Improvements and Extension of the Linear Carbon Sink Model

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Comments on “Improvements and extension of the linear carbon sink model” by Dengler.

The estimation and future projection of carbon sinks are of great importance for climate change research as well as the formulation of long-term emission reduction and temperature rise scenarios. This paper improved and expanded the linear carbon sink model established in the author's previous paper, focusing on land use and temperature disturbances. It achieved results that surpass those of the previous work and is capable of reproducing paleoclimate results established by ice core studies. This paper provides a tool for carbon cycle and climate change research. Therefore, although this paper needs improvement in writing, the reviewer recommends acceptance with a major revision, serving as an extension and supplement to the previous paper. The following are some suggestions need to be concerned.

 

Major comments:

1. Introduction part: The introduction section appears to be somewhat weak, and the scientific questions are not very clear. The importance of conducting this research needs to be well introduced. What similar models currently exist, what are the main issues, and what the advantages of simple linear models are? These questions need to be addressed in the introduction. I understand that some of the related scientific questions were covered in the previous article, but as an independent paper, this article still needs a qualified introduction.

2. Prediction part: The predictions of this paper only go up to the year 2023. As a complete work, I strongly suggest using CMIP5 or CMIP6 future projection scenarios to drive the model in this paper to make future projections. The projection results can then be compared with the ensemble mean of multiple Earth System Models in the IPCC report, thereby discussing the differences between simple and complex models. I concern that the results of this paper are based on a very high correlation between temperature and atmospheric CO2 concentration, especially since ice core data represent the pre-industrial revolution climate state, which was entirely the result of carbon balance. However, for the "non-carbon balance" state, which is clearly influenced by human activities, whether the linear carbon sink model can still be used requires discussion.

 

Minor comments:

1. Line 45-54, it’s better to place them after “see Figure 1 in [2]:” in the last paragraph, rather than arranging them with dots. The same goes for the rest of the article, and try not to list in dots.

2. Figure 1 was cited after Figure 2 in the text, so the order of the figures needs to be adjusted.

3. Figure 2, the grey shade needs to be explained in the captions.

4. The figure captions throughout the paper need to be improved, and some basic information needs to be clarified in the figure captions.

 

Author Response

Major comments:

1. I rewrote the introduction and put my research into the context of the state of the art without assuming that my previous paper has been read.
2. Following your recommendation, I introduced a new chapter with predictions. Originally I did not consider predictions to be essential, because the extension I made in this paper  (temperature as a predictor of CO2 concentration) has no real relevance for predictions, as long as temperature is as correlated to CO2 concentration as it has been for the last 70 years. I explain in the paper, why it is better to use the original apparently temperature independent linear carbon sink model for predictions. 
   
   In order to introduce something new, I added the experimental comparison with the discussed Bern model, which is the model usually applied in IPCC scenarios (the Nobel price winner Hasselmann had built it into a general circulation model; this is now referenced in the paper). 
   
   You suggested to use  the IPCC scenarios for the sake of comparability. I am discussing these in the paper, coming to the conclusion, that 3 of them are so much outside of reality, that I do not want to contribute to reality denial by propagating them.  I focussed on the reality based IEA "Stated Policies" scenario, which comes very close to the "middle" IPCC scenario. In order to have some "humanly possible" variability, I concstructed two more emission reduction scenarios, one of which comes close to one more IPCC scenario.  I hope this is acceptable for you. 

Minor comments:

1. I removed all lists with dots in the paper
2. Figure reference corrected
3. Now explained as the 95% confidence interval based on the prediction error
4. All figure captions have been rewritten with considerably more text.

Reviewer 2 Report

Comments and Suggestions for Authors

Review of “Improvements and extension of the linear carbon sink model” by Joachim Dengler.

 

The study presents improvements to the linear sink model for CO2 concentrations by taking into consideration the trends in land-use changes and air temperature. The modified model is tested on the long-term observations of CO2 and Temperature obtained from the VOSTOK Ice core data.

 

Overall, the manuscript is sound and follows the previous research done by the author. Some of the figures can be combined to make it less cluttered. It is suitable for publication only after the below comments are addressed.

 

Comments

1. The article needs more introduction to make the readers familiar with the current trends, and models that are addressing the issue highlighted by the author.

2. Figure 4: It is interesting to see the total growth concentration behaved almost opposite to the emissions trend listed in the CarbonBrief project (reference #11 in the original manuscript). For example: Consider the spike (maximum) in 2016; from the CarbonBrief project, the total emissions reduced from 2015 to 2016 meaning the growth concentration should have dipped for 2016 but instead it recorded a maximum. Similarly, the spike in 1998; again, from the reference 11, the land-use emissions recorded a local maximum in 1997 not 1998.

3. Figures 8 and 9 can be merged to make the point mentioned in lines 192-200 clearer.

4. How is the Pinatubo sink value/trend estimated?

5. I didn’t quite understand the concept of temperature data shift by 1450 to 1500 years. As stated earlier, (line 162), the authors didn’t want to infer the causality between the CO2 and Temperature, but by shifting the temperature data they stated in the conclusions that it leads CO2 concentration. Accepting this statement without any inference on the causality between the two is difficult.

6. The present work stands alone, in the sense that it needs comparison with other existing model(s). Adding this would make the manuscript robust.

7. The model when applied against the paleoclimate trends, gave a lower value of dC/dT and the authors contribute this to the time interval rather than the fact that anthropogenic emissions are not included in the paleoclimate data. 

 

Author Response

1. An completely new introduction is written, which does not rely any more on the previous paper,
2. First we need to look at the quality of the used data. The concentration and the "spiky" concentration growth data have by far the highest quality. If in doubt, I would always trust these data more than others.  
   Assuming that you refer to referenz 12 (Zeke Hausfather, CarbonBrief), as a consequence the numbers in that emission graph have to be taken with a grain of salt. There is a wide error bar, which justifies the title statement (in 2021!) that "for a decade emissions have been flat".  This argument applies even more to emissions from land use change, which have even wider error bars. 
   
   Obvious inconsistencies, which I encountered in my first paper (and did not resolve them there) made it necessary to discuss the topic of land use change emissions now, coming to the hopefully well founded conclusion that the best we can do now, is to set the land use change emissions of the last 70 years to a small constant. An alternative would be to assume a much lower zero-emissions equilibrium concentration than the well-accepted 280 ppm (this is what I implicitely did in my first paper), with the consequence of slightly less reliable predictions.  In the first half of the 20th century things were quite different, it seems as if we had quite large contributions of LUC emissions before 1950. That is still subject to further investigation, and I am not sure if this can be resolved, considering the rather unreliable measurement data before 1958.
    
   The other point is, that emission changes, which are only a small fraction of the emissions in an individual year, explain only a part of concentration growth, the other part is due to the sink effect, see equation 6.   E.g. the  visible Emission drop in 2020 due to Covid lockdowns is smaller than then spikes of the unfiltered concentration growth, which point in the other direction and overcompensate the "Covid lockdown" effect.  These spikes are reflected in sink residuals in Figure 5 and are later explained as being caused by temperature fluctuations, see Figure 7.   A reconstruction with the linear sink model throws away all these spikes in order to reach a "noise free" concentration growth. Figures 2 and 3 show, that the predicted/reconstructed concentration is faithful to the actual concentration.  When we want to know the consequences of anthropogenic emissions, it is better to throw away the "noise" created by zero-mean temperature spikes, especially when we make predictions for the future.  
    
3. ok
4. It is estimated from the emission residual in Figure 7. After applying the temperature dependence the residual becomes so small, that -- after a bit of smoothing, the "Pinatubo sink peak" can be masked out by a noise threshold. I have added some text into the caption of Figure 7.   
5. My statement about ignorance on causality of present CO2 just means, that I don't want to get involved in the "sensitivity discussion", i.e. how much CO2 influences temperature via the greenhous effect -- today. I am only interested in the correlation, not in causality for the particular question of that section. 
   
   The model introduced in this paper has a clear causality direction: Temperature fluctuations cause CO2 fluctuations - by means of induced emissions, e.g. ocean upwelling, but certainly not the other way round.  When I apply this model to the paleo data, by definition this implies that temperature drives CO2. And it is meanwhile a wellknown and mostly accepted fact, that there is a time lag of several centuries between the two. Due to the different "clocks" of temperature measurement and CO2 measurement in the VOSTOK data, an alignment of the data sets has to be made. This is what I have done.   And there is a clear error minimum when the "correct" alignment is reached.   
6. With the new introduction and the chapter on prediction, the model is compared with the state of the art models argumentatively as well as experimentally
7. You make a good point, but I am not quite sure how to deal with it. The short term changes in CO2 concentration which motivate the extension of the model and from which the parameters have been derived, have clearly the causal direction Temperature->CO2-concentration.   
   I will mention your suggestion, and add the possibility in the paper that due to the  added carbon and temperature in the ocean and atmosphere also the equilibrium between temperature rise and upwelling carbon may have changed. 

Reviewer 3 Report

Comments and Suggestions for Authors

 

Joachim Dengler al present a very interesting study on CO2 modeling and sinc evaluation based on prepocesing existing data, regarding the influence of El Nino event, Pinatubo eruption, etc. The interesting part is that the aplied model is used both for industrial era and for long term data (VOSTOK) and underlines the interdepecies of CO2 with Temperature.  

 

General remarks and suggestions

I suggest To exend a litle bit the introduction using more citation of paper on the subject of the paper. 

 All graphical representations must be improved by introducing the measurement unit and what each axis represents(adding exact axis titles)

Specific remarks and suggestions

line 102 check english betwen brackets)

line  200 check Figure 9 title

line 2018 add measurement unit to axis titles in Figure 10.

line 289 add degree sign

 

Comments on the Quality of English Language Minor typo and language corrections (mentioned in the specific remarks)

Author Response

General remarks and suggestions:

I have now created a much longer introduction, which does not depend on the previous paper any more. 

All Figures have been updated with much more text in the captions and improvements at the axis texts where necessary

 

Specific remarks and suggestions:

line 102: changed to "(where emissions caused by land use change were included)"

line 200: Figure caption is now a long text explaining the multiple graphs

line 218: Measurement units have been added to the axis descriptions

line 289: Degree sign (°) has been added. In this context I added a footnote, explaining that I use just ° for temperature anomalies instead of  °C, which could imply a fixed temperature scale and lead to misunderstanding.  

Reviewer 4 Report

Comments and Suggestions for Authors

1.      The introduction should introduce the topic and show the scientific background of the issue. It would be advisable to show the evolution of CO2 budget models, describing the advantages and disadvantages, and then demonstrate the novelty of your solution against this background. Please, see Instructions for Authors in Atmosphere.

2.      The Introduction section should end with specifying the research concept, i.e. stating the purpose(s) of the research and its scope, as well as a general description of the data and methods used.

3.      Cited references should be supplemented by providing background information and a brief history of the research.

4.      V. 43: What does the abbreviation w.r.t. mean? Abbreviations should be explained. Please check the entire text.

5.      V. 45-47: This fragment is incomprehensible “the oceans have both an emission process - upwelling in warm ocean - as well as an absorption process - downwelling in cold ocean - in the form of advection governed by Henry’s law”. Advection and Henry's Law are completely different things. Advection is certainly not governed by Henry's Law.

6.      V. 50: This fragment is unprecise “land plants as well as marine biota extract carbon from the atmosphere”. Land plants extract carbon from the atmosphere, but marine biota extract carbon from the water.

7.      Figure 1 should be described factually. It is not clear what the Figure shows. In particular, the title of the vertical axis needs to be specified (ppm is only a unit), and the charts need to be explained. The caption "Simple linear sink model" does not explain anything and is misleading because the linearity of the process is not shown.

8.      Figures 2 and 3 are discussed very briefly. It is not known why they were included, how they differ and what they show. The description says the measured CO2 concentration, but where? Authors should consider whether showing these Figures adds anything to the analysis.

9.      Please do not refer to equations or figures posted in other articles. If they are important for the analysis, please present them (equations) or describe them (charts).

10.  I don't understand equation (1) Gi = Ci+1 − Ci, the logical and understandable form of this equation is: Gi = Ci - Ci-1.

11.  Equation (2) Ei – Gi = Ai – Ni is incomprehensible because the physical meaning of the variables Ei, Ai, Ni is not explained in the text. This equation only makes sense if Ei, Ai, Ni are expressed as concentrations in ppm. Unfortunately, it is not described how to do this.

12.  What do Ai absorptions mean and what does sink mean? The author should specify this. Otherwise, the entire argument will be incomprehensible.

I am unable to evaluate the entire text as presented. Without understanding the assumptions, symbolism and other elements, it is impossible to evaluate the results and conclusions. The article should be rejected because it is not suitable for evaluation in this form. The manuscript is written extremely carelessly, with no respect for the potential reader. Unfortunately, the manuscript does not meet the standards expected by a highly rated scientific journal.

Author Response

1. The introduction has been substantially expanded according to the guidelines you wrote.
2. The research concept is now in a subsection of the introduction at the end
3. In the introduction and partly in the chapter "The components of the carbon cycle" background information are given and the history of the research ist described.
4. The abbreviation w.r.t. (=with respect to) has been replaced by the long form or a similar formulation  (at 3 locations).
5. This section has been reformulated (now at lines 106-111).
6. Has been reformulated to:
   In the net primary production process via photosynthesis  land plants as well as marine biota extract carbon from the atmosphere or the mixed layer of the ocean respectively. 
7. Figure 1 has now an elaborated caption explaining the graphs.
8. Text has been added to explain and motivate Figures 2 and 3.
9. Following your suggestion, I copied the referred image into the new paper.
10. I changed the indices of the equations according to your proposal. But this had quite some consequences for the following equations.  
11. This is a key equation. Therefore I rewrote the whole section in order to bring the (existing) description of the variables closer to the equation. Also the conversion between ppm and PgC is discussed.
12. Due to the much longer introductory sections the essential expressions "sink" and "absorption" are now better defined

I am sorry for the inconvenience this paper has caused you, and I hope that this updated version is more enjoyable. 

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The author has revised and responded to my questions, and I have no further comments.

Author Response

Thank you for your approval. 

Reviewer 2 Report

Comments and Suggestions for Authors

The author has addressed the reviewer's comments well. I recommend this version of the manuscript for publication. 

Author Response

Thank you for your approval. 

Reviewer 4 Report

Comments and Suggestions for Authors

In my opinion, the manuscript should be rejected. Despite the changes and corrections, the manuscript is written carelessly. I still don't see any respect for the potential reader.

1.      The Introduction section does not explain much and does not introduce the issue. Hermetic language was used, with no attempt to explain/define the terms used. A non-expert reader will not understand the problem. The research concept was not specified, which disqualifies the manuscript. "The purpose of this paper is to take a closer look at the linear sink model..." - this is not enough. The purpose, scope of the research and methodology used have not been described.

2.      Some terms that are key to the research concept, such as "the land use change emissions", were not explained.

3.      The data presented in the work and their origin were not described.

4.      Henry's law could describe the state of equilibrium at the boundary between the oceans and the atmosphere. They can be invoked if there is a balance. Meanwhile, the author states that ocean waters are not saturated with CO2, so there is no equilibrium.

5.      In the aqueous phase, chemical equilibria are very important, related to the dissociation of carbonic acid and the precipitation of bicarbonates and carbonates. Without taking into account these chemical equilibria, based only on flows and diffusion, it is impossible to model CO2 absorption complex phenomena.

6.      I was very confused by the treatment of emissions in concentration units (e.g. ppm). Emission is expressed as the amount of substance emitted (in mass units, number of particles or number of moles) per unit of time. I don't understand how emissions were converted to concentration. It should be described. Treating emissions as concentration is a serious terminological error. Alternatively, you could write about "concentration increase caused by emission".

7.      The statement that CO2 concentration correlates linearly with temperature is risky, although in the short term it may be confirmed by measurement. Rather, nonlinear correlations can be expected because Henry's constant, chemical equilibrium constants, chemical reaction rate constants are described by nonlinear functions of temperature.

Author Response

1.  After the previously justified criticism of the lack of a proper introduction, I have taken this very serious, and went to great length to explain and introduce the issue of the paper:
   
   a) I began by pointing out that there are two essentially different research approaches, which are both valid. When it is justified to analyse the global behaviour of a system with a single or few parameters, it is not necessary to know all the contribution details. We know this, e.g. from thermodynamics. 
   When you accept this in principle, you have to allow me neglecting details, which may be important for a bottom up approach -- unless you can prove in detail a serious error when neglecting them.  
   
   b) I introduced the investigated issue with this expression as beginningrt of the discussion of the state of the art:
   The relation between anthropogenic carbon emissions, CO$_2$ concentration and the carbon cycle.
   
   In order to clarify  I added now a statement before this discussion:
   
   This paper aims at deepening the understanding of the relation between anthropogenic carbon emissions, CO$_2$ concentration and the carbon cycle by extending a previously constructed top down model 
   
   c) For describing the details of the research concept I have devoted the whole subsection 1.1.  The sentence that you criticize as not being sufficient, is just the bridge to the following subsection. In order to clarify this, I now moved the sentence into the subsection 1.1 as its first sentence.  
   
   
2. I added  at the first occurrence of "land use change emissions" in the introduction, section 1.1, this text and an accompanying reference:
   
   These are emissions caused by changes of the natural carbon cycle such as deforestation and urban growth. A comprehensive introduction into the meaning of this type of emissions is given in \cite{Schwingshackl2023}.
   
   I am not aware of other undefined expressions.
    
3. All used data are publicly available and well known data series, listed in the Data availability statement, which has been introduced with the sentence:
   
   All evaluations are based on publicly available data and software:
   
   Additionally I now introduced the data sets at the end of the introduction: 
   
   All data sets used is this publication are well known and undisputed standard data series, all of them referenced in the Data availability statement.  The Carbon emission data, including the land use change emissions, are from the Global Carbon Budget \cite{essd-15-5301-2023}, the CO$_2$ concentration data are from Maona Loa \cite{maonaloa2023} and the temperature time series is the global yearly sea surface temperature data set HadSST4 \cite{HadSST4-2019}. The historic ice core data are referenced and described in the section where they are used.
   
   
4. It is a common approach in most research of this kind (and can be regarded as common knowledge in the field) that the ocean is divided into the top layer called "mixed layer" and the deep ocean. Depending on the issue this can be further refined.   The mixed layer is considered to be approximately in equlibrium with the atmosphere. I added these sentences to clarify the applicability of Henry's law:
   
   Henry's law applies to the state of equilibrium. Whereas the climate system as a whole is not in equilibrium, the relevant subsystem mixed layer (top 75m of ocean) and atmosphere can be regarded to be in a state of equilibrium due to the known small relaxation time of appr. 1-2 years -- compared to the time ranges relevant for climate changes. Some authors (e.g. \citep{halparin2015}) treat the mixed layer as an extension of the atmosphere.
   
   
5. As I layed out in the introduction, there are two approaches to complex problems.  I understand that you claim that no understanding can be reached without deeper analysis of the chemical processes in the ocean. This is in my understanding an element of what I call the bottom up approach, i.e. understanding all contributing mechanism in detail. My claim in this and the previous paper is, that there is a valid second road to understanding, the top down approach, which rather looks at the response  of the system as a whole, without investigating all components in detail.  
   In order to justify   this top down approach, I had already written in the introduction, that the top down approach is based on the linearity assumption (lines starting with 67). Assuming that you will raise doubts about the validity of this assumption, I added these lines to the section:
   Apart from the fact that this linearity assumption leads to consistent results over a more than 70 years period, additionally the underlying processes have been analysed to justify from first principles that they can be linearized  within the range of realistically expected parameter values \citep{halparin2015},\citep{DenglerReid2023}
   
   
6. As I wrote, in order to set up the mass balance equation, which is fundamental for the paper (equation 2 and many others), all occuring entities have to have the identical measurement unit.
   In order to motivate ppm also for emissions and absorptions, which in this case is justified and not an error, I added explanatory sentences and the reference to the IPCC publication where the same conversion is done:
   
   Obviously emissions, absorptions, and concentration must be measured with the same unit. The natural unit for evaluating mass conservation would be Pg, but atmospheric masses are usually measured as concentration, relative to the total mass of the atmosphere. For emissions and absorption their masses translate into potential concentration change. Therefore ppm is used here consequently, where 1 ppm (parts per Million) is equivalent to 2.12 PgC (Petagram Carbon). This conversion factor is also used by IPCC \cite{IPCCWG1AR52018}. 
   
   
7. At no point I draw any conclusion of the kind you mention from the correlation between temperature and CO2 concentration. It is an observation about what actually happened, not more. To make that even more clear, I now changed the sentence in question to:
   We make no claim of causality nor any other dependence between CO$_2$ concentration and temperature, in neither direction, but just recognise their strong correlation for the last 70 years
   
   The point I am making is, that there has historically been a correlation that is large enough to be able to seperate the temperature into 2 components, one of them is a strict linear function of concentration, and the other is the residual. This works always and bears no risk at all - you have a linear fit and a residuum. This implies that the residual is zero mean without trend over the measurement interval.  So the "CO2 temperature proxy" is for me more a mathematical tool than a statement about physics or chemistry.  It's not me but others who impose a lot of meaning into the relation between CO2 and temperature.    
   In the sink model any effect of the first temperature component (a linear function of concentration) could equally be attributable to concentration,  explaining, why the simple linear model does not show any trend of natural emissions, as shown in Figure 6.  Only effects of the "residual temperature" can be detected directly by analysing emissions and concentration growth as shown in Figure 8.