the Creative Commons Attribution 4.0 License.
the Creative Commons Attribution 4.0 License.
| 12 Sep 2025
Why a mechanistic theory of soils is crucially important: Another line of supportive arguments exists, seldom invoked in soil science
Abstract. In the last few decades, the sizable effort that has been devoted to the mechanistic, quantitative description of soil processes has been justified on the grounds that theories and models help us understand how soils function, and also predict how, e.g., they are likely to adjust in the future to environmental change. The argument, familiar to physicists, that theories uniquely determine what should be measured has rarely if ever been invoked in the soil science literature. On the contrary, to enable the classification and mapping of soil, enormous amounts of “theory-free” data have been and continue to be amassed by soil scientists. In this general context, the key objective of the present Forum article is to argue that the accumulation of more “theory-free” data, in particular to allow the application of artificial intelligence methods, is not sensible at this stage, and that the development of improved theories of soil processes is crucial, to provide guidance about the type of measurements that should be performed. Hopefully, this Forum article will stimulate a debate on this issue, and will lead to a much needed intensification of theoretical research and modelling in soil science.
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Status: final response (author comments only)
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RC1: 'Comment on egusphere-2025-4250', Göran Ågren, 16 Oct 2025
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AC1: 'Reply on RC1', Philippe C. Baveye, 19 Oct 2025
Thank you, Professor Göran Ågren, for these interesting comments.
I agree that, to anyone with a physics background, what I wrote will appear “rather obvious”. Therefore, to a large extent, my targeted audience consists of the non-physicists in the soil science community, and especially among them, the colleagues who have recently started promoting the adoption of machine learning and artificial intelligence as “the” way forward.
Thank you for pointing out your article with Ernesto Bosatta. I must admit I was not aware of its existence, as I do not frequently scan the pages of American Naturalist. As soon as I manage to get hold of a copy of this article, I will read it in detail, and will mention it in the revised version of my Forum piece.
Your point about the complexity of models becoming rapidly unmanageable for most soil scientists, as soon as one goes from the relatively simple discrete formulations to the more complicated, continuous ones, is very well taken. Most soil physicists giving seminars to mixed audiences have experienced the rapid glazing-over of the eyes of the non-mathematically-minded attendees as soon as an equation appears on the screen, soil microbiologists being the worst in many ways. This is no doubt a reflection of how the education of soil scientists has been approached in the past, with advanced mathematics being considered unnecessary for most, except soil physicists. One approach to resolving the problem is, as you suggest, for soil physicists to participate in soil science studies, but from my experience, interdisciplinary research works best when participants know sufficiently about what the others are equipped to do to understand what is going on overall in the research. Soil physicists and chemists need to know about the intricacies of genome sequencing, and soil microbiologists need to be comfortable with partial differential equations. It would not necessarily help if at the point of describing things quantitatively, participants just turned to soil physicists and told them “OK, now you do your magic, and it’s a wrap…” Theory and model development will have to be a collective effort, which means we need to rethink the education of the next generation of soil scientists, so that everyone is quantitatively literate. Nothing new there; Some of us have been writing it consistently for the last 30 years.
Citation: https://doi.org/10.5194/egusphere-2025-4250-AC1
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AC1: 'Reply on RC1', Philippe C. Baveye, 19 Oct 2025
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RC2: 'Comment on egusphere-2025-4250', Anonymous Referee #2, 19 Oct 2025
While reading this manuscript, I found myself keeping nodding and agreeing strongly with the message elaborated by Dr. Baveye that soil science needs a mechanistic theory of soils to guide future measurement. He explained that, because correlation is not equivalent to causality, simply piling up more data that are just easy to collect won’t give us the predictive power and understanding we aspire to achieve, even when such big data are analyzed using machine learning and AI, which by and large work based on correlation. (Thinking along the same line, I often speak to my colleagues that, unlike psychological games, repeating the same wrong approach thousand times won’t make the answer correct.) Moreover, he argues that having a mechanistic theory will save resources so that measurement can be targeted at more important variables and avoid collecting variables that are only of tangential importance. He also lay out a working draft (Figure 1) that a mechanistic model can be developed from bottom-up scaling from pore-scale dynamics to ecosystem level dynamics.
While I fully agree with what Dr. Baveye has advocated, I think it will be very helpful if he can elaborate more on how he thinks the mechanistic theory should look like, or more specifically, what key myths the mechanistic theory should be able to explain? The history of physics suggests a successful theory can only be constructed when the subject or mystery to be explained is clearly stated. For instance, the legendary apple triggered Newton’s theory of gravitation, which solved the myths shown in Tycho Brahe’s big data on the motions of different celestial bodies. Meanwhile, the Black-Body Radiation and the Ultraviolet Catastrophe motivated the development of quantum mechanics. Similar stories occurred to Maxwell’s development of theory of electromagnetics. However, personally, as someone who by serendipity migrated from physics into soil science, I think the subject in soil science is often vague or to some extent too immense to summarize: it literally includes everything one can find in physics, and includes the live and dead, soft and hard, big and small, and even (animals’) psychological warfare. So where should the mechanistic theory focus on? I think, if there is a list of essential soil science myths to be explained, then the mechanistic theory is more likely to be identified.
Citation: https://doi.org/10.5194/egusphere-2025-4250-RC2 -
AC2: 'Reply on RC2', Philippe C. Baveye, 23 Oct 2025
I am very grateful to Referee #2 for his/her positive comments and for "agreeing strongly" with the message of my Forum piece.
With respect to the second paragraph of Referee #2’s comment, I am not sure I agree with the statement that “the subject in soil science is often vague or to some extent too immense to summarize”. I do not think that the subject in itself is vague or too immense. I believe, instead, that soil processes have often been approached from a perspective that researchers in other disciplines, and especially in physics, would consider non-scientific. To a large extent, the fact that a “data amassing” approach has been adopted for a very long time in soil science has allowed myths to proliferate, which would have been avoided, I think almost entirely, if a more rigorous, mechanistic path had been systematically followed. For example, some researchers have advocated that the incorporation of biochars in soils improves soil structure. This claim has been backed by an accumulation of correlation data showing that in soils amended with biochars, soil structure (i.e., really, aggregate stability) is better. Any researcher with a mechanistic bend would not be satisfied with such evidence, and would try to come up with a detailed explanation of the effect, i.e., would try to find the exact mechanism(s) by which biochars, which are fundamentally inert materials, could improve soil structure. In looking for this mechanism, one may find out that biochars themselves do absolutely nothing, but the various chemical compounds that biochars contain initially as a result of their pyrolysis contribute significantly to stimulate microbial activity, and thereby improve soil structure in the short-run. If that is the case, one would expect the effect to disappear after a few years. A related myth is that biochars increase crop yields. Again, a mechanistically-based approach, trying to uncover causes rather than correlations, might have revealed years ago that biochars do not have much of an effect in the long run on yields. Because this approach was not adopted, the myth has been allowed to go on, unchecked (see in this respect the recent critical article by Chaplot et al., 2025).
In that context, I agree with the referee that a list of essential soil science myths would be a good addition to the text, to provide an idea of what some of the key ingredients of models of soils should be. The problem I foresee in creating such a list is that there are many such myths in soil science, related, e.g., to topics as varied as the importance of the elusive “aggregates” in soils (e.g., Vogel et al., 2022; Baveye et al., 2022), the fuzzily-defined notion of “soil health” (e.g., Harris et al., 2022), or the promise of metagenomics to help us quantitatively describe microbially-mediated processes in soils, that establishing an exhaustive list would be a daunting endeavour. Nevertheless, I agree that mentioning a few examples, in a number of subdisciplines of soil science, to illustrate further the crucial need for a mechanistic theory, would be very worthwhile, and I will try to do that in the revised version of the manuscript.
References
Baveye, P. C., Balseiro-Romero, M., Bottinelli, N., Briones, M., Capowiez, Y., Garnier, P., ... & Vogel, H. J. (2022). Lessons from a landmark 1991 article on soil structure: distinct precedence of non-destructive assessment and benefits of fresh perspectives in soil research. Soil Research, 60(4), 321-336.
Chaplot, V., Baveye, P., Guenon, R., Le Guyader, E., Minasny, B., & Srivastava, A. K. (2025). Biochars improve agricultural production: The evidence base is limited. Pedosphere, 35(1), 295-298.
Harris, J. A., Evans, D. L., & Mooney, S. J. (2022). A new theory for soil health. European Journal of Soil Science, 73(4), e13292.
Vogel, H. J., Balseiro‐Romero, M., Kravchenko, A., Otten, W., Pot, V., Schlüter, S., ... & Baveye, P. C. (2022). A holistic perspective on soil architecture is needed as a key to soil functions. European Journal of Soil Science, 73(1), e13152.
Citation: https://doi.org/10.5194/egusphere-2025-4250-AC2
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AC2: 'Reply on RC2', Philippe C. Baveye, 23 Oct 2025
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AC3: 'Comment on egusphere-2025-4250', Philippe C. Baveye, 29 Oct 2025
Dear Anne,
As my replies to the two reviewers suggested, I fully agree to take on board the points that they mention, namely for reviewer #1, the fact that the complexification of theory may make it somewhat difficult for soil scientists who do not have a sufficient mathematical background to handle, and for Reviewer #2, that it would be nice to mention "myths" in soil science, to provide a target in the development of the "theory of soils".
My answer to reviewer #2 comes first in the text. I have added a paragraph on lines 84-99 in Section 2, which reads:
"More fundamentally, one could argue that, over the years, the focus of many researchers in soil science on “theory-free” data and on potentially groundless statistical correlations, rather than on trying to understand and describe quantitatively the basic mechanisms involved in soil processes, has allowed the proliferation of what one of the reviewers of the present article refers to as “myths”. Examples abound and include, to name only a few, the alleged positive impacts of biochars on soil structure and crop yields, of soil biodiversity on a number of soil functions, or of some aspects of the metagenomic make-up of soils on the activity of microorganisms. For example, if researchers had from the onset tried to understand at a basic level by what mechanisms biochars might improve crop yields, they might very well have discovered that biochars by themselves do absolutely nothing, but that it is the various nutrients that biochars contain initially as a result of their pyrolysis that have an effect on crop yields, and only for a short period of time. In order to ascertain this, a full characterization of the physical and chemical properties of biochars (e.g., Baveye, 2014), clear testable hypotheses about mechanisms, and targeted experiments with proper controls would have been required. A recent analysis of the literature on the topic shows that, largely, this research has yet to be carried out and no real conclusion can be drawn on this topic at present (Chaplot et al., 2025). The same applies to the extent to which the incorporation in soils of fresh organic matter really contributes to the long-term “sequestration” of carbon in soils (e.g., Chaplot and Smith, 2023, 2024; Baveye et al., 2023). At another level, one might also argue that the fact that many researchers are content with merely identifying correlations between parameters explains why “soil health” remains so poorly conceptualized at this point (e.g., Harris et al., 2022; Baveye et al., 2025)."
To address Reviewer #1's comment, and also to some extent Reviewer #2's, I have modified the end of section 3, which now reads: "
One of the reviewers of this article, referring to past examples in physics and astronomy, suggested that a good way to proceed toward the development of a mechanistic theory of soils would be to first list the various “myths” currently being circulated in our discipline, to get an idea of what the theory should look like and what it should be able to explain. Even though listing all, or even a good portion, of the numerous “myths” about soils would be a dauntingly time-consuming endeavour, focusing on some of them might indeed be a good way forward. In essence, one might consider that this is indeed what motivated the work on the microscale description of soil processes over the last two decades (e.g., review in Baveye et al., 2018). Realization that traditional kinetic equations involving macroscopic measurements of SOM content and soil biomass could not help us predict how much actual mineralization of SOM would take place, prompted a number of us to try to quantify the microscale spatial distribution of SOM and microorganisms. A particular difficulty with this type of research is caused by the fact that, in soils at the microscale, physical, mineralogical, (bio)chemical, and biological processes interact intimately, and cannot be studied independently.
To make progress in understanding these interactions, research therefore needs to be interdisciplinary and requires a break with the very much mono-disciplinary focus that continues to dominate soil science (e.g., Baveye and Wander, 2019; Baveye et al., 2024). We need to train soil scientists who are equipped to engage in this type of research. One can argue that this is still not the case, even though the topic has been discussed for decades. In addition, the development of a comprehensive theory of soils will require soil scientists to be far more quantitatively literate than they tend to be at the moment, except for soil physicists. Perhaps one of the reasons there has been so much emphasis on mere statistical correlations in soil science up to now is that, to a large extent, they correspond to the level of mathematical complexity that most soil scientists can handle. As pointed out by the other reviewer of this article, Professor Göran Ågren, and as illustrated clearly in Bosatta and Ågren (1991), “to get from the many conventional discrete pool models of soil organic matter transformations to models based on process understanding raises the level of mathematical knowledge considerably”. One possible solution to the problem might be to involve soil physicists closely in any interdisciplinary research effort on soils. However, I would contend, based on my experience over the last four decades, that interdisciplinary research yields valuable results only if all participants share a common language. It would not do in this context if at the point of describing things quantitatively in the work, participants just turned to soil physicists and told them “OK, now you do your magic, and it’s a wrap…”"
Aside from modifications to these two portions of the text, I have made a number of very minor edits as well, so that the whole text reads well. In particular, in the introduction, I have alluded to a call in the ecology literature a decade ago, to develop a "theory of ecology". I think that this call largely parallels the one I am trying to support in my text, so I thought it would be a good idea to mention it.
The revised manuscript is ready and can be submitted at any time. I believe that, thanks to the reviewers' constructive inputs, the manuscript's message has been significantly improved. Hopefully, it will stimulate a debate in our discipline. That is the sole goal I am pursuing.
Best regards.
Philippe
Citation: https://doi.org/10.5194/egusphere-2025-4250-AC3
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General comments
What the author argues about is rather obvious. Having a theoretical basis for performing experimental studies makes them more structured and efficient. This paper can hopefully inspire some scientists to take some time to develop theories before embarking on extensive experimental studies. A problem I see here is the weak mathematical training soil scientists have. As an example, to get from the many conventional discrete pool models of soil organic matter transformations to models based on process understanding raises the level of mathematical knowledge considerably ( see papers on a continuous description rather than discrete ones, e.g. Bosatta, E. Ågren, G I. 1991. Dynamics of carbon and nitrogen in the organic matter of the soil: A generic theory. The American Naturalist 138: 227-245). A possible solution to this problem could be to invite physicists to participate in soil science studies.