The paper is well written, it is addressed to a wide readership and could trigger more intensive research on the above topic by interdisciplinary research teams.

Taking into account all the above I would suggest that the paper should be accepted as is.

Author Response

Although I am not an expert in geochemistry or atmospheric physics to judge the corresponding parts of the specific paper, I consider that the authors have presented a convincing study proving that the fast variability in atmospheric CO_2 growth rate cannot be explained by the anthropogenic CO_2 emissions, while shares common spectral components with global seismic-moment release. This finding, within the frame of the LENR hypothesis, might provide an explanation for the observed fast variability of atmospheric CO_2 growth rate which could be considered an evidence of the relationship between atmospheric and seismic variables. The paper is well written, it is addressed to a wide readership and could trigger more intensive research on the above topic by interdisciplinary research teams. Taking into account all the above I would suggest that the paper should be accepted as is. The authors wish to thank the reviewer for his positive evaluation

Reviewer 2 Report

Taking into account all my observations listed hereafter, I encourage the authors to do some extra effort to improve the paper. They end the paper with “certain conclusions” without any strong and robust analysis of the data in terms of causality analysis. I suggest them to simply smooth their findings and to turn the paper into a way to open a debate on the models which regulates atmospheric CO₂.

To check if atmospheric CO₂ is characterized by the superposition of a trend plus some cyclical components is interesting, and scientifically correct as approach, as for every time series (here in particular a climatic one). To detect the significant oscillations and to understand their correlation with other variables connected to Earth activity can be interesting, also. But I ask for a more deep analysis.

The authors can propose this work, by underlying that a detailed study will follow, and by softening some too strong conclusions, in my opinion, not supported by suitable analysis.

Some comments/proposal/requirements follow.

Introduction

Pag. 1

Line 4. “[..] very different from today’s, of which the origin”, I suggest to convert into:

“very different from the current one, whose origin”.

Line 9. When the authors assess that “[…] the changes in element concentrations appear to be intimately correlated to the Earth’s tectonic activity”, may be they can put here some references about that evidence?

Line 10. When the authors say: “composition time variations in the Earth’s atmosphere”, may be they can turn into: “the temporal evolution of the Earth’s atmosphere composition”?

Line 16. The authors call Fig. 1. To me it is not clear from where the picture is taken. Did they produce Fig.1 by themselves by collecting the information taken from the set of references [21–26], or, rather did they took the figure from other sources? If so, put the reference/es in the figure caption also. In any case, may be the authors can disentangle this point, adding just one more sentence.

The same for Fig. 2.

Pag 2

Fig. 2. Caption: the authors should define “Archean area” also in the text.

The authors say that from 3.8 to 2.5 Gyr ago H₂O and CO₂ underwent a huge increase. From the figure, I see an increase from 3.5 Gyr, a plateau, and then a decrease before 2.5 Gyr. Analogously, N₂ and O₂ are expected to increase after 2.5 Gyr. From the time scale of Fig. 2 the “critical” year seems to occur before 2.5 Gyr.

Can the authors improve/correct the time scale interpretation?

Line 11. After eq. (1), the authors speak about an “estimated Mg increment of about 3.2%”.

From where they took this information? Does it come from the set of references [27 – 31] ? I suggest to the authors to better develop this point, since it is not so intuitive for a not specialized reader. For example, the authors explain two type of “second set of reactions”: 1) Si, Al, Mg as starting elements, (C, N, O) as product; 2) Mg as the starting element, C as the product. May be, I’m missing something here.

Analogously, what about the first set of reactions?

Pag 3

The authors present the quantitative considerations of the hypothesis they support. I have to ask to the authors first on which ground they perform the calculation? Second, is it possible to add an estimation of the goodness and reproducibility of the results? The authors obtain an atmospheric pressure of about 660.70 atm. To assess if this measure is “consistent” with the theoretical value of about 650 atm, some statistical tests have to be performed.

I’m sure the authors took into consideration this aspect, so I suggest they add a sentence about that.

Paragraph 2 – Atmospheric CO₂ and Carbon cycle.

Pag. 5

Line 3. The authors say that CO₂ levels exceed measurements form the last 1000 years. Actual values for the global average of atmospheric CO₂ concentrations in ppm (more than 400 ppm) exceed the values recorded for the last 800.000 y at least – according to artic ice cores measurements – not only the last 1000 years values.

Refer for example to Luthi et al., Nature, 2008 (EPICA Dome C ice core) and to the data provided by NOAA NCEI Paleoclimatology Program.

Line 6.

The “problem” concerning GHGs is their huge amount in the last decades, especially. Anthropogenic CO₂ is not considered the “only” attributing factor by scientific community, but it is considered the “main” attributing factor to the sudden increase in CO₂ emissions in the last decades. That’s the point. It is not so “strange” the presence of a long term oscillation of CO₂ emissions, but what is alarming is the fact that CO₂ grew up of about 40% in the last 200 y, especially after the WWII, due to the rebirth of European economies first, and then to the developing countries industrial growth (China, but also India). The “speed” of that change is dangerous more than the change itself. The same it can be noticed for both N₂O (+20%) and CH₄ (+140%), which are also more dangerous than CO₂.

NB: all the percentage here are evaluated as percentage of growth w.r.t. the beginning of Industrial Era.

Line 16 and discussions therein.

The authors cite some basic papers about the carbon storage by tropical forests. Anyway, in my personal opinion, the authors are not giving any scientific proof about the huge interpretative correction they propose. Even if some other terms could be taken into account in the balance equation of CO₂ atmospheric growth, that observation does not put into discussion that actual atmospheric CO₂ rising trend is mainly connected to human activities: the last IPCC report (2018) call it a “virtually true” (p > 0.99) fact, thus testifying the common scientific belief of a strong significant correlation between extreme climate events (the growing of CO₂ concentration in the atmosphere is just one of them) and the anthropogenic activity. For example, oceans are carbon sinks, but the actual situation is provoking an increase in oceans acidification. The main consequence is that oceans become carbon sources, since they are no more able to absorb CO₂, and rather they start to emit it. Some extra sources, missing in the balance, can also be positive feedback of the human activity, again.

Paragraph 3 – Data Analysis

The authors propose some other “sources” for CO₂ emission in the atmosphere. Their idea is acceptable, but I ask them to smooth their conclusions, to be more precise and critical, especially in data analysis, and to be less generic.

1) The authors propose as extra source of atmospheric CO₂ the one coming from tectonic activity. This is true, there are scientific evidences about the fact that changes in atmospheric concentration are connected to Earth’s tectonic activity, as the authors describe in the Introduction. Anyway, that’s true in “big” events, such as the events connected to tectonic plate formation, not for small “negligible” events. This is a first observation. Actually we are not experiencing plate formation events.

2) The authors introduce the concept of CO₂ as precursor of seismic activity. That’s completely different, and it is one of the most controversial topics in recent scientific literature.

Sure, in the presence of some huge earthquakes an increase of daily CO₂ is locally recorded. Nevertheless, there are evidences of big tectonic activity (with connected extra CO₂ emissions) which didn’t bring to any earthquake.

So I ask to the authors not to use tectonic activity as synonymous of earthquakes and to consider several aspects they omit. First, CO₂ emission related to tectonic activity depends on the concomitance of several factors, such as the presence of an anomalous heat flux below Earth’s crust, and the presence of crustal thinning. Several authors focused on localized CO₂ degassing areas connected to seismic activity. On the contrary, the authors of this paper try to find global and general conclusions with a too limited approach, by comparing global CO₂ atmospheric emissions with global seismic-moment release.

I propose to the authors to consider and cite more basic papers about that, by starting from the precursors (King, 1986, Journal of Geophysical Research; Thomas, 1988, PAGEOPH). I propose some recent works that can be considered as starting point by the authors, from more general theories to local evidences: Martinelli and Dadomo (2017, Chemical Geology), Manga et. al (2012, Reviews of Geophysics), Barberio et. al (2017, Scientific Reports), Gherardi and Pierotti (2018, Applied Geochemistry), Pierotti et al. (2017, Physics and Chemistry of the Earth).

3) I ask the author to be more detailed. From which database the annual anthropogenic CO₂ emissions are taken? Please add a sentence about that, not only a link. The same for the atmospheric CO₂ growth rate.

I cannot follow the next 3 listed comments.

The authors say that the downward trend of atmospheric CO₂ (such as in 1988, 1993) is not reflected in a reduction of CO₂ emissions, for example. Trends and oscillatory patterns have to be studied as a whole, when reading a time series. It is obvious that atmosphere is not answering immediately to a change in CO₂ emissions, since CO₂ belongs to the complex atmosphere-ocean-land CO₂ cycle. There are “delays” between a perturbation and the answer to that perturbation. A change in the amplitude or frequency of an oscillatory pattern can or not be reflected in the trend. Or it can be reflected with some delay. In 2008 the CO₂ growth rate underwent a reduction due to industrial crisis. Nevertheless, the global trend of CO₂ growth rate was positive as well. The system absorbed the perturbation, without changing its global trend, or viceversa.

4) The authors perform a time series analysis on all the three series they study.

First they detrend the time series, then they perform a FFT analysis. Which detrending methods have they used? Detrending is one of the most delicate procedure, when analyzing short and noisy time series, such as in that case.

Second, I cannot see any significance test which assesses the “real existence” of the 20 y, 3.7 y, and 2.5 yr. Did the authors consider some advanced spectral techniques? Which kind of background noise the authors assumed for this analysis? The idea of performing a spectral analysis on this three indicators can be interesting and should be encouraged.

5) A spectral analysis is neither a causality analysis nor a synchronization analysis. Even when I find a common cycle between two different indicators, I cannot say nothing about the reciprocal causality relation if I use a data-driven approach. Common cycles can indicate that both the indicators depend on a third one (spurious correlation), not that one of them influence the other.

So I ask to the authors to smooth their conclusions, since no evidence is proved from the analysis.

Author Response

Line 1. “Recent geochemistry studies [..] ”. I see paper from the Eighties in the references that the authors cite. May be authors can say “Several geochemistry studies” or add “Recent and past geochemistry studies”? Yes, the authors have modified the sentence accordingly: “Several geochemistry studies…” Line 4. “[..] very different from today’s, of which the origin”, I suggest to convert into: “very different from the current one, whose origin”. Yes, the authors have modified the sentence accordingly. Line 9. When the authors assess that “[…] the changes in element concentrations appear to be intimately correlated to the Earth’s tectonic activity”, may be they can put here some references about that evidence? The references are those reported later: 21 Favero, G.; Jobstraibizer, P. The distribution of aluminum in the Earth: from cosmogenesis to Sial evolution. Coord Chem Rev 1996, 149, 367–400. 22 Taylor, S.R.; McLennan, S.J., Planetary Crusts: their composition, origin and evolution; Cambridge University Press: Cambridge; 2009. 23 Hawkesworth, C.I.; Kemp, A.I.S. Evolution of the continental crust. Nature 2006, 443, 811–817. 24 Doglioni, C. Interno della Terra. In Enciclopedia Scienza e Tecnica; Treccani, 2007; pp. 595–605. 25 Rudnik, R.L.; Fountain, D.M. Nature and composition of the continental crust: a lower crustal perspective. Rev Geophys 1995, 33(3), 267–309. 26 Yaroshevsky, A.A. Abundances of chemical elements in the Earth’s crust. Geochem Int 2006, 44(1), 54–62. Line 10. When the authors say: “composition time variations in the Earth’s atmosphere”, may be they can turn into: “the temporal evolution of the Earth’s atmosphere composition”? Yes, the authors have modified the sentence accordingly. Line 16. The authors call Fig. 1. To me it is not clear from where the picture is taken. Did they produce Fig.1 by themselves by collecting the information taken from the set of references [21–26], or, rather did they took the figure from other sources? If so, put the reference/es in the figure caption also. In any case, may be the authors can disentangle this point, adding just one more sentence. In the captions the following sentence has been added: “(the picture, extracted from [31], was produced by collecting information taken from [21-26]; more details are reported in [32]).” where: 32 Carpinteri, A.; Manuello, A. Reply to “Comments on ‘Geomechanical and Geochemical Evidence of Piezonuclear Fission Reactions in the Earth’s Crust’ by A. Carpinteri and A. Manuello” by U. Bardi and G. Comoretto. Strain 2013, 49, 548–551. Pag 2 Fig. 2. Caption: the authors should define “Archean area” also in the text. Yes, the authors have modified this sentence: “Recent data on the composition time variations in the Earth’s atmosphere have shown that CO2 and H2O concentrations in the atmosphere increased dramatically between 3.8 and 2.5 Gyr ago, between the tectonic plate formation and the most severe tectonic activity.” as follows: “Recent data on the temporal evolution of the Earth’s atmosphere have shown that CO2 and H2O concentrations in the atmosphere increased dramatically during the Archean era, occurring 3.8 to 2.5 Gyr ago, between the tectonic plate formation and the most severe tectonic activity.” The authors say that from 3.8 to 2.5 Gyr ago H2O and CO2 underwent a huge increase. From the figure, I see an increase from 3.5 Gyr, a plateau, and then a decrease before 2.5 Gyr. Analogously, N2 and O2 are expected to increase after 2.5 Gyr. From the time scale of Fig. 2 the “critical” year seems to occur before 2.5 Gyr. Can the authors improve/correct the time scale interpretation? The authors have modified this sentence: “Thus, a significant coupling appears between the periods of intense tectonic activity and the sudden increments of CO2 (and H2O), and later of N2 and O2 levels in the atmospheric composition over the Earth’s lifetime [1,19,20] (see Fig. 2).” as follows: “Thus, a significant coupling appears between the periods of intense tectonic activity and the sudden increments of CO2 (and H2O), occurred 3.5 Gyr ago, and later, 2.5 Gyr ago, of N2 and O2 levels in the atmospheric composition over the Earth’s lifetime [1,19,20] (see Fig. 2).” Line 11. After eq. (1), the authors speak about an “estimated Mg increment of about 3.2%”. From where they took this information? Does it come from the set of references [27 – 31] I suggest to the authors to better develop this point, since it is not so intuitive for a not specialized reader. For example, the authors explain two type of “second set of reactions”: 1) Si, Al, Mg as starting elements, (C, N, O) as product; 2) Mg as the starting element, C as the product. May be, I’m missing something here. Analogously, what about the first set of reactions? This information was taken from ref [22]: 22 Taylor, S.R.; McLennan, S.J., Planetary Crusts: their composition, origin and evolution; Cambridge University Press: Cambridge; 2009. The text has been modified accordingly: “..(3.2 %, according to [22])” The reactions are reported in Tab. 12.2 p. 176 in [31], as pointe out in the text. In particular, the LENR involving Mg and C is: Mg12 --> 2C6 Pag 3 The authors present the quantitative considerations of the hypothesis they support. I have to ask to the authors first on which ground they perform the calculation? Second, is it possible to add an estimation of the goodness and reproducibility of the results? The authors obtain an atmospheric pressure of about 660.70 atm. To assess if this measure is “consistent” with the theoretical value of about 650 atm, some statistical tests have to be performed. I’m sure the authors took into consideration this aspect, so I suggest they add a sentence about that. Yes, the authors have modified the text by smoothing the sentence as follows: “Interestingly, a comparison between a very rough estimate and experimental evidences seems to support this hypothesis. […] Given a terrestrial surface area of 5.1×1014m2 and conjecturing the same gravitational acceleration for the proto-Earth, we obtain ~660 atm as a tentative value for the atmospheric pressure.” Paragraph 2 – Atmospheric CO2 and Carbon cycle. Pag. 5 Line 3. The authors say that CO2 levels exceed measurements form the last 1000 years. Actual values for the global average of atmospheric CO2 concentrations in ppm (more than 400 ppm) exceed the values recorded for the last 800.000 y at least – according to artic ice cores measurements – not only the last 1000 years values. Refer for example to Luthi et al., Nature, 2008 (EPICA Dome C ice core) and to the data provided by NOAA NCEI Paleoclimatology Program. The authors have modified the sentence as follows: “As current atmospheric CO2 levels exceed measurements from the last 800,000 years, according to artic ice core measurements [47],...” Where: 47 Luthi, D. et al., High-resolution carbon dioxide concentration record 650,000 - 800,000 years before present. Nature 2008, 453, 379–382. Line 6. The “problem” concerning GHGs is their huge amount in the last decades, especially. Anthropogenic CO2 is not considered the “only” attributing factor by scientific community, but it is considered the “main” attributing factor to the sudden increase in CO2 emissions in the last decades. That’s the point. It is not so “strange” the presence of a long term oscillation of CO2emissions, but what is alarming is the fact that CO2 grew up of about 40% in the last 200 y, especially after the WWII, due to the rebirth of European economies first, and then to the developing countries industrial growth (China, but also India). The “speed” of that change is dangerous more than the change itself. The same it can be noticed for both N2O (+20%) and CH4(+140%), which are also more dangerous than CO2. NB: all the percentage here are evaluated as percentage of growth w.r.t. the beginning of Industrial Era. The following sentence: “…are rising quickly, anthropogenic perturbation of the global carbon cycle is considered to be the only responsible for causing the dramatic increase in CO2 of the contemporary Earth’s atmosphere [46,47]. ” has been modified as follows: “…and are rising quickly, anthropogenic perturbation of the global carbon cycle is considered to be the only responsible for causing the dramatic increase in CO2 as well as that of the other greenhouse gases in the contemporary Earth’s atmosphere Global Carbon Budget Archive [48,49].” Line 16 and discussions therein. The authors cite some basic papers about the carbon storage by tropical forests. Anyway, in my personal opinion, the authors are not giving any scientific proof about the huge interpretative correction they propose. Even if some other terms could be taken into account in the balance equation of CO2 atmospheric growth, that observation does not put into discussion that actual atmospheric CO2 rising trend is mainly connected to human activities: the last IPCC report (2018) call it a “virtually true” (p > 0.99) fact, thus testifying the common scientific belief of a strong significant correlation between extreme climate events (the growing of CO2 concentration in the atmosphere is just one of them) and the anthropogenic activity. For example, oceans are carbon sinks, but the actual situation is provoking an increase in oceans acidification. The main consequence is that oceans become carbon sources, since they are no more able to absorb CO2, and rather they start to emit it. Some extra sources, missing in the balance, can also be positive feedback of the human activity, again. The following sentence has been added: “It must be said that some extra sources, missing in the balance, can also be caused by the human activity, such as the increasing acidification of the oceans, which makes them carbon sources as well.” Paragraph 3 – Data Analysis The authors propose some other “sources” for CO2 emission in the atmosphere. Their idea is acceptable, but I ask them to smooth their conclusions, to be more precise and critical, especially in data analysis, and to be less generic. 1) The authors propose as extra source of atmospheric CO2 the one coming from tectonic activity. This is true, there are scientific evidences about the fact that changes in atmospheric concentration are connected to Earth’s tectonic activity, as the authors describe in the Introduction. Anyway, that’s true in “big” events, such as the events connected to tectonic plate formation, not for small “negligible” events. This is a first observation. Actually we are not experiencing plate formation events. 2) The authors introduce the concept of CO2 as precursor of seismic activity. That’s completely different, and it is one of the most controversial topics in recent scientific literature. Sure, in the presence of some huge earthquakes an increase of daily CO2 is locally recorded. Nevertheless, there are evidences of big tectonic activity (with connected extra CO2 emissions) which didn’t bring to any earthquake. So I ask to the authors not to use tectonic activity as synonymous of earthquakes and to consider several aspects they omit. First, CO2 emission related to tectonic activity depends on the concomitance of several factors, such as the presence of an anomalous heat flux below Earth’s crust, and the presence of crustal thinning. Several authors focused on localized CO2 degassing areas connected to seismic activity. On the contrary, the authors of this paper try to find global and general conclusions with a too limited approach, by comparing global CO2 atmospheric emissions with global seismic-moment release. I propose to the authors to consider and cite more basic papers about that, by starting from the precursors (King, 1986, Journal of Geophysical Research; Thomas, 1988, PAGEOPH). I propose some recent works that can be considered as starting point by the authors, from more general theories to local evidences: Martinelli and Dadomo (2017, Chemical Geology), Manga et. al (2012, Reviews of Geophysics), Barberio et. al (2017, Scientific Reports), Gherardi and Pierotti (2018, Applied Geochemistry), Pierotti et al. (2017, Physics and Chemistry of the Earth). 3) I ask the author to be more detailed. From which database the annual anthropogenic CO2emissions are taken? Please add a sentence about that, not only a link. The same for the atmospheric CO2 growth rate. I cannot follow the next 3 listed comments. The authors say that the downward trend of atmospheric CO2 (such as in 1988, 1993) is not reflected in a reduction of CO2 emissions, for example. Trends and oscillatory patterns have to be studied as a whole, when reading a time series. It is obvious that atmosphere is not answering immediately to a change in CO2 emissions, since CO2 belongs to the complex atmosphere-ocean-land CO2 cycle. There are “delays” between a perturbation and the answer to that perturbation. A change in the amplitude or frequency of an oscillatory pattern can or not be reflected in the trend. Or it can be reflected with some delay. In 2008 the CO2 growth rate underwent a reduction due to industrial crisis. Nevertheless, the global trend of CO2 growth rate was positive as well. The system absorbed the perturbation, without changing its global trend, or viceversa. As regards points 1 to 3, the text of Paragraph 3. Data Analysis has been modified as follows: “However, it can be argued that the atmosphere, as a part of a complex system which includes oceans and lands, may give a delayed answer to a perturbation, such as the change in CO2 emission. Instead, there are scientific evidences about changes in atmospheric composition connected to tectonic activity [56], and neutron emissions observed in correspondence to fracturing at laboratory and Earth’s scales. Consistently, the hypothesized LENR related to neutron emissions may be regarded as the cause of magnesium depletion and related carbon formation (according to table 12.2, page 176 in [31]) during events connected to tectonic plate formation. The consequent degassing of freshly formed CO2 depends on concomitant factors, such as the presence of anomalous heat flux below Earth’s crust and crustal thinning. Furthermore, since there are evidences of big tectonic activity (with related extra CO2 emissions) which didn’t bring to any earthquake, it also has to be said that tectonic activity and earthquakes are not synonymous. However, it is still worth investigating the possible relationship between the atmospheric CO2 growth rate and the global seismic-moment release rate (Nm yr−1, newton-metres per year), although several studies focused on temporary and localized CO2 emissions connected to seismic activity [57,58]. Therefore, a comparison among the rates of anthropogenic CO2 emission, atmospheric CO2 growth (refer to xls files in Global Carbon Budget Archive [48]), and global seismic-moment release (calculated from data provided by the USGS Earthquake Hazards Program [59])” Where: 56 King, C.H.. Gas Geochemistry Applied to Earthquake Prediction: An Overview. Journal Geophys Res 1986, 91(B12), 12269–12281. 57 Pierotti, L., Botti, F., D'Intinosante, V., Facc, G. Anomalous CO2 content in the Gallicano thermo-mineral spring (Serchio Valley, Italy) before the 21 June 2013, Alpi Apuane Earthquake (M = 5.2). Physics and Chemistry of the Earth 2015, Parts A/B/C, 85–86. 58 Gheradi, F., Pierotti, L. The suitability of the Pieve Fosciana hydrothermal system (Italy) as a detection site for geochemical seismic precursors. Applied Geochemistry 2018, 92, 166–179. 59 https://earthquake.usgs.gov/earthquakes/search/. 4) The authors perform a time series analysis on all the three series they study. First they detrend the time series, then they perform a FFT analysis. Which detrending methods have they used? Detrending is one of the most delicate procedure, when analyzing short and noisy time series, such as in that case. The following sentence has been modified: “…by subtracting the trend component (identified by a simple curve-fitting approach)…” Second, I cannot see any significance test which assesses the “real existence” of the 20 y, 3.7 y, and 2.5 yr. Did the authors consider some advanced spectral techniques? Which kind of background noise the authors assumed for this analysis? The idea of performing a spectral analysis on this three indicators can be interesting and should be encouraged. The authors have tested the spectral coherence analysis: “Instead, the 3.7-year periodicity is relevant both in atmospheric CO2 and in seismic-moment spectra, as well as other periodicities like spectral peaks at approximately 2.5 years (see Figs. 5(b) and (c)). Then, residuals are subjected also to coherence analysis [60] to find out more systematically on which frequencies the spectral coherence appears between an input x(t) and an output y(t) time series, i.e., on which frequencies the output responds on the input. The spectral coherence Cxy(f) (or normalized cross-spectral density) is defined as: Cxy(f) = |Gxy(f)|2·Gxx−1(f)·Gyy−1(f) (3) where Gxy(f) is the cross-spectral density between x and y, and Gxx(f) and Gyy(f) the auto-spectral density of x and y respectively. Here, Cxy(f) is calculated to estimate the degree of relationship between the perturbation x (the anthropogenic or the seismic time series) and the answer y (the atmospheric time series) in the frequency domain. Coherence diagrams of Fig. 6 differentiate mainly in the interval 0.2 – 0.4 yr−1, where the spectral coherence between seismic and atmospheric data is higher than that between anthropogenic and atmospheric data, consistently with the previous observations. High-coherence values between 0.2 and 0.4 yr−1 reflect relevant common cycles between 2.5 and 5 years in the spectrum of both seismic and atmospheric fluctuations, almost absent in the anthropogenic time series. Thus, short-range atmospheric CO2 fluctuations seems better correlated with seismic than anthropogenic activity. Unfortunately, the narrowness of the considered time window does not allow to grasp possible and, in a sense, expected long-term effects of the seismic activity.” Where: 60 Padron, E.; Melian, G., Marrero, R., Nolasco, D., Barrancos, J., Padilla, G. et al. Changes in the diffuse CO2 emission and relation to seismic activity in and around El Hierro, Canary Islands. Pure Appl. Geophys 2008, 165, 95–114. 5) A spectral analysis is neither a causality analysis nor a synchronization analysis. Even when I find a common cycle between two different indicators, I cannot say nothing about the reciprocal causality relation if I use a data-driven approach. Common cycles can indicate that both the indicators depend on a third one (spurious correlation), not that one of them influence the other. So I ask to the authors to smooth their conclusions, since no evidence is proved from the analysis. The abstract has been modified accordingly: “Assuming a correlation between such seismic and atmospheric fluctuations, the latter could be explained by cycles of worldwide seismicity, which would trigger massively LENR in the Earth’s Crust. In this framework, LENR from active faults could be considered as a relevant cause of carbon formation and degassing of freshly formed CO2 during seismic activity.” and by finally adding the following sentence: “However, further studies are necessary to validate the present hypothesis which, at the present time, mainly aims to stimulate debate on the models which regulates atmospheric CO2.” Conclusions have been modified by adding: “Obviously, in absence of any causality analysis, the performed spectral analysis does not permit to say anything conclusive about the reciprocal causality relation between these indicators. This study simply aims to open a debate on the models which regulates the atmospheric CO2 levels, by suggesting more detailed investigations of the oscillations in climate variables and their correlation with other variables connected to the Earth’s activity.” and deleting: “the present relationship between atmospheric and seismic variables appears to be rather robust during the last 50 years, and provides a new diagnostic tool for better understanding of the global carbon cycle. In conclusion, the time series analysis demonstrates the trending behavior of atmospheric CO2 growth rate in response to the anthropogenic emissions, whereas, in the light of LENR, atmospheric CO2 fluctuations can be ascribed to the cycles of the worldwide seismicity.”

Round 2

Reviewer 2 Report

The authors fully addressed my comments and suggestions.

I thank them for their clear, precise, and humble approach to my several comments, which aimed at improving the manuscript, at the best of my knowledge.

The paper has improved after the reciprocal discussion, even if, as the authors underline, further studies are necessary to validate the present hypothesis which, actually, aims to stimulate debate on the models which regulates atmospheric CO2. I'm favourable to any kind of debate.

I suggest to the authors to go on with this kind of research, but being aware of the several difficulties this study includes. I especially recommend them to pay attention when comparing global CO2 measurements with local effects (such as eartquakes) or millenial effects (such as faults mouvement). This can make the difference and can be an important approach to follow, in general: just be aware of the different time and spatial scales when comparing measurements.

Author Response

The authors were aware of all the drawbacks of their analysis. Moreover, they were able to clarify and to answer back to all my observations, especially concerning the methodology and the estimation of results significance. At this purpose, I suggest to the authors to apply more advanced spectral analysis methodologies, such as the Multi-taper Method, the Singular-Spectral Analysis (SSA), which are know to be able to extract significant oscillations (and periodic cycles) from short and noisy time series. Ref. to Ghil et. al, 2002, Advanced spectral methods for climatic time series and references therein. For future work a causality analysis could be taken into account, also. The paper has improved after the reciprocal discussion, even if, as the authors underline, further studies are necessary to validate the present hypothesis which, actually, aims to stimulate debate on the models which regulates atmospheric CO2. I'm favourable to any kind of debate. I suggest to the authors to go on with this kind of research, but being aware of the several difficulties this study includes. I especially recommend them to pay attention when comparing global CO2 measurements with local effects (such as eartquakes) or millenial effects (such as faults mouvement). This can make the difference and can be an important approach to follow, in general: just be aware of the different time and spatial scales when comparing measurements. The authors wish to thank the referee for her valuable comments that contributed to improuve the paper quality. In particular, possible future works on this topic will be based on the proposed methodologies for time series analysis

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