Con el tiempo, estos Mapas Desmesurados no satisficieron y los Colegios de Cartógrafos levantaron un Mapa del Imperio, que tenía el tamaño del Imperio y coincidía puntualmente con él. Menos Adictas al Estudio de la Cartografía, las Generaciones Siguientes entendieron que ese dilatado Mapa era Inútil y no sin Impiedad lo entregaron a las Inclemencias del Sol y los Inviernos.
Jorge Luis Borges, Del Rigor en la Ciencia, 1946
A big part of our research program has been centered in understanding the rules that govern the assembly and function of microbial communities. To this end, we study communities that form in the lab under well controlled conditions in synthetic environments. This offers many advantages, perhaps most notably that we can alter the external environmental conditions in which assembly takes place, the diversity and composition of the initial inoculum, the degree of connectivity between habitats, the rate of nutrient and energy inflows, etc. The ability to control the environment is critical if we wish to tease apart questions such as how do multiple different environmental nutrients contribute to community composition, how temperature affects the taxonomic structure of microbial communities, or whether simple pairwise assembly rules may capture coexistence in a complex community.
A common critique we have received, as a weakness of this strategy, is that our experiments are conducted under artificial conditions, and therefore they represent just a “toy model” for the real world. Over the years, I have given several responses to this critique, which I would like to share in case they are useful to others.
The first one is that there is nothing wrong with toys! Toys can be extremely useful devices to help us figure out laws and principles of nature. Toys like pendulums and springs play a prominent role in physics, as they were instrumental to figure out the the very same laws that, to first approximation, govern the motion of planets and all other naturally occurring objects. Likewise, microbial consortia grown in the lab can be used to inquire about the existence of general rules and principles in microbial ecology. It is certainly fair to ask whether the rules that govern the stability, productivity and function of lab-grown microbial consortia should fundamentally differ from those that shape natural microbial ecosystems, whose scale, diversity, environmental complexity etc. are much larger. I do not know the answer yet. Many times in science “more is different”, and it is very possible that the principles that govern low-diversity consortia will in fact differ from those that shape natural ecosystems. But precisely to that point, studying how exactly they differ is an enormously important question. If such fundamental differences exist as the system grows in scale and diversity, isn’t it worth identifying and understanding how and why?
The second reason is practical in nature: microbial communities grown in artificial, man made environments such as fermentors can have enormous biotechnological potential, as many have argued before. These artificial microbial consortia are ecological communities in their own right, as legitimate a system of study (and as worth of our attention) as any other in ecology. Just their practical utility alone makes a good case for why studying such artificial microbial consortia is in fact very relevant, even if it were true that the lessons one learns by doing so do not translate in an obvious manner to natural microbial ecosystems.
Related to this response, I would also argue that studying the ecology of biotechnologically useful consortia can lead to theory whose applications extend well beyond the realm of artificial systems. The laws of thermodynamics were discovered largely by scientists studying engines, pistons, and other industrial devices at the dawn of the industrial revolution. The gases that one finds in these settings are far more controlled than those that form, say, the clouds in the sky. Yet, the thermodynamic principles that rule both of them, at equilibrium, are the same. Remarkably, thermodynamic laws reflect relationships between emergent properties of systems containing many particles, e.g. the law of Guy Lussac describes the relationship between the pressure and temperature of a gas at constant volume. Are there similar relationships between emergent ecosystem properties? Even if one is of the persuasion that such laws do not exist, isn’t it worth putting the effort in making sure? Microbial consortia studied in the lab are ideal systems to search for the relationships between emergent properties, as similar to engines and pistons, they allow for a fluid dialog between theory and quantitative experiment.
While I draw from physics quite a lot in the previous examples, there is also plenty of precedent in biology for studying microbial consortia under artificial conditions. A lot of what we know about proteins and protein function was figured out by isolating proteins from their “natural environment” (e.g. the cytoplasm of a cell) and placing them under well controlled laboratory conditions that could be manipulated and their effect unambiguously monitored. The fields of enzymology, protein folding, molecular motors, etc. have their foundation on such experiments. I often argue that the interior of a cell, from the perspective of a population of proteins, may not look much less complex than an ecosystem does from the perspective of a population of individuals. Is there a solid argument why such a reductionist approach is reasonable for proteins but not for microbial cells?
I am aware of the many limitations of synthetic consortia, and the dangers of over-generalizing any findings one makes. A microbial consortium formed in the lab is not meant to be a wet-simulation of the soil microbiome, let alone of guppies in a stream, or hippos in the savanna, and extending the lessons learned from one to the other is far from straightforward. There is strong evidence that the functions of microbial consortia are highly sensitive to the environment, and a consortium that exhibits a particular function in the lab should not be trivially expected to maintain it if we simply spray it onto, say, the leaves of a plant. While being cautious in this regard is definitely a good idea, this does not argue against reductionism altogether. The lessons learned from reductionist experiments in protein biochemistry can and have been challenged by later studies. Chaperones were not present in the initial Anfinsen experiment, and many proteins require them to fold properly. While Anfinsen's dogma was later qualified, few would now argue that it was not a critical step in the field. Moreover, the study of chaperones has also benefited from in vitro experiments, arguing for their continuous relevance to modify incomplete pictures. Similarly, synthetic communities lacking a particular element, say phages, protists, or spatial structure, may give us an incomplete view of the assembly process, but this is not a lethal flaw. Rather, I would argue that it is an advantage as, by construction, synthetic microbial communities allow for the systematic addition and removal of different components of a natural microbiome.
In sum, I argue here that studying microbial communities under well controlled, artificial laboratory conditions may be as fruitful and useful as similar reductionist approaches have been in other areas of science, both in biology and beyond. The key question is not whether they should be studied or not, for the answer I argue is yes, but rather "what do we use them for". Nobody I know who studies microbial communities in the laboratory is under any delusions that their low-diversity consortia grown under stable laboratory conditions are a faithful representation of "the real thing in nature". Attempting to reconstruct the soil or the human gut in the lab is practically impossible, and it may be pointless too. No matter how many components and details one adds, any laboratory system will never be "the real thing", as some detail or another will always be missing. As in the famed Borges story, only the real thing is "the real thing". If one is able to capture essential features of an ecosystem under highly artificial conditions, this is a massive step forward. But I would argue that the main use of Synthetic communities is not to simulate a particular ecosystem, rather, it is to find general principles that rule community assembly and community function.
As argued above, synthetic communities not only offer an excellent testing ground for theory, but they also have practical utility of their own. They are an essential component of the scientific process in microbial ecology, which also includes of course observational and manipulative studies of natural communities in their natural habitats. If rules and generalities exist, and we wish to find them, studying artificial communities is a must.
In our lab’s most recent paper, we find that most members of stable enrichment communities do not coexist with one another in pairwise coculture, and we also find that competitive exclusion is strongly hierarchical: the most competitive species outcompetes most others, the second most competitive outcompetes most of the ones below (but is oucompeted by the top competitor) and so on.
These two findings can be summarized in a way that I find useful: most bacterial species are driven extinct by the most competitive members of their communities when they face them alone in direct, head-to-head competition. Yet, when the other community members are present too, extinction is avoided and all species coexist stably. As they would say in La Bola de Cristal: “solo no puedes, con amigos sí”.
Our study was motivated by a remarkable paper by Jonathan Friedman, Logan Higgins & Jeff Gore. Jonathan and his coworkers took a (semi-random) set of soil bacteria and grew them all in pairwise co-culture under in vitro conditions. They found that the outcome of these bacterial competitions would predict a species presence or absence in more complex assemblages: all species that ended up coexisting together in multispecies communities would also coexist with one another in pairwise coculture. I would want to encourage folks who are not familiar with their paper to go to the source directly and read it. Typical of Jonathan’s papers, this article is beautifully written, rigorous, and thought-provoking, and it prompted us to ask if this additive “rule of assembly” would also work for species that had a prior history of stable coexistence in the same habitat where the pairwise competitions would be carried out.
Luckily, in a previous paper we had developed what we thought was an ideal system to address this question, as we had assembled a large number of stable enrichment communities in minimal media with glucose as the only added carbon source. The diversity of these communities is low enough that we could isolate most of their members and compete every pair under the exact same conditions as in their community of origin. We carried out this experiment for 12 of these communities, which contained between 3 and 10 species each, and developed a machine learning approach to quantify the composition of each pairwise co-culture after ~ 60 generations. As summarized above, the additive assembly rule would not have predicted the composition of our experimental communities, and competitive exclusion was the most common outcome.
This prompts the question of under what conditions should we expect community assembly to be an emergent property of the community, as opposed to a simple additive affair. What is the main difference between both experiments? Is it the previous history of coexistence under identical culture conditions? Or is it related to growth conditions (nutrients, habitat, buffering, etc)? Are communities assembled from a highly diverse initial pool (as in our own experiments) fundamentally different from those assembled from a low-diversity initial pool (as in Friedman et al)? When additive, pairwise assembly rules fail to predict community composition, is it possible to formulate non-additive pairwise rules that would do the trick? If not, would third-order assembly rules work out, or is it just hopeless? Does the complexity of community assembly reside in the particular network of largely pairwise interactions, or is it the consequence of higher-order interactions between species?
There are clearly many open questions that arise from the apparent discrepancy in results between both experiments. Addressing them will benefit from a combination of theoretical models and experiments, and we hope that our study and the tools and model empirical systems we have developed here will be of help in this goal.
Should we expect to be surprised by a new study in order to be persuaded of its significance? The knee-jerk reaction to this question may differ for various individuals, possibly reflecting their scientific background. In at least some fields of biology, it is not uncommon to receive scalding comments from a colleague or, even worse, a reviewer's report expressing their concern about the lack of surprise regarding the results of a new study. However, in other areas of science, surprise does not seem to carry the same weight. It would be difficult to argue that the detection of the Higgs boson at CERN in 2012, or the observation of gravitational waves by LIGO in 2015, were surprising at all. Both of these empirical findings confirmed theoretical predictions and were rightly considered monumental successes of the scientific enterprise. Why are things so different in some fields of biology?
To make progress in answering this question, it would be productive to clarify what we mean by surprise. The Merriam-Webster dictionary defines surprise as "the feeling caused by something unexpected or unusual." Surprise is, therefore, a human feeling, an emotion that we experience when reality does not match our expectations. As it is true of most feelings, surprise (or lack thereof) would be a valid initial response to any kind of news. Yet, feelings are unavoidably subjective and personal, and this is a good reason for being cautious at using them to judge scientific results.
Surprise is not necessary in science. As outlined above, the history of science is full of celebrated experiments that provided confirmation of theoretical expectations. The empirical detection of gravitational waves or the finding of the Higgs boson were significant precisely because they agreed with longstanding theoretical predictions. Because these findings were expected in light of currently accepted theory, they could not be qualified as surprising. Rather, they are a necessary consequence of the theory itself, which may have had to be corrected had the outcome of the experiments been different.
Empirically confirming theoretical predictions is enormously valuable, and I would claim we need more of it, not less. While nobody would argue for experiments that merely confirm well-established knowledge in areas where similar experiments have been carried out before, theories often have boundaries, and finding and confirming them is an essential part of the scientific process. We cannot adequately chart these boundaries if we do not test theoretical expectations in different scenarios. I worry that an undeserved emphasis on surprise would undermine such studies, which may be deemed unworthy of submission for peer review and thus from disseminating them to the community.
Surprise is not (always) sufficient. Because surprise is a reaction to an unexpected empirical observation, it is critical that we identify where our expectations came from in the first place. While ideally our expectations would derive from a predictive formal theory, it is legitimate that expectations may also come from past experience, i.e. from well-established empirical distributions of expected outcomes. In such instance, one may feel surprised by any event that is rare enough, from observing a shooting star to finding a four-leaf clover. It is uncommon in my daily life to encounter a person standing seven feet tall for they are few in Spain. Yet, surprised as I may be, meeting one such person would not force us to question the distribution of viable individual sizes in our species (as would be the case if a twenty feet tall human happened to walk into my lab), and it is therefore not the subject of scientific inquiry. The emphasis should be on whether the distribution of heights needs to be revised, not on whether we find an event at its tails, even if this would indeed be surprising. My argument does not require any particular shape for the distribution and would equally apply to scale-free ones.
Even in circumstances where we see something we had never observed before, such as when a naturalist discovers a new species, surprise would be a poor gauge for scientific relevance. Discovering a new species is a precious addition to the scientific knowledge regardless of whether we found it in a well-explored habitat, where we may think we have already charted and documented its biodiversity (thus, the discovery would be surprising), or whether we find it in less explored parts of our planet. In the latter case, since we are aware that our knowledge of that area's biodiversity is incomplete, the extent to which discovering a new species is surprising may depend on whether we had any reasons to believe that no new species should have been found. But this is besides the point. The value of discovering a new type of organism is self-evident, and it does not reside in whatever our expectations were. If the species is discovered in a habitat that we believed we had fully charted already, all this tells us is that we were wrong and our census was incomplete. While this may be surprising, its value pales compared with the discovery of a new life form.
Finally, many areas of biology are at a stage where a strongly predictive theory, either based on theory or based on prior experience, does not quite exist yet. Some fields are still in an exploratory phase, where we simply lack strong expectations before conducting an experiment. If we have no way to estimate the likelihood of a particular outcome before conducting an experiment, we cannot claim to be neither surprised nor unsurprised no matter what we find. The outcome of exploratory experiments cannot be surprising, but this does not mean they are not significant. The data and evidence contributed by such experiments are necessary to, slowly, build a set of expectations that will guide future work, laying the ground to building a predictive theory. It is clear that this would be a valuable addition to the scientific literature.
We should be skeptical of surprise and question where it comes from. When strong predictive theory does not exist, it is often tempting to make ourselves believe that we could have expected the outcome of an experiment before conducting the study. It is indeed common to hear oneself saying "I knew it!" after being confronted with a piece of news, scientific or not. The question we should ask ourselves immediately after such a thought is, "did I really know it beforehand?". Fooling ourselves that we could have predicted an event after the fact is exceptionally easy when our theories about the world are implicit and our priors are weak. When confronted with the inevitable randomness of life events, we often face situations where an outcome and its alternative are both reasonably likely. For instance, before a presidential election, the polls are often close enough that, even when a candidate is favored to win, the other candidate has a pretty decent likelihood to win as well. It is therefore very reasonable to entertain both possibilities in our head before the votes are counted and, once the outcome is announced, feel that the result has confirmed what we thought would happen. This is because we had indeed contemplated that the final outcome was possible, before flickering to the alternative. We can thus convince ourselves that we knew things would turn out the way they did, and we are not exactly lying.
We are not exactly lying to ourselves, not entirely, but we are still fooling ourselves when we do that. Not only do most of us indulge in this habit in our day-to-day lives, but we all do it often, and it is thus easy for scientists, most of whom appear to be humans after all, to carry the habit to our workplace. This is particularly dangerous for those of us who work in fields of science where the available theories do not generally make strong predictions. No matter how smart, knowledgeable, and experienced we are, I contend that unless the expectation comes from an objective, ideally quantitative theory that is widely available and external to us, we should be careful about our feelings of surprise.
What should one do when we feel unsurprised by a new empirical result in biology? I argue above that placing the focus on the surprise factor of a finding is not productive. In fields where a predictive theory is available, the importance of a result resides in whether and how our findings should update this theory. In fields that do not yet have such a strong predictive theory, how can we even decide if a finding is surprising or not? I am open to being convinced of the contrary, but my current stand is that we could simply disregard surprise as a factor to judge scientific results. If we insist on using it, I suggest that we at least try to be honest with ourselves and ask whether there exists any theory that could have predicted exactly what the study reports. Goes without saying that we cannot cheat, as building strawmen and steelmen is easy and tempting, but these are falacies. We must confront our internal belief that the outcome could have been predicted with some external evidence that this is indeed true. Which theory would have predicted it? Where is it published? If the existing theory could have predicted the reported outcome of an experiment, then it should be able to predict as well the effect of at least some perturbations we could make to the experimental design. For instance, one would expect that such a predictive theory will be able to tell us what would happen if we decided to change or perturb (within reason, as even strong theory has its limits) the initial conditions of the experiment, say the temperature, the pH, the chemical composition of the environment, etc. If such a theory does not exist, then I contend that surprise is simply not a good proxy for scientific significance.
In the above, I caution against surprise not because I think that experiencing it is useless, as heuristics offer advantages in many contexts, but rather because I do not trust it for the particular purpose of evaluating the merits of a research study. The initial emotional response to learning about a new result may simply reflect our biases (which may or may not be correct) and can be affected and confounded by other equally valid feelings: from envy to self-interest. It may also come from a good place, but still misled by our tendency to overestimate what we actually know, which is different from what we can rationalize. The key argument is that we should be critical with our expectations and make sure we can identify where they come from, and that it is easy to fool oneself about our ability to have predicted the observed outcome. Everything can seem obvious after the fact, and it often does.