How to (not) write a microbiome grant, Part I

I'm involved in something that I shouldn't talk much about, but suffice it to say I'm smack dab in the middle of evaluating multiple different microbiome grants. As such I'm the exact target audience you should be aiming to reach with your microbiome grant, literally, the exact target audience. There are a few grantsmanship things at the forefront of my reviewing mind right now that I'd like to get down in written form with the hopes of helping people out in the future (myself included). I'm especially wary going forward because there is currently a push to make microbiome studies the next BRAINI and we as a community are going to do ourselves a huge disservice if we get this wrong. The last thing I want to see is a huge movement for government funding within an area I care deeply about, only to have it not really come close to living up to the hype. I'll definitely have more to say on this as I digest some more, but here are a few things to keep you going:

1. Think about your hypothesis when designing experiments and keep this hypothesis in the forefront of your thoughts. 

Microbiome constituency is going to change over time at some level, it's going to change in some way with pretty much every manipulation you can think of. It is soooooo tempting to write experiments that focus on measuring this change over time, measuring how individuals differ, or that measure the variation associated with treatment X. Maybe one community changes at different rates than others? Maybe there is something magical and emergent that happens when you put all of this community information together?

When you are writing your grant, you are going to be couching the effect of the microbiome in terms of something. The microbiome is important for human/plant health, the microbiome affects geochemical cycling, the microbiome affects evolution of species, etc.....The problem I'm repeatedly seeing with grants is that the whole project is built with the idea that the microbiome will have an effect on X, and measuring how treatment Y affects the microbiome is important for understanding X, but to me at least it seems a lot of people forget to directly link treatment Y with its effect on X. If the treating the phyllosphere microbiome with jasmonic acid is going to change its constituency or dynamics, and jasmonic acid is therefore predicted to affect "plant health", please try to include measurements of "plant health" within your treatments. Keep the whole hypothesis in mind and don't just measure how treatment Y will change the microbiome and then assume that this change is going to impact X. Directly measure the impact of Y on X in the context of the microbiome.

2. It is very tempting to want to use the latest technology to measure "system level" effects of the microbiome. Proceed at your own risk, and with enough preliminary data to make me believe that you can adequately carry out the experiments. 

A couple of years ago, on a completely different panel, every grant seemingly included RNAseq. Now every grant is including metabolomics and metatranscriptomics. These technologies are awesomely powerful, and they will truly revolutionize some areas of science. If you are writing a grant, however, don't just say you will evaluate the microbiome with "metatranscriptomics". I want to see data for how many reads you might expect in a given environment (pilot experiments work wonders). I want to know that you are proposing to sequence enough depth to actually have a reasonable chance at seeing differences. Every system is different, and just citing papers that it's possible doesn't do the trick. This is especially challenging when studying microbiome communities within a host. Much of the metatranscriptomics work right now is being done in environmental communities, and a lot of the papers/technologies are being developed with these kinds of studies in mind. Any time you include a eukaryotic host in microbiome studies, you are going to get A LOT of eukaryotic RNA in your metatranscriptomes. Sure, pulling down with PolyA might clean up some, but for a lot of plant systems the chloroplast RNA isn't polyadenylated and is present at high frequencies. For 16s based studies you can design PNA blockers to limit the amount of eukaryotic contamination that comes through, but this doesn't work at a metatranscriptomic level yet. Sure, you can just throw everything onto a few HiSeq lanes and only use bacterial RNA reads, but as a reviewer I want to see enough information to convince me that using the "sequence everything and cull what you don't want approach" or maybe "the overkill-ome" is going to work. Tell me the fraction of reads that are host vs. microbiome, even if you only have this information from a small scale pilot study.

3. I don't ever want to see this in your grant:

Figure 1. Bad Hairball Plot. 
mage from: http://www.wired.com/wp-content/uploads/images_blogs/wiredscience/2013/11/bad_hairball.jpg

That is a plot of some random network I found with a Google search. Microbiome studies tend to sample many different taxa under different situations over time. It's tempting to put all of this interaction data together in a plot such as the one above, so that in your grant you can demonstrate that you do "systems biology". THERE IS NOTHING USEFUL VISUALLY IN THESE KIND OF PLOTS. In many cases, the nodes aren't even labelled. The only thing I can assume that this plot is trying to show is that you can do "systems biology". Grant space is so precious and limited, why waste it on a figure that doesn't relay any information at all?

If you do find interesting interactions, feel free to make a small figure including just a few nodes (labelled of course) that shows these interactions and explains what this interaction visually means. A hairball plot like the one above serves absolutely no purpose for the reviewer of a grant, and actually annoys me. Don't annoy the reviewer.

End of rant for now:)

Realized and Fundamental Niches in Academia

Two things I read last week motivated me to sit down and post some thoughts. Last night I found some time to read Jesse Shapiro's new preprint (because, for once, my kiddo went to sleep early and I still had some energy at the end of the day), which focused on using metagenomic data to tease apart how recombination and selective sweeps affect genetic diversity within bacterial populations over time. It provides quite a good summary of recent research into this topic and I found myself binge reading a bunch of newer papers late on a Sunday night. It's surely not for everyone, but I am and have always been fascinated by this research topic. When I finished grad school, this was kind of what I thought I'd be researching over the course of my career.

I'm a few months from submitting my tenure packet, and have been working for the better part of the last 5 years to sculpt that document. Over that time I've been lucky to have really good people working in my lab, and we've been lucky enough to be decently successful in terms of funding and manuscripts. However, even though all of the work we're doing is interesting and exciting, it has ostensibly nothing to do with recombination in bacterial populations despite my intrinsic interests. I wouldn't say that I'm sad about this, but I definitely have feelings that border on regret.

Couple these thoughts with a great blog post I read earlier in the week from Proflikesubstance describing "Tenure Funk". Since I don't have tenure, it's a bit premature for me to say anything about the feelings after accomplishing that goal, however I think I'm on a trajectory towards something that resembles a funk. As a PI you work so hard to find ways to carry out experiments, pay for research, and take care of your people. You have to do what you can to make sure that the lab survives. When I started my lab, a friend (also a PI) described having to "sell out" in order to find ways to fund research. There are no doubt lucky people out there that can do exactly the research they want and find ways to pay for it, but I think there are a lot of us out there that find that our "lanes" diverge from where we thought they'd go. You have to do what you can to survive, and this often means downshifting your energy away from experiments you love to pursue the fundable. Aside from $, there are also institutional pressures that direct your research. I'm in a Plant Science department in a School of Agriculture. I feel compelled to work on systems and questions that my whole department and school can easily relate to. Sure, there are bits and pieces of research that would allow me to investigate recombination in bacterial populations in agricultural settings, but I find these projects more difficult to sell across the campus/school than applied projects.

In ecology, researchers talk about fundamental and realized niches. A fundamental niche is the total space/role that an organism can theoretically fill in nature if not affected by outside forces. The realized niche is the space that an organism actually fills in nature. As we progress through our careers, we all find out what our realized academic niche is (this may be what type of college you work at, what type of research you do, what industry you work in, etc...). This often differs from our fundamental academic niche because outside forces affect the direction of our lives. At certain points in our careers (like tenure time) there are benchmarks that force us to sit down and evaluate how we're doing. It's at these benchmark times that the divergence between our realized and fundamental academic niches becomes apparent. I can see pretty clearly now how these realizations could lead to "tenure funk" or related funks across careers. Can't say that I know how to fix it, although the idea of taking sabbaticals to think and develop projects is definitely appealing. I also have a feeling that realization of divergence between what I'm doing and what I'd do given unlimited funds is actually quite good in the end.

It just hit me that, in my 5th year review meeting, my department head made exactly this point. Tenure is a great time to evaluate the course of your career and what you'd change. Now that I've established a couple of interesting (and fundable so far, fingers crossed) systems, I can begin to tweak these to ask questions that align better with my intrinsic interest in bacterial evolution. When you start your lab everything goes so fast and time management is so difficult that you have to focus on only the most important things.  Now that I'm a few years in, I have a better sense of how to carry out smaller exploratory projects given time constraints. Being a PI is the greatest job in the world (IMO, for me) even though it's stressful as hell and bathes you in bad news most of the time. Truth is that it takes a few years to figure out how to navigate the system where the research you truly want to do may not be fundable. The research is still quite possible, it just takes some time and perspective to see how to get the paths to converge again.