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”.