothing helps much.”
The time averaging I was referring to in my post above was not the dating uncertainty but rather the sample measured actually representing multiple years. In that way a single measurement actually gives a multiple year average which by itself would give a better estimate of the mean temperature during the base line period.
Unfortunately in the Marcott reconstruction case the measurement errors overwhelm the year to year temperature variations expected in these samples. Marcott freely notes this in explaining the basis of his Monte Carlo.
I would have more confidence in using a Monte Carlo approach in determining the effect of the means uncertainty on the anomaly uncertainties. If I think this through I would expect the mean to bias the anomalies of the 73 individual proxies. When getting a feel for the proxy CIs by I looking at the millennial mean differences between the six pairs of coincidently located proxies in the Marcott reconstruction, I could and did use the absolute temperatures. Now I am thinking that added uncertainity will arise from using anomalies given the sparseness of data points to estimate the mean for the base line period.
Kenneth Fritsch (#112235) –
I have no more Latin than you. I made a stab at “mensurati” from the English word mensuration; but if it’s actually the correct word it would be merely a wild stroke of luck. I just hoped people would puzzle out its intended meaning, as you did.
Nick, as usual, we define quantities in a manner that improves the reproducibility, reduces the effects of local effects and improves the ability to model it.
For surface air temperature, around 1-5m is optimal for technical reasons that I can summarize if needed. Briefly you need to stay in the surface boundary layer of the planetary boundary layer, so above the interstitial layer but below the mixed layer.
People define things more precisely when it affects outcome. Here it doesn’t.
DeWitt, good point on water vapor and absolute temperature.
• Based on empirical studies, the minimum absolute surface sea temperature for hurricane genesis is 26.5°C.
• Convective storm activity is also a strong function of temperature.
• Modeling evaporation rate in summer, a third (important for drought modeling).
I suspect the list gets long indeed when you include biological impacts.
cce, I’d avoid conflating James Hansen’s comments, driven no doubt in part by the limitations of GISTEMP, with those of the rest of the community.
Of course absolute (radiometric) surface temperature is measurable:
Nice image.
The idea that you could estimate the surface integral for (radiometric) surface temperature for the Earth using this data product isn’t particularly a radical one. Nor is the idea you can relate this to a (vertically and horizontally weighted) measure of near-surface air (thermodynamic) temperature.
With a tad bit of work, Nick could generate this sort of figure himself with his data viewer.
As Nick himself pointed out, the exact definition isn’t very important, because the outcome is insensitive to the particulars. This can be understood in terms of convective overturn time, which is in seconds for the surface boundary layer, versus measurement interval, which is typically in minutes or hours.
I wouldn’t spend much energy on the argument that absolute temperature isn’t measurable or not important, personally.
My browser has stopped remembering the id and email fields for reasons unknown. Anyway:
Carrick,
The fact that we don’t have a good handle on the absolute global temperature field is precisely why, from a metrological viewpoint, current measurements are not fit-for-purpose for climate change measurement. But they’re all we have, so we have to make do. Note that that applies in spades to non-instrumental proxy measurements of past temperatures.
DeWitt–
It turns out the supercache plugin rolled out a quick emergency owing to a very dangerous vulnerability. The glitches began when I activated the new one. I’m guessing there is some weirdness in the emergency update. (Hopefully no new vulnerability.)
Carrick,
You are confusing skeptics’ pre-occupation with absolute temperature with the relative disinterest of the “community.” If their goal was absolute temperatures, their series would be expressed in absolute temperatures. Then they wouldn’t have to continually answer questions about base periods or why the Arctic is so red.
If you want an idea of the importance that these guys put on absolute temperatures, this is what HadCRUT gives you: “It is possible to develop an absolute temperature series for any area selected, using the absolute file, and then add this to a regional average in anomalies calculated from the gridded data. If for example a regional average is required, users should calculate a time series in anomalies, then average the absolute file for the same region then add the average derived to each of the values in the time series. Do NOT add the absolute values to every grid box in each monthly field and then calculate large-scale averages.” Not exactly turn key, not exactly global, and not exactly accurate.
You can certainly come up with a method that combines a bunch of numbers together that will give you something in the ballpark (HadCRUT provides numbers in the 1999 paper). And someone could use a different but equally “well defined” method and come up with a different number. And those numbers would be separated by differences that would take decades to accumulate if we were comparing different methods of measuring the change in temperature.
As for your image, if you launched an identical satellite and applied the same math, it would give you a picture that looked equally pretty with the same spatial patterns, but the numerical values would be different. Witness the difference in absolute values provided by the various MSU/AMSU instruments.
Re: cce (Apr 24 23:31),
You continue to miss the point. Anomalies are better for detecting change given the low quality of the past instrumental data. But GCM’s don’t model the climate using anomalies. By converting model absolute temperatures to anomalies, the modelers are able to mask how bad their models really are. No wonder the “community” doesn’t make absolute temperatures their goal.
Another reason that people list for anomalizing is to remove the seasonal component. With a sparse network of sensors this reduces the amount of internal noise in the global average, and is desirable.
However, you can subtract off a zero-mean baseline average, which preserves the absolute scale of the data.
As I mention, BEST used a different (improved IMO) method than common-baseline anomalization. However, they also choose to leave in the offset, showed the measurement error (excluding the offset uncertainty), and just quoted the offset uncertainty in the legend.
This is pretty much exactly what I would do too.
They claim an offset uncertainty of ±0.12°C, which is considerably smaller than the number Hansen quotes (which I think was picked out of a hat in any case).
BEST Figure 1 w/ caption.
The IPCC AR4 also has a plot of absolute temperature, see here. Unfortunately no error bars were provided.
Since the data seem relatively constrained, it would be interesting to see a comparison of individual models to data, where less has been swept under the rug than was performed in the AR4 discussion. (Link here.)
cce:
This is a pretty myopic viewpoint on your part.
I think you’re confusing my interest in metrological (not meteorological) issues with climate debate nonsense. I understand fully why the errors shown don’t fold in absolute uncertainties when plotting anomaly curve, as well as the real purposes of anomalization.
I will assure you the reasons scientists do this has little to do with “continually answer[ing] questions” about why the poles are colder than the equator. If for no other reason, most of them don’t answer any questions from contrarians, let alone are forced to do so continuously.
Carrick,
Since the data seem relatively constrained, it would be interesting to see a comparison of individual models to data, where less has been swept under the rug than was performed in the AR4 discussion. (Link here.)
Check the supplementary material for chapter 8.
I think climate scientists must use transparent rugs given all the things that are supposedly swept under them while remaining in plain sight.
Paul S–
You can’t just say because the supplental materials exist things aren’t swept under the rug.
I’ve read the supplemental materials for Chapter 8 and discussed them. I’d characterize handling and discussions in Chapter 8 “swept under the rug”. Choice of figures, language etc. all make it rather difficult for someone to see just how poorly the models agree with data and how much they disagree with each other and so on.
I would be surprised if the AR5 is any better. Maybe I’ll be pleasantly surprised.
Lucia:
Yes, that was rather my thought too. They were very careful about how they prepared the text on this to minimize the actual level of disagreement between models.
With respect to “hidden in plain sightâ€, I agree with the “hidden†part.
I have been cataloguing the climate model global monthly temperature data for the CMIP5 from KNMI Climate Explorer and characterizing the models with ARMA. I then compare the models to the observed temperatures from HadCRUT, GISS, NCDC, UAH and RSS. The temperature series all used a 1981-2010 baseline for producing anomalies. Currently, I have been primarily interested in looking at the noise of the modeled and observed temperatures and next want to analyze these temperatures as linear segment trends as defined by breakpoints.
I have found that generally the noise in the models is rather consistent with ARMA(1,2) or ARMA(1,1), with the (1,2) most often barely favored by the AIC score, and with a seasonal component with ARMA(1,1). The observed temperatures are consistent with an ARMA(1,1) and ARMA(1,2) model with the (1,1) model almost always favored by the AIC score. The observed series contain, like the models, a seasonal component best fit to an ARMA(1,1). The models tend to have a higher auto correlation than the observed series in both the main and seasonal components.
The models tend to show the structure of the observed temperatures in the instrumental period part of the series and then tend in the future time periods to have little of the observed series structure but instead have rather smooth linearly orientated upward trends.
The anomalies did not remove the seasonal component of either the modeled or observed series.
Also I have read that modelers often intentionally add stochastic features to the models in order to move away from a strictly deterministically looking series. The noise of the models does appear to approach that of the observed series with the exception that it is more auto correlated.
To me at this point in my analysis I see the model results when graphed as appearing as something indicating a simple superposition of red noise on some rather straight forward deterministic trends of various shapes.
Eli, as a practitioner, has always had his doubts about bomb calorimeter measurements, and therefore, taking Lucia’s sage advice from now on will ignore the issue of calories no matter the gentle hints from Ms. Rabett.
On the other hand, having touched this off, he will point to what he said above
“You can set out procedures for calculating a parameter you call the Earth’s temperature, but that is a) not unique no matter what it is and b) often not very useful. Anomalies, OTOH, are better constrained.”
This entire discussion appears to have verified the truth of a and b.
Carrick set out a procedure, but it certainly was not unique. For example why not average over T^4? The seasonal issue is also a killer in such an average over the earth unless you do local averaging by either comparing temperature during the same yearly times first, e.g. getting an anomaly (See here for an example)
Eli
This is nonesense. With respect to “uniqueness” what is the claim that the earth’s temperature is not unique even supposed to mean?!
If it’s supposed to mean the earth is not in thermodynamic equilibrium or steady state: Uhmm… no. But that’s not “non-uniqueness”. If it’s supposed to mean the temperature of the earth is not spatially invariant.. uhmm… no. But both those issues apply to anomalies. And more over, neither interfere with the definition of “Temperature” whether absolute or anomolized. So it sounds like someone is trying to make some sort of profound but meaningless statement which can’t be rebutted because the statement has zero information content.
Why not define the anomalie based on T^4 relative to the baseline T^4? Answer: One could define an average of T^4 if one wished. And one could do exactly the same for anomalies defining the ‘anomolous’ T^4 value. That one may chose one defintion rather than another only means that we have flexibility. If, for some problem, it is convenient to use an average over one thing rather than another, people will use that. Both can be carried along in a field. This fact does not detract from the utility of anything.
If you are joining in with Nick to explain that sometimes, for some problems of interest and for some applications, anomalies are convenient: Everyone agrees with that.
But the fact that anomalies (like say, gauge pressure) are sometimes convenient doesn’t make them somehow more fundamental, real, better defined or suggest the non-existance of absolute temperature (or absolute pressure). Repeating a statement about anomalies everyone agrees with in a tone that suggests that somehow that observation in anyway touches the one people are disagreeing about is just silly. The fact that anomalies are sometimes convenient is utterly irrelevant to whether or not ‘absolute temperature’ of the earth exists, is measureable (which does not mean ‘easy to measure’) and it is absolutely irrelevant to whether anomalies can be defined if absolute temperature cannot be defined.
The fact is: Anomalies cannot be defined if absolute temperature cannot be defined. This is just a simple fact.
Re: Eli Rabett (Apr 29 07:35),
You realize that you and Nick are very close to channeling Gerlich and Tscheuschner, here:
No one here, AFAICT, disputes that anomalies aren’t better constrained. However, KT97 and TFK09 both assign an absolute average effective surface temperature by assigning a value to the average surface IR emission. You can’t do that with anomalies. You also have a much harder time proving a greenhouse effect exists at all with anomalies instead of absolute temperatures. See G&T again.
Lucia,
“Anomalies cannot be defined if absolute temperature cannot be defined. This is just a simple fact.”
Defining is the easy part. The next question is, can you quantify it?
You invite people to risk their precious quatloos based on knowledge of the global anomaly for April. And some, not Eli to be sure, are prepared to risk it. But I think we’ve established that none of them know what the global absolute average temperature was.
DeWitt,
“You also have a much harder time proving a greenhouse effect exists at all with anomalies instead of absolute temperatures.”
There’s no dispute about the existence of absolute surface air temperatures. Met offices report them. The question is whether you can usefully compile a global average. That has nothing to do with the existence of a greenhouse effect.
You’re probably right that the best chance we have is measuring average IR emission to space in some atmospheric window frequencies. But that’s not quite surface air temperature.
For reference, KT97 in DeWitt’s comment is Kielh & Trenberth 1997, Earth’s Annual Global Mean Energy Budget
TFK09 is Trenberth, Fasullo and Kielh 2009 Earth’s Global Energy Budget
Off topic but maybe of interest: http://www.climatedialogue.org/long-term-persistence-and-trend-significance/
A forthright exchange of technical views between three scientists on a contentious climate topic… the influence of long term persistence on the statistical significance of climate trends.
Essex and McKitrick, who were clueless about what an anomaly was, how to calculate it, and what it told you, what it meant to measure a temperature at any location and frankly non-equilibrium thermo appears to have moved on. Other than that, it was an ok paper:)
Eli, it is also possible for somebody to know how to calculate an anomaly without understanding what it actually represents.
(The belief you can reduce the uncertainty of a physically measured quantity to zero by an appropriate algebraic transformation is a tip-off.)
SteveF (Comment #112307)
SteveF, I read that blog exchange and still remain uncertain how one can characterize the instrumental period as having LTP. Data of 150 years of which at least the early have must be suspect I do not think is sufficiently long to say anything about temperature having LTP. I’ll have to follow up on one of the discussants implications that spectral analysis can show LTP over relatively short time periods. These discussions get a bit hazy when the discussants do not account for an intervening deterministic trend and the longer term cyclical patterns in the temperature record.
I do think that some so called temperature proxies are of sufficient length to show LTP and I believe some do, but that does not mean that the proxies are a faithful indicators of temperature and that thus, in turn, temperature has LTP.
I suppose if one were to model climate without external factors that would place deterministic trends in the series and use a sufficiently long periods of time one could make a valid search for LTP in temperature. That exercise would require an assumption that models have it essentially correct on temperature. Also how does the repeating glacier episodes and the Milankovitch theory fit into all this – and chaos theory.
I use ARMA models of temperature series, both from observed and modeled. The model fitting seems to simulate well what I see in these series and would appear to make some practical sense over the shorter term and particularly if one bothers to initially linearly segment the series at breakpoints and detrend it.
Kenneth,
I think a fair (and interesting) conclusion you can draw from the discussion is that separating potential LTP effects from a trend due to ‘external’ influences is very difficult to do. This fact calls into question the claimed certainty in many ‘attribution’ studies in climate science, since these inevitably are based on a set of assumptions… one of which is no LTP.
.
I found the long term records of Nile river level particularly persuasive for at least the possibility of LTP effects; changes in river level are both large and persistent over many centuries where human influence on the climate was much smaller than today.
.
The apparent ~60 year cycle in the global temperature trend, the PDO, and AMO cycle, among others, all seem to support, if not LTP, then processes which are important, long term, and clearly not included in climate models. I think Demetris Koutsoyiannis is trying to point out that a great deal of climate data (not ‘modeled reanalysis data’!) is perfectly consistent with LTP, and that many of the estimates of uncertainty in climate science are therefore wildly optimistic, since they discount the possibility of contributions from LTP.
SteveF (Comment #112312)
May 1st, 2013 at 10:45 am
“I think a fair (and interesting) conclusion you can draw from the discussion is that separating potential LTP effects from a trend due to ‘external’ influences is very difficult to do. This fact calls into question the claimed certainty in many ‘attribution’ studies in climate science, since these inevitably are based on a set of assumptions… one of which is no LTP.”
I agree that looking at shorter term series with a trend could be confused with a longer term series that has LTP, or, for that matter, an ARMA modeled series which can also produce rather lengthy trends in a series. A deterministic trend has to have a physically based causation, and while we know that GHGs will put deterministic trends into the temperature series, because of the uncertainty of the effects of feedbacks we do not have a hard and fast number. Maybe the spectral analysis magic one of the discussants was referring to will clarify some of these issues.
I am sure that we have many different deterministic and stochastic effects operating on the temperature, but sometimes this discussion appear to have advocates that want to argue for a narrow band of effects.
Carrick who said anything about zero? This is all about finding parameters which better represents noisy records.
Carrick,
“(The belief you can reduce the uncertainty of a physically measured quantity to zero by an appropriate algebraic transformation is a tip-off.”
This gets silly. Neither the global anomaly not the global average is a physically measured quantity. There’s no global thermometer.
The permeability of free space (magnetic constant) has uncertainty zero. It’s just a matter of how things are defined.
Eli:
Nick did. You missed it because you arrived at the end of a conversation.
He thinks the measurement error goes to zero for $latex \hat T(t) = T(t) – T(1960)$, when $latex t = 1960$.
Maybe you can knock some sense into his head.
Nick:
There is no “gets” there is only “has gotten”, and you’ve been there for a while.
If you are using temperature measurements to compute the global mean anomalized temperature, then it most definitely is a physically measured quantity, albeit not a directly measured one.
Can you name a device that “directly” measures temperature for a “continuous” medium?
Mercury thermometers don’t measure temperature, they measure the amount of linear expansion of mercury confined in a thin tube. And of course they don’t respond to temperature, but heat energy flux. For continuously varying temperature, the mercury thermometer will always have a latency and a frequency cut-off.. the relationship to true temperature is to be had only indirectly. (Eli will probably say to remember to calibrate and correct for changes in static pressure…)
Permeability of free space isn’t a continuously varying measurable, quantity, it’s merely a defined constant that relates the units of measure It relates mechanical units (e.g. meters, kilograms & seconds) to the independently made up unit of measure “coulombs.” (See Gaussian units, which has no separate unit of measure for charge).
So actually, it’s not just a matter of arbitrary definition. It’s a matter of precise definition with a thorough understanding of measurement science when you do so.
For $latex \hat T(t) = T(t) – T(1960)$ you can compute the uncertainty for any t, and show that:
$latex \sigma_{\hat T}^2(t) = \sigma_T^2(t) + \hat \sigma_T^2(1960)$,
$latex \sigma_{\hat T}(t) = $uncertainty in measurable $latex \hat T(t)$
$latex \sigma_{T}(t) = $uncertainty in measurable $latex T(t)$,
This works for any value of t including $latex t = 1960$, no magical cancellations.
Here’s a simple example:
Compute $latex {d\over dx} \sin x$ for $latex x = 1960$.
So let’s set $latex x = 1960$ then take the derivative, right?
Any dunderhead can see this is just a matter of definition and this has gotten too silly!
Or not, order of operation does matter.
When you compute uncertainties, you perform the residual analysis first, and then you substitute in the particular value (or values).
Otherwise you will always get nonsense for answers.
[None of this presupposes that you don’t have to treat certain values via special case. E.g.
$latex (\cos x – 1)/x$ is a well defined function at $latex x = 0$ as a limit of $latex x \rightarrow 0$, but to evaluate its derivative at $latex x = 0$ involves special care.]
Carrick,
$latex \hat{T}(t)=T(t)-T(1960)$
No, you can’t sum variances when t=1960.
$latex T(1960)$ and $latex T(1960)$ are not independent.
Nick, what you’ve described is exactly the problem in using the measured variance in anomalized temperature measurements to estimate measurement uncertainty: The two quantities you are subtracting are 100% correlated.
Since you can’t screw yourself up to admit there’s an issue with Marcott in using the measured variance to estimate uncertainty, I don’t suppose any more discussion is going to be fruitful on this.
(The first part of the solution is admitting there’s a problem. Till then…)