The microbiome is one of the hottest areas in biology, with outstanding scientists and laboratories contributing new papers on a daily basis.  Classical microbiology has been almost pushed to one side as everyone climbs on board this hottest of topics.  But is all of this research delivering on its initial promise and excitement?  Is there a danger that microbiome research will suffocate under the sheer weight of the many studies being published, compounded by the ever-increasing complexity of those papers?  In this post I wonder whether or not it is time to move the focus away from measuring the microbiome (a task that has no end) and towards developing insights into the roles of individual members and clusters of microbes.  In essence, is it time for microbiome scientists to become microbiologists again?

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One of the worst things you can give a scientist is a better ruler.  The urge to go back to something that has already been measured, and measure it again to a finer resolution is almost impossible to resist.  The rewards are inbuilt – there is almost certainly already a body of literature on the object that is being measured, and no-one can deny the obvious fact that knowing any object in more detail is intrinsically a good thing.  Of course, it also means that the scientists with the better ruler can tend to be somewhat disparaging of any study using the old ruler!

Something like this may be in danger of happening in microbiome research.  Nearly every paper I read and talk I attend seems to present a yet more complicated set of bioinformatic algorithms, deeper and deeper sequencing, with shotgun metagenomics replacing 16S profiling, meta-transcriptomics replacing metagenomics, single cell transcriptomics replacing community based sequencing, biopsies replacing fecal samples, adding in the virome (mea culpa), etc, etc.  Meanwhile, cohorts are growing in size and huge amounts of metadata are being included in the analysis.  I have been to talks by brilliant scientists where practically every slide is a condensation of an entire paper published in a top tier journal, delivered at breakneck speed.  This is exciting, but can tend to numb any sense of personal engagement with, or limit your ability to critical analyse, the avalanche of data.  While improved methods are always welcome and necessary to advance any field, there is a danger that we are creating scientific and economic entry barriers for young scientists, or those wanting to enter the field.  It is hard not to come to the conclusion that if you want to get a grant to study the microbiome, or get your study into a ‘big’ journal, it seems that the size of the study cohort, the sheer weight of the data ingested and digested, and an overwhelming display of bioinformatic power and figures that look like Jackson Pollock paintings will usually trump a well-designed hypothesis-based study.  Studies involving humans (the only animals that can lie to researchers about their diet and behavior, and by far the least controlled test subjects) always garner praise, while meticulously performed studies in mice and rats are often disparaged for not being ‘in humans’.  I am perhaps exaggerating to make a point, but I think many who attend microbiome conferences will recognize at least a grain of truth in this characterization of the direction the microbiome field is taking.

I also find, and many I have spoken to agree, that the field has become complicated to the point where it is difficult to peer review papers.  Very few scientists have the depth and breadth of knowledge required to critically assess all aspects of a paper put together by a multi-disciplinary team of microbiologists, biochemists, endocrinologists, clinicians, mathematicians, bioinformaticians, and on and on.  It is a truly daunting problem, and the standard review by two or three of your peers may simply not be up to the task.

My concern is that a sense of ‘my study is deeper and wider than yours and is therefore better’ is creeping into the field.  Let me say that my admiration for the intellect of the scientists performing these more and more detailed measurements knows no bounds, and many tantalizing and potentially important associations are being uncovered. I will also readily admit that a large part of my resistance to these mega-studies is a fear that the complexity of the field is moving it out of the reach of my less developed brain.  At many conferences I find myself almost disheartened by the quasi-industrial ‘measure everything deeply, and then deeper still’ approach to microbiome science.  Is anyone else disappointed that after so many outstanding studies and so many measurements, we still cannot define a healthy microbiome, or understand the dreaded term ‘dysbiosis’?  I find myself longing for the more traditional microbiology seminars in which a clearly defined hypothesis is outlined, meticulous experiments are conducted to test or disprove it, and old-style reductionist approaches are used (gene knock-out’s and knock-in’s, interventions involving purified and characterised microbes or dietary components and highly defined endpoints).

My hope is that we are now reaching the stage where the most interesting strands of ‘microbiome’ research will revert to being ‘microbiology’ research, and that we can find room for those who put the rulers aside for a while and use the tools that have been developed as exactly that – tools to test and challenge hypotheses and help us to realize the enormous potential of the microbiome to deliver solutions for society.