Two Visions of Ecological Research

Let us assume for the moment that the goal of scientific ecology is to understand the reasons for changes in the distribution and abundance of animals, plants, and microbes. If you do not think this is our main agenda, perhaps you should not read further.

The conventional, old paradigm to achieve this goal is to obtain a good description of the natural history of the organisms of interest in a population or community, define the food web they operate within, and then determine by observations or manipulations the parameters that limit its distribution and abundance. This can be difficult to achieve in rich food webs with many species, and in systems in which the species are not yet taxonomically described, and particularly in microbe communities. Consequently a prerequisite of this paradigm is to have good taxonomy and to be able to recognize species X versus species Y. A whole variety of techniques can be used for this taxonomy, including morphology (the traditional approach) and genetics. Using this approach ecologists over the past 90 years have made much progress in deriving some tentative explanations for the changes that occur in populations and communities. If there has been a problem with this approach, it is largely because of disagreements about what data are sufficient to test hypothesis X, and whether the results of manipulation Y are convincing. A great deal of the accumulated data obtained with this approach has been useful to fisheries management, wildlife management, pest control, and agricultural production.

The new metagenomics paradigm, to use one label, suggests that this old approach is not getting us anywhere fast enough for microbial communities, and we need to forget most of this nonsense and get into sequencing, particularly for microbial communities. New improvements in the speed of doing this work makes it feasible. The question I wish to address here is not the validity or the great improvements in genetic analysis, but rather whether or not this approach can replace the conventional old paradigm. I appreciate that if we grab a sample of mud, water, or the bugs in an insect trap and grind it all up, and run it through these amazing sequencing machines, we get a very great amount of data. We then might try to associate some of these kinds of data with particular ‘species’ and this may well work in groups for which the morphological species are well described. But what do we do about the undescribed sequences? We know that microbial diversity is much higher than what we can currently culture in the laboratory. We can make rules about what to call unknown unit A, unknown unit B, and so on. That is fine, but now what? We are in some sense back where Linnaeus was in 1753 in giving names to plants.

Now comes the difficult bit. Do we just take the metagenomics approach and tack it on to the conventional approach, using unknown A, unknown B, etc. instead of Pseudomonas flavescens or Bacillus licheniformis? We cannot get very far this way because the first thing we need to decide is does unknown A a primary producer or unknown B a decomposer of complex organic molecules? So perhaps this leads us to invent a whole new taxonomy to replace the old one. But perhaps we will go another way to say we will answer questions with the new system like is this pond ecosystem changing in response to global warming or nutrient additions? We can describe many system shifts in DNA-terminology but will we have any knowledge of what they mean or how management might change these trends? We could work all this out in the long term I presume. So I guess my confusion is largely exactly which set of hypotheses are you going to test with the new metagenomics paradigm? I can see a great deal of alpha-descriptive information being captured but I am not sure where to go from there. My challenge to the developers of the new paradigm is to list a set of problems in the Earth’s ecosystems for which this new paradigm could provide better answers more quickly than the old approach.

Microbial ecology is certainly much more difficult to carry out than traditional ecology on macroscopic animals and plants. As such it should be able to use new technology that can improve understanding of the structure and function of microbe communities. All new advances in technology are helpful for solving some ecological problems and should be so used. The suggestion that the conventional approach is out of date should certainly be entertained but in the last 70 years the development of air photos, of radio telemetry, of satellite imagery, of electrophoresis, of simplified chemical analyses, of automated weather stations, and the new possibilities of genetic analysis have been most valuable to solving ecological questions for many of our larger species. But in every case, at every step we should be more careful to ask exactly what questions the new technology can answer. Piling up terabytes of data is not science and could in fact hinder science. We do not wish to validate the Rutherford prediction that our ecological science is “stamp collecting”.

6 thoughts on “Two Visions of Ecological Research

  1. Nick Loman

    An interesting and provocative post, but I would take issue with your use of terminology. You are in fact describing phylogenetic profiling / metabarcoding / marker gene studies rather than metagenomics. Metagenomics refers to sequencing all of the DNA in a sample and is therefore is able to detect the possible range of biochemical functions expected within a microbiome. In some cases it is possible to tie particular functions back to specific genomes.

    Regarding the point about unnamed OTUs, this is commonplace in analysis, but it reflects a kind of useful simplification to treat organisms >97% identical as specific genomopecies and helps deal with sequencing errors. But both metagenomics and phylogenetic profiling is able to a greater or lesser extent integrate with the existing taxonomic databases, particularly for well characterised parts of the tree of life.

    1. Charles Krebs Post author

      Thank you Nick. I am far from an expert on this area, and I appreciate your corrections to my terminology. I look forward to see how this field moves forward. We have had enough problems trying to sort out the ecology of large organisms we can see and name more easily, so I appreciate the ecological problems of working at a scale so tiny.

  2. Stuart Jones

    Nick’s clarifications are useful, but challenging in practice. His last statement in the 1st paragraph where particular functions are tied to specific genomes is not common. This is where the “conventional approach” is most valuable. Identifying ecological tradeoffs and traits under strong selection is very difficult to impossible in the gimish of metagenomic data. I do however see a strong potential in identifying genomic markers of ecological traits using comparative genomic approaches and then applying those models to complex, speciose, messy environments. As is always the case a hybrid approach might be most effective!

  3. Noah Fierer

    Just an opinion of one microbial ecologist:

    First, we use DNA sequencing approaches not because we are particularly enamored with DNA sequencing, but rather because DNA sequencing provides a useful tool for exploring the vast amount of microbial diversity that cannot be characterized using more conventional means (e.g. direct microscopy or culturing).

    Second, we often use DNA sequencing precisely because we are trying to figure out the natural history and ecological attributes of undescribed taxa. One way to understand the ecology of a microorganism is to figure out its biogeographical distribution (e.g. where it lives, which taxa it co-occurs with, and what environmental conditions influences its abundance). DNA sequencing allows us to gain this insight. Microbial ecologists don’t have the luxury of being able to see our organisms in their native habitats. If you had a plant species that you couldn’t see and had no information on its traits or life history attributes, wouldn’t you start by trying to figure out where that plant likes to live, what other plant species it lives with, and what environmental conditions it seems to prefer? That is what microbial ecologists are often trying to do (and I recognize that this effort may sometimes seem Sisyphaean).

    Third, as in all areas of ecology, data collection without specific questions and/or hypotheses is not good science. Yes, there are examples of people doing ‘metagenomics’ just because they happen to have a shiny new DNA sequencer sitting in their laboratory, but no one would argue that simply generating data is equivalent to conducting good science and the majority of studies using such tools are driven by solid questions and hypotheses. Yes – many of the questions asked by microbial ecologists are akin to questions asked by plant and animal ecologists in the 19th century, but they are still solid questions that are advancing our understanding of that overwhelming portion of taxonomic, phylogenetic, and metabolic diversity found on Earth – diversity that has long been ignored by the myopic focus of many ecologists on plants and animals.

  4. Paul Carini

    Budding Microbial physiologist/”ecologist” here.

    +1 to everything Noah said.

    I would like to add that sequencing gives us a powerful tool to peer inside microbial metabolism in a way that was previously impossible. We can now “see” the genes that confer the phenotypes to uncultivated microbes (admittedly though, we don’t know what many of them do).

    To me, this is a relatively unexplored avenue pertinent to microbial ecology thus far: What does the sequence data mean at an organismal level? Can we use this information to cultivate new species? Once cultivated, can we identify important phenotypic traits that can be linked to their ecology? Some of these hypotheses could even be tested using “classical” approaches in the field.

    Metagenomics gives us the opportunity to further contextualize such lab-based findings by identifying the distribution of these important/relevant genes in many locations/datasets as Noah pointed out. In the marine field, the labs of Chisholm, Giovannoni, Moran, etc., etc. have really pioneered combined approaches.

    That said, I think we are all still learning, how to best use this information to gain insight into how microbes interact with each other and their environment. Perhaps its not ‘two approaches,’ but two parts to a single approach and they depend on one other.

  5. Martin Brummell

    I’m extremely happy to be able to post in a comment thread under Dr. Fierer, because several of his papers have been instrumental in structuring the questions I’ve been asking in the course of my PhD, which *right now* I *really should* be working on. But this seems highly relevant and I can’t write my LIterature Review for 8 uninterrupted hours (but please don’t tell my committee that).

    As has been mentioned, many microbial ecological sequence-based approaches start with a functional gene. In my case, I’ve used DNA-microarrays to examine the community composition of ammonia-oxidizing bacteria and archaea in soil samples. I do not know the identity of the species that correspond to the fragments of Ammonia-oxidase subunit A (AmoA) I have amplified, reverse-transcribed, and hybridized onto the probes on my microarrays, but the pattern of abundances and presence / absence, combined with the measurements I made in the field of gas production (in this case, N2O) and soil parameters such as available ammonia, nitrate, water, organic matter, and porosity allows posing ecological questions such as “How important are ammonia-oxidizing archaea to the net emissions of greenhouse gases from this landscape?” and “Why do archaea appear to dominate in some environments, while bacteria dominate in others, within a given functional group such as ammonia-oxidizers?”

    There is a paper from 2005 anyone interested in these ideas might appreciate:
    Oremland, R.S., D.G. Capone, J.F. Stolz, and J. Fuhrman, Whither or wither geomicrobiology in the era of ‘community metagenomics’. Nature Reviews Microbiology, 2005. 3: p. 572-578.


Leave a Reply

Your email address will not be published. Required fields are marked *