The research avenues NOT taken
Do you ever think about all those possible studies that you could have done but which for one reason or another you never did?
Do you ever think about all those possible studies that you could have done but which for one reason or another you never did? What if they would have led to something incredible (or, less gloriously, to a tenure). At least I find myself doing that, and increasingly so after reading about scientists’ life stories: those early days in their careers when there were no hints that something with which they were struggling with would actually become a major discovery or breakthrough. How many valuable ideas go to waste collectively every single day due to lack of resources or time, or because someone in a position to decide fails to acknowledge the insight? On the flipside of the coin, how many studies are conducted just because people do not come up with any better ideas? Age old questions, I know, but as I am enduring (enjoying) the few research-free weeks of the summer holidays (see the pic), I ended up thinking about all the paths not taken from a more personal perspective (and much to my own enjoyment). I suppose similar stories abound.
In my own stumbling in research life there have been a variety of options and opportunities for choosing alternative paths. Sometimes decisions were easy, sometimes forced, but most often they were based on a vague gut feeling (governed more or less by somewhat unfortunate seasoning with academic realism, i.e. what is likely to produce publishable results and perhaps help scoring grants). Here are a few:
Hunt for unicorns that may not exist. One interesting missed possibility was to investigate the viruses of hyperthermophilic bacteria. Viruses of hyperthermophilic archaea have many unique structural architectures, none of which are found from viral parasites of other host organisms (including bacteria). This led me to ponder whether also the representatives of bacterial domain in boiling geothermal habitats (such as Aquifex and Thermotoga) might have some surprises in store. Could it be possible that in these extreme environments the early (and potentially more diverse) virosphere was preserved better than elsewhere? No studies of viruses of Aquifex or Thermotoga were available at that time. Anyway, we had recently co-discovered the first new bacteriophage family in decades (Sphaerolipoviridae) by studying the viruses of moderately thermophilic bacterium Thermus thermophilus, so the reasoning was not completely delusional. Eventually we even bought all the equipment for concentrating viruses from very hot geothermal waters and were heading to Iceland for an expedition. A little bit too late we realized that special permits are required for extracting samples from Iceland given the economic value of thermotolerant enzymes. Although the local researchers were supportive of possible collaboration in the future, my professor very unfortunately passed away and my two co-supervised PhD students (which I was left to supervise alone) were doing their theses on completely different topics. So reality checked us out from the unicorn hunt, at least for now.
The path of lifelong struggle. The origin of life is an interesting puzzle. During my PhD studies, I built a computational model for a primordial community of replicators. It was fascinating to observe the community to evolve as group selection (in this particular system) decided the genetic winners over losers. Patterns emerged and disappeared. Yet, the model was simple and thus restricted by its own predefined limitations. For many times I considered the possibility to develop a more fundamental model, to tinker a system that in essence mimicked nature’s laws in a simplified form. If genetic replication could somehow emerge from the modeled interactions between molecules instead of being pre-programmed into the model, then it would be very intriguing to observe how the molecular evolution starts to shape the whole system. How far could such simulations go? Yet, very early on I realized that it may easily take a lifetime to even develop such a model and still it would be likely to fail. Modeling the folding of a single protein is already next to impossible, so the interactions in this origin of life model would have to be way more rudimentary compared to the actual reality (in which the proteins exists). Would the emerging features also always remain too rudimentary to yield anything worth the effort? Who knows, but I decided to leave such brave endeavors for brighter minds – even though following that path to the very end might have been an interesting life, if nothing else.
Funding decides for you. Could it possible to genetically engineer the natural gut flora of human beings with modified conjugative plasmids instead of trying to introduce foreign probiotic bacteria to already established microbial community? We had been working with plasmids and their dispersal among bacteria for quite some time, so I even applied for an ERC Starting Grant to study “midbiotics” (plasmid-probiotics) and scored high. Close, but no cigar, I thought. I modified the proposal according to review comments and applied for a smaller grant from a domestic funding body: substantially lower scoring. My current funding had just ended, so I decided that it is too uncertain to keep playing with the idea at this time.
Bigger or applicable questions? Mobile genetic elements are to blame for much of the antibiotic resistance. In our everyday research, we are focusing on the details behind the genetic exchange among microbes (with potential applications in mind). Yet, there is the bigger picture: how did the eons of horizontal gene transfer shape the life around us? To what extent does genetic exchange maintain genetic compatibility between different bacteria? Is the emergence of mobile elements inevitable in a system that would consist of only vertically inherited chromosomes? Some mobile elements are clearly beneficial, others heavily costly. In an attempt to make sense to the genetic circus, with Eugene Koonin from NCBI we formulated a classification based on the selfishness and altruism of genetic elements in respect to the host cell. This classification includes viruses as a part of natural continuum from truly altruistic but essentially immobile (chromosome) to completely selfish but exclusively mobile elements (lytic viruses) and provides a sort of answer to the question whether or not viruses are alive. However, to determine the general principles governing ecological and evolutionary dynamics of mobile elements would require much more systematic research. So far I have found very little time to even begin with studies as the chips have fallen over the decision to go after smaller although arguably more “beneficial” questions. (Nevertheless, there is a PhD student position available in our lab to start exploring the more general aspects of genetic exchange, see goo.gl/xbrQZj).
Idea depository. Already almost ten years ago, we came up with an idea with my friend while we were driving all the way from London to St Andrews for a meeting: could there be a website for good experiment ideas? Something that is in between of a full-scale scientific hypothesis (that can be published in various journals) and a small-scale practical solution. Think of something alike the idea of utilizing Cas9 to tinker eukaryotic genomes – it might or might not work, but you cannot know without trying (of course, very few ideas would be this good, but, well, some could be). On the site, you could share your insight needing experimental verification or development that for some reason is not possible to be executed by yourself or your collaborators. Anyone could use your idea, but the site would require a “gentleman agreement” that, in case the idea realizes into a publication, you would be given an opportunity to co-author the study, should you wish to do so. Your idea would not go to waste, yet, you would not need to go through the laborious work of publishing it as a paper on its own. No official strings would be tied in order to retain freedom for all the parties involved. We even sent the proposal as a letter to few journals, but ink was in short supply, I guess. Yeah, it might never work in practice.
Or could it?