I believe there is indeed a growing trend in ecology and environmental science that the more deeply a study investigates a question—and the more comprehensive its technical approaches are—the more likely it is to convince editors and reviewers. Multilevel mechanistic validation, omics analyses, and global-scale datasets, which were once regarded as additional strengths, are gradually becoming implicit requirements for publication in high-impact journals. Studies that do not trace a causal chain down to the molecular level or lack large-scale data may therefore be considered insufficiently complete or important.
As a result, scientific publishing is increasingly turning into an arms race in which researchers compete by accumulating more resources, technologies, and layers of evidence.
Large research groups have the funding, personnel, technical platforms, and collaborative networks needed to combine multiple established methods, expand sample sizes, and add layers of omics evidence in order to construct an apparently comprehensive causal chain. Researchers with fewer resources, however, may struggle to publish in leading journals even when they have developed genuinely important scientific questions, simply because they cannot afford such extensive validation.
Truly original and important ideas are difficult to generate, whereas adding analytical layers using established techniques is comparatively straightforward when sufficient funding and personnel are available. When technical complexity and resource investment are treated as equivalent to scientific depth, this further reinforces the Matthew effect in science, allowing already powerful groups to become even stronger and making resource-intensive, technology-driven research increasingly disadvantageous for the majority of researchers.
A very good take on that problem, Guanghui, thanks for writing. I think you are spot on. We can only hope that other types of research don't disappear from the most 'desirable' journals.
This is a really important observation. There can be a tradeoff between reaching a high level of mechanistic resolution and external validity. In ecology, achieving a high level of mechanistic resolution often requires well-replicated experiments. These have a greater chance of getting published in high-impact journals than observational field studies. However, how often do we lose track of how relevant a signal picked up in the lab really is in nature? I think that our recent work on the novel weapons hypothesis and allelopathy can serve as a good example of how going down highly mechanistic approaches may be misleading in the true ecological sense.
Thanks, Pedro. Yes, you are making an excellent point here. I guess this is the part with which I have struggled: if you play this 'pinpointing causality' game to a great deal of detail you can't do other things. So it's clearly a trade-off in terms of effort. Maybe if it was 'worth it' would need to be checked on a case-by-case basis.
If anything, I worry about the lack of mechanistic resolution. Microbial ecology has become dominated by studies that describe phenomena, but never subsequently pursue mechanism: generate nucleic acid sequence data / run through various statistical routines --> point out clusters, 'signatures'
Thanks - this is the flip side of the argument. I agree with this view. There must be a Goldilocks zone in terms of causal resolution then: too little is clearly bad, too much could be overkill!?
"Normally, I would say, the mechanism is a thing that resides at the level immediately below the level at which a phenomenon is observed" -- I would strongly disagree with this. The philosophers of science Craven and Darden discuss this in their book, In Search of Mechanisms.
'For these ‘new mechanist’ philosophers, a causal mechanism comprises a heuristic explanatory device of a complex system that includes a description of component objects and how they interact (in space and time) to cause an observable phenomenon' (taken from https://thinkmicrobe.substack.com/p/mechanisms-as-explanations-in-biology ).
These 'objects' are nested within a multi-level hierarchy. If one digs deep enough, yes you may get to the molecular level; the depth of pursuit depends upon your research purpose. For me, I am most interested in principles of microbial ecology that have general (not necessarily universal) applicability so I would want more detail than that mycorrhizal fungi mobilize P for plants or that something destabilized soil aggregates. The 'how' is important and may in fact be relevant to other systems.
Thanks! I realize, also from other comments, that causality and mechanism are complex topics in philosophy of science.
I am also not disagreeing at all with the notion that it is important to dig deep into molecular mechanisms of phenomena - of course not. But that is also not the point of what I wrote. My point is that I have no seen several papers going way beyond the call of duty to explain a certain phenomenon in an experiment. Doing that detracts from other potential mechanisms that perhaps were not pursued all the way, and from the fact that in the real world situation, the mechanism may not be important. That is quite a different point, I believe. The problem is opportunity costs (and, as I wrote in the newsletter, setting perhaps the wrong standards and problems with other parts of the world staying competitive).
OK, sorry that I misunderstood your point. Could you direct me to those 'beyond the call of duty' papers (either here or via email). I would like to look at / deconstruct them for some of the things I have been thinking about re the 'philosophy' of microbial ecology
Thank you! I have only read the introductory summary material so far, but I would say this is primarily a 'plant physiological ecology' paper. If one is interested in the architecture of roots at the microscale, then digging down to abscisic acid distributions at the microscale seems meaningful in terms of understanding causal mechanism. RE plant/microbe interactions, I guess it shows how plant sensing can be 'generic' (acidification) rather than microbe-specific.
I think there is no better paper to illustrate my point. Opportunity costs, causal pathways not followed etc. If they had started the paper from the pH sensing point on, I would agree with your assessment, but the paper does start much broader. It follows a potentially pretty meaningless causal chain (in terms of broader applicability), but it is difficult to spot.
OK, I went through the sequence of experiments and I see your point. On the other hand, I was thrilled that someone was doing actual experiments rather than extract DNA/sequence/run through clustering algorithm of choice/speculate. In my opinion, the total 'opportunity costs' of that line of inquiry is much greater. My specific concern with metagenomics is that it can certainly identify 'core' genes (glycolysis, TCA cycle, amino acid biosynthetic pathways etc), but is poor at providing the *specificity* of the most ecologically interesting genes -- transporters and regulators
I agree, well-adapted study designs to research questions in a multidimensional research framework are definitively as relevant as going into the very detail. Nevertheless, multi-method approaches and high-resolution are needed to mechanistically link taxonomy and function in soil ecology. See e.g.: https://doi.org/10.1111/nph.19560
Thanks! I completely agree. In the paper you mention (which is a good one) the question is already quite focused on that particular link between AMF hyphae and the hyphosphere bacteria etc. What I am talking about is if you start from a phenomenon "higher up" in the hierarchy and then drill way, way down.
But I also agree that doing this drilling is not bad science, and I agree that we need a plurality of approaches. The worry is: will this be the new "norm". Because there are clearly opportunity costs (and others).
Technological progress has rendered complex experiments more feasible than a few years ago. But the question is “just because we can, should we go for these super elaborate experiments?” I have to say, that some papers leave me with the feeling that the authors designed their super experiment by targeting solely by the impact of the papers which the involved scientists wish to publish (a very concerning route, for me). That is, high-impact papers shape the type of experiments we read about …
These molecular experiments you mention immediately pose the question “how is this happening in nature/communities/habitats; how are these results materialised in nature?”. This question always made me think if “molecular ecology” actually exist!!! Can molecules behave ecologically by themselves? Do macroceological principles apply to these molecules? etc. These molecules belong to cells of organisms, and ecology is a matter of living cells/organisms … Or the term just means interpreting organism ecology via molecules (which to me is a different thing and should be called with a different name)…?
To me the scientific hypothesis of any experiment in ecology should by dictated by field observations and should be tested (to any possible degree) in the field.
Thanks for writing. Yes, this is thing: is the way we are expected to do science being reshaped right now.
Specifically for ecological questions there certainly are opportunity costs in focusing on mechanism to an extreme degree, exactly what you write: how important is that particular chain of events actually in nature. You can't do both, so pursuing the mechanism to such great detail means you can't check the external validity of your findings, the degree to which things apply in nature, etc.
Molecular ecology: this is an established term meaning the use of molecular tool to study ecological aspects, especially used in microbial ecology, since molecules is how we describe microbial communities. It's just a shorthand for "using molecular approaches to study microbial communities" for the most part.
I too observe this, however I apply a different "why". If we use topology as an analogy with elevation tied to experimental outcome, physics and mathematics occupy the deep basin with chemistry above. As you move higher in elevation you start to encounter mostly complex adaptive systems, -which are really difficult to describe accurately. So, you either drill down to something small and mechanistic or you take the poetic naturalist path, choose your level of description and your domain of applicability. Finding bridge language that allows a specialty to cross a saddle adds another complication. However, I have also seen a trend in this where saddles are becoming easier to cross for many disciplines, and I believe that is good for science.
I think the actual thing that 'worries' me is the opportunity costs that come with drilling down very deep into mechanism: you then cannot also examine under which conditions, in nature, your mechanism actually applies. For the case of environmental science, ecology, that is a serious trade-off.
I also do not think that this bad for science, as I wrote in the newsletter, but I think there are costs.
I agree, well-adapted study designs to research questions in a multidimensional research framework are definitively as relevant as going into the very detail. Nevertheless, multi-method approaches and high-resolution are needed to mechanistically link taxonomy and function in soil ecology. See e.g.: https://doi.org/10.1111/nph.19560
I believe there is indeed a growing trend in ecology and environmental science that the more deeply a study investigates a question—and the more comprehensive its technical approaches are—the more likely it is to convince editors and reviewers. Multilevel mechanistic validation, omics analyses, and global-scale datasets, which were once regarded as additional strengths, are gradually becoming implicit requirements for publication in high-impact journals. Studies that do not trace a causal chain down to the molecular level or lack large-scale data may therefore be considered insufficiently complete or important.
As a result, scientific publishing is increasingly turning into an arms race in which researchers compete by accumulating more resources, technologies, and layers of evidence.
Large research groups have the funding, personnel, technical platforms, and collaborative networks needed to combine multiple established methods, expand sample sizes, and add layers of omics evidence in order to construct an apparently comprehensive causal chain. Researchers with fewer resources, however, may struggle to publish in leading journals even when they have developed genuinely important scientific questions, simply because they cannot afford such extensive validation.
Truly original and important ideas are difficult to generate, whereas adding analytical layers using established techniques is comparatively straightforward when sufficient funding and personnel are available. When technical complexity and resource investment are treated as equivalent to scientific depth, this further reinforces the Matthew effect in science, allowing already powerful groups to become even stronger and making resource-intensive, technology-driven research increasingly disadvantageous for the majority of researchers.
A very good take on that problem, Guanghui, thanks for writing. I think you are spot on. We can only hope that other types of research don't disappear from the most 'desirable' journals.
This is a really important observation. There can be a tradeoff between reaching a high level of mechanistic resolution and external validity. In ecology, achieving a high level of mechanistic resolution often requires well-replicated experiments. These have a greater chance of getting published in high-impact journals than observational field studies. However, how often do we lose track of how relevant a signal picked up in the lab really is in nature? I think that our recent work on the novel weapons hypothesis and allelopathy can serve as a good example of how going down highly mechanistic approaches may be misleading in the true ecological sense.
Thanks, Pedro. Yes, you are making an excellent point here. I guess this is the part with which I have struggled: if you play this 'pinpointing causality' game to a great deal of detail you can't do other things. So it's clearly a trade-off in terms of effort. Maybe if it was 'worth it' would need to be checked on a case-by-case basis.
If anything, I worry about the lack of mechanistic resolution. Microbial ecology has become dominated by studies that describe phenomena, but never subsequently pursue mechanism: generate nucleic acid sequence data / run through various statistical routines --> point out clusters, 'signatures'
Thanks - this is the flip side of the argument. I agree with this view. There must be a Goldilocks zone in terms of causal resolution then: too little is clearly bad, too much could be overkill!?
"Normally, I would say, the mechanism is a thing that resides at the level immediately below the level at which a phenomenon is observed" -- I would strongly disagree with this. The philosophers of science Craven and Darden discuss this in their book, In Search of Mechanisms.
https://press.uchicago.edu/ucp/books/book/chicago/I/bo16123713.html
'For these ‘new mechanist’ philosophers, a causal mechanism comprises a heuristic explanatory device of a complex system that includes a description of component objects and how they interact (in space and time) to cause an observable phenomenon' (taken from https://thinkmicrobe.substack.com/p/mechanisms-as-explanations-in-biology ).
These 'objects' are nested within a multi-level hierarchy. If one digs deep enough, yes you may get to the molecular level; the depth of pursuit depends upon your research purpose. For me, I am most interested in principles of microbial ecology that have general (not necessarily universal) applicability so I would want more detail than that mycorrhizal fungi mobilize P for plants or that something destabilized soil aggregates. The 'how' is important and may in fact be relevant to other systems.
Thanks! I realize, also from other comments, that causality and mechanism are complex topics in philosophy of science.
I am also not disagreeing at all with the notion that it is important to dig deep into molecular mechanisms of phenomena - of course not. But that is also not the point of what I wrote. My point is that I have no seen several papers going way beyond the call of duty to explain a certain phenomenon in an experiment. Doing that detracts from other potential mechanisms that perhaps were not pursued all the way, and from the fact that in the real world situation, the mechanism may not be important. That is quite a different point, I believe. The problem is opportunity costs (and, as I wrote in the newsletter, setting perhaps the wrong standards and problems with other parts of the world staying competitive).
OK, sorry that I misunderstood your point. Could you direct me to those 'beyond the call of duty' papers (either here or via email). I would like to look at / deconstruct them for some of the things I have been thinking about re the 'philosophy' of microbial ecology
We're reading one in lab meeting today. https://www.science.org/doi/10.1126/science.adw6568
Thank you! I have only read the introductory summary material so far, but I would say this is primarily a 'plant physiological ecology' paper. If one is interested in the architecture of roots at the microscale, then digging down to abscisic acid distributions at the microscale seems meaningful in terms of understanding causal mechanism. RE plant/microbe interactions, I guess it shows how plant sensing can be 'generic' (acidification) rather than microbe-specific.
I think there is no better paper to illustrate my point. Opportunity costs, causal pathways not followed etc. If they had started the paper from the pH sensing point on, I would agree with your assessment, but the paper does start much broader. It follows a potentially pretty meaningless causal chain (in terms of broader applicability), but it is difficult to spot.
OK, I went through the sequence of experiments and I see your point. On the other hand, I was thrilled that someone was doing actual experiments rather than extract DNA/sequence/run through clustering algorithm of choice/speculate. In my opinion, the total 'opportunity costs' of that line of inquiry is much greater. My specific concern with metagenomics is that it can certainly identify 'core' genes (glycolysis, TCA cycle, amino acid biosynthetic pathways etc), but is poor at providing the *specificity* of the most ecologically interesting genes -- transporters and regulators
I agree, well-adapted study designs to research questions in a multidimensional research framework are definitively as relevant as going into the very detail. Nevertheless, multi-method approaches and high-resolution are needed to mechanistically link taxonomy and function in soil ecology. See e.g.: https://doi.org/10.1111/nph.19560
Thanks! I completely agree. In the paper you mention (which is a good one) the question is already quite focused on that particular link between AMF hyphae and the hyphosphere bacteria etc. What I am talking about is if you start from a phenomenon "higher up" in the hierarchy and then drill way, way down.
But I also agree that doing this drilling is not bad science, and I agree that we need a plurality of approaches. The worry is: will this be the new "norm". Because there are clearly opportunity costs (and others).
I don't know, I'm still thinking about it.
Yes, I have noticed what you have nicely put.
Technological progress has rendered complex experiments more feasible than a few years ago. But the question is “just because we can, should we go for these super elaborate experiments?” I have to say, that some papers leave me with the feeling that the authors designed their super experiment by targeting solely by the impact of the papers which the involved scientists wish to publish (a very concerning route, for me). That is, high-impact papers shape the type of experiments we read about …
These molecular experiments you mention immediately pose the question “how is this happening in nature/communities/habitats; how are these results materialised in nature?”. This question always made me think if “molecular ecology” actually exist!!! Can molecules behave ecologically by themselves? Do macroceological principles apply to these molecules? etc. These molecules belong to cells of organisms, and ecology is a matter of living cells/organisms … Or the term just means interpreting organism ecology via molecules (which to me is a different thing and should be called with a different name)…?
To me the scientific hypothesis of any experiment in ecology should by dictated by field observations and should be tested (to any possible degree) in the field.
Thanks for writing. Yes, this is thing: is the way we are expected to do science being reshaped right now.
Specifically for ecological questions there certainly are opportunity costs in focusing on mechanism to an extreme degree, exactly what you write: how important is that particular chain of events actually in nature. You can't do both, so pursuing the mechanism to such great detail means you can't check the external validity of your findings, the degree to which things apply in nature, etc.
Molecular ecology: this is an established term meaning the use of molecular tool to study ecological aspects, especially used in microbial ecology, since molecules is how we describe microbial communities. It's just a shorthand for "using molecular approaches to study microbial communities" for the most part.
I too observe this, however I apply a different "why". If we use topology as an analogy with elevation tied to experimental outcome, physics and mathematics occupy the deep basin with chemistry above. As you move higher in elevation you start to encounter mostly complex adaptive systems, -which are really difficult to describe accurately. So, you either drill down to something small and mechanistic or you take the poetic naturalist path, choose your level of description and your domain of applicability. Finding bridge language that allows a specialty to cross a saddle adds another complication. However, I have also seen a trend in this where saddles are becoming easier to cross for many disciplines, and I believe that is good for science.
Thanks for writing.
I think the actual thing that 'worries' me is the opportunity costs that come with drilling down very deep into mechanism: you then cannot also examine under which conditions, in nature, your mechanism actually applies. For the case of environmental science, ecology, that is a serious trade-off.
I also do not think that this bad for science, as I wrote in the newsletter, but I think there are costs.
I agree, well-adapted study designs to research questions in a multidimensional research framework are definitively as relevant as going into the very detail. Nevertheless, multi-method approaches and high-resolution are needed to mechanistically link taxonomy and function in soil ecology. See e.g.: https://doi.org/10.1111/nph.19560