Tag: CO2

Climate Causality Confusion

A newish set of papers (1. Theory (preprint); 2. Applications (preprint); 3. Extension) is making the rounds on the climate skeptic sites, with – ironically – little skepticism applied.

The claim is bold:

… According to the commonly assumed causality link, increased [CO2] causes a rise in T. However, recent developments cast doubts on this assumption by showing that this relationship is of the hen-or-egg type, or even unidirectional but opposite in direction to the commonly assumed one. These developments include an advanced theoretical framework for testing causality based on the stochastic evaluation of a potentially causal link between two processes via the notion of the impulse response function. …. All evidence resulting from the analyses suggests a unidirectional, potentially causal link with T as the cause and [CO2] as the effect.

Galileo complex seeps in when the authors claim that absence of correlation or impulse response from CO2 -> temperature proves absence of causality:

Clearly, the results […] suggest a (mono-directional) potentially causal system with T as the cause and [CO2] as the effect. Hence the common perception that increasing [CO2] causes increased T can be excluded as it violates the necessary condition for this causality direction.

Unfortunately, these claims are bogus. Here’s why.

The authors estimate impulse response functions between CO2 and temperature (and back), using the following formalism:


where g(h) is the response at lag h. As the authors point out, if

the IRF is zero for every lag except for the specific lag ℎ0, then Equation (1) becomes y(t)=bx(t-h0) +v(t). This special case is equivalent to simply correlating  y(t) with x(t-h0) at any time instance . It is easy to find (cf. linear regression) that in this case the multiplicative constant is the correlation coefficient of y(t) and  x(t-h0) multiplied by the ratio of the standard deviations of the two processes.

Now … anyone who claims to have an “advanced theoretical framework for testing causality” should be aware of the limitations of linear regression. There are several possible issues that might lead to misleading conclusions about causality.

Problem #1 here is bathtub statistics. Temperature integrates the radiative forcing from CO2 (and other things). This is not debatable – it’s physics. It’s old physics, and it’s experimental, not observational. If you question the existence of the effect, you’re basically questioning everything back to the Enlightenment. The implication is that no correlation is expected between CO2 and temperature, because integration breaks pattern matching. The authors purport to avoid integration by using first differences of temperature and CO2. But differencing both sides of the equation doesn’t solve the integration problem; it just kicks the can down the road. If y integrates x, then patterns of the integrals or derivatives of y and x won’t match either. Even worse differencing filters out the signals of interest.

Problem #2 is that the model above assumes only equation error (the term v(t) on the right hand side). In most situations, especially dynamic systems, both the “independent” (a misnomer) and dependent variables are subject to measurement error, and this dilutes the correlation or slope of the regression line (aka attenuation bias), and therefore also the IRF in the authors’ framework. In the case of temperature, the problem is particularly acute, because temperature also integrates internal variability of the climate system (weather) and some of this variability is autocorrelated on long time scales (because for example oceans have long time constants). That means the effective number of data points is a lot less than the 60 years or 720 months you’d expect from simple counting.

Dynamic variables are subject to other pathologies, generally under the heading of endogeneity bias, and related features with similar effects like omitted variable bias. Generalizing the approach to distributed lags in no way mitigates these. The bottom line is that absence of correlation doesn’t prove absence of causation.

Admittedly, even Nobel Prize winners can screw up claims about causality and correlation and estimate dynamic models with inappropriate methods. But causality confusion isn’t really a good way to get into that rarefied company.

I think methods purporting to assess causality exclusively from data are treacherous in general. The authors’ proposed method is provably wrong in some cases, including this one, as is Granger Causality. Even if you have pretty good assumptions, you’ll always find a system that violates them. That’s why it’s so important to take data-driven results with a grain of salt, and look for experimental control (where you can get it) and mechanistic explanations.

One way to tell if you’ve gotten causality wrong is when you “discover” mechanisms that are physically absurd. That happens on a spectacular scale in the third paper:

… we find Δ=23.5 and 8.1 Gt C/year, respectively, i.e., a total global increase in the respiration rate of Δ=31.6 Gt C/year. This rate, which is a result of natural processes, is 3.4 times greater than the CO2 emission by fossil fuel combustion (9.4 Gt C /year including cement production).

To put that in perspective, the authors propose a respiration flow that would put the biosphere about 30% out of balance. This implies a mass flow of trees harvested, soils destroyed, etc. 3.4 times as large as the planetary flow of fossil fuels. That would be about 4 cubic kilometers of wood, for example. In the face of the massive outflow from the biosphere, the 9.4 GtC/yr from fossil fuels went where, exactly? Extraordinary claims require extraordinary evidence, but the authors apparently haven’t pondered how these massive novel flows could be squared with other lines of evidence, like C isotopes, ocean Ph, satellite CO2, and direct estimates of land use emissions.

This “insight” is used to construct a model of the temperature->CO2 process:

In this model, the trend in CO2 is explained almost exclusively by the mean temperature effect mu_v = alpha*(T-T0). That effect is entirely ad hoc, with no basis in the impulse response framework.

How do we get into this pickle? I think the simple answer is that the authors’ specification of the system is incomplete. As above, they define a causal system,

y(t) = ∫g1(h)x(t-h)dh

x(t) = ∫g2(h)y(t-h)dh

where g(.) is an impulse response function weighting lags h and the integral is over h from 0 to infinity (because only nonnegative lags are causal). In their implementation, x and y are first differences, so in their climate example, Δlog(CO2) and ΔTemp. In the estimation of the impulse lag structures g(.), the authors impose nonnegativity and (optionally) smoothness constraints.

A more complete specification is roughly:

Y = A*X + U

dX/dt = B*X + E

where

  • X is a vector of system states (e.g., CO2 and temperature)
  • Y is a vector of measurements (observed CO2 and temperature)
  • A and B are matrices of coefficients (this is a linear view of the system, but could easily be generalized to nonlinear functions)
  • E is driving noise perturbing the state, and therefore integrated into it
  • U is measurement error

My notation could be improved to consider covariance and state-dependent noise, though it’s not really necessary here. Fred Schweppe wrote all this out decades ago in Uncertain Dynamic Systems, and you can now find it in many texts like Stengel’s Optimal Control and Estimation. Dixit and Pindyck transplanted it to economics and David Peterson brought it to SD where it found its way into Vensim as the combination of Kalman filtering and optimization.

How does this avoid the pitfalls of the Koutsoyiannis et al. approach?

  • An element of X can integrate any other element of X, including itself.
  • There are no arbitrary restrictions (like nonnegativity) on the impulse response function.
  • The system model (A, B, and any nonlinear elements augmenting the framework) can incorporate a priori structural knowledge (e.g., physics).
  • Driving noise and measurement error are recognized and can be estimated along with everything else.

Does the difference matter? I’ll leave that for a second post with some examples.

 

 

A natural driver of increasing CO2 concentration?

You wouldn’t normally look at a sink with the tap running and conclude that the water level must be rising because the drain is backing up. Nevertheless, a physically similar idea has been popular in climate skeptic circles lately.

You actually don’t need much more than a mass balance to conclude that anthropogenic emissions are the cause of rising atmospheric CO2, but with a model and some data you can really pound a lot of nails into the coffin of the idea that temperature is somehow responsible.

This notion has been adequately debunked already, but here goes:

This is another experimental video. As before, there’s a lot of fine detail, so you may want to head over to Vimeo to view in full screen HD. I find it somewhat astonishing that it takes 45 minutes to explore a first-order model.

Here’s the model: co2corr2.vpm (runs in Vensim PLE; requires DSS or Pro for calibration optimization)

Update: a new copy, replacing a GET DATA FIRST TIME call to permit running with simpler versions of Vensim. co2corr3.vpm

A few parts per million

IMG_1937

There’s a persistent rumor that CO2 concentrations are too small to have a noticeable radiative effect on the atmosphere. (It appears here, for example, though mixed with so much other claptrap that it’s hard to wrap your mind around the whole argument – which would probably cause your head to explode due to an excess of self-contradiction anyway.)

To fool the innumerate, one must simply state that CO2 constitutes only about 390 parts per million, or .039%, of the atmosphere. Wow, that’s a really small number! How could it possibly matter? To be really sneaky, you can exploit stock-flow misperceptions by talking only about the annual increment (~2 ppm) rather than the total, which makes things look another 100x smaller (apparently a part of the calculation in Joe Bastardi’s width of a human hair vs. a 1km bridge span).

Anyway, my kids and I got curious about this, so we decided to put 390ppm of food coloring in a glass of water. Our precision in shaving dye pellets wasn’t very good, so we actually ended up with about 450ppm. You can see the result above. It’s very obviously blue, in spite of the tiny dye concentration. We think this is a conservative visual example, because a lot of the tablet mass was apparently a fizzy filler, and the atmosphere is 1000 times less dense than water, but effectively 100,000 times thicker than this glass. However, we don’t know much about the molecular weight or radiative properties of the dye.

This doesn’t prove much about the atmosphere, but it does neatly disprove the notion that an effect is automatically small, just because the numbers involved sound small. If you still doubt this, try ingesting a few nanograms of the toxin infused into the period at the end of this sentence.

Bathtub Still Filling, Despite Slower Inflow

Found this bit, under the headline Carbon Dioxide Levels Rising Despite Economic Downturn:

A leading scientist said on Thursday that atmospheric levels of carbon dioxide are hitting new highs, providing no indication that the world economic downturn is curbing industrial emissions, Reuters reported.

Joe Romm does a good job explaining why conflating emissions with concentrations is a mistake. I’ll just add the visual:

CO2 stock flow structure

And the data to go with it:

CO2 data

It would indeed take quite a downturn to bring the blue (emissions) below the red (uptake), which is what would have to happen to see a dip in the CO2 atmospheric content (green). In fact, the problem is tougher than it looks, because a fall in emissions would be accompanied by a fall in net uptake, due to the behavior of short-term sinks. Notice that atmospheric CO2 kept going up after the 1929 crash. (Interestingly, it levels off from about 1940-1945, but it’s hard to attribute that because it appears to be within natural variability).

At the moment, it’s kind of odd to look for the downturn in the atmosphere when you can observe fossil fuel consumption directly. The official stats do involve some lag, but less than waiting for natural variability to shake out of sparse atmospheric measurements. Things might change soon, though, with the advent of satellite measurements.

State Emissions Commitments

For the Pangaea model, colleagues have been compiling a useful table of international emissions commitments. That will let us test whether, if fulfilled, those commitments move the needle on global atmospheric GHG concentrations and temperatures (currently they don’t).

I’ve been looking for the equivalent for US states, and found it at Pew Climate. It’s hard to get a mental picture of the emissions trajectory implied by the various commitments in the table, so I combined them with emissions data from EPA (fossil fuel CO2 only) to reconcile all the variations in base years and growth patterns.

The history of emissions from 1990 to 2005, plus future commitments, looks like this:

State emissions commitments, vs. 1990, CO2 basis

Note that some states have committed to “long term” reductions, without a specific date, which are shown above just beyond 2050. There’s a remarkable amount of variation in 1990-2005 trends, ranging from Arizona (up 55%) to Massachusetts (nearly flat).

Continue reading “State Emissions Commitments”