Looking up

Let’s talk today about how I have been approaching finding a first research subject in ecology after my initial conversations. When it comes to entering a research field, it works a bit differently when you start as an already experienced researcher, compared to a new undergrad or PhD student. Your new colleagues just are not going to serve you a subject on a plate, treat you like a newbie, and train you from scratch. That is not what I expected from my colleagues anyways, and certainly not how I would myself deal with colleagues my age eager to get into astrophysics (how I would approach this is in itself an interesting question!). Instead, it was immediately clear between us that I would come up with my own ideas and baggage, and try to create bridges with them and their expertise. In other words, you shouldn’t expect that somebody will take care of you when you start such a transition. It is up to you to create your niche and to make yourself valuable to your new colleagues and to the field.

There are three key considerations in my thought process to approach this. The first one is to make sure I would enjoy doing what I decided to go for; the second one to identify a subject/problem I thought would be feasible, using my existing skills (even better, for which my skills would bring something new to the field), so I could get somewhere relatively fluently and in finite time; the third to make sure what I was going to start doing on the short term could serve as a springboard to diversify my activities towards more applied ecological research on the longer term.

Enjoying one’s time

The first point is also the most obvious one: to never forget that good research is almost always research one enjoys doing in the first place. I am not painfully slowly getting out of a theoretical astrophysics rut to get into another one immediately. So, everytime I read about an ecological research problem that I start to mildly understand, for which I start to have ideas and think I could get something going, the first question I try to always remind myself to ask is: “would working on this bring joy and excitement ?” If not, if it looks too convoluted, too far fetched, or just does not resonate enough, I pass. It looks simple written like that, but in reality, we researchers often have to fight against our own tendencies to think that just because something seems doable, we should do it (especially in the short-term project funding era). Well, no. For me, working on something is only worthwhile if I first truly enjoy working on it, and feasibility/importance comes second. I guess that also explains many of my failures to secure funding in the past, but I have always favoured living with convictions and practicing self-criticism, rather than jumping on bandwagons. It’s one of the rare things I am truly proud of looking back at the first part of my career (yes, US and European colleagues, I know many of you have no choice in the system you are working in, and I am an irritating spoiled brat. But don’t worry, French government reforms will also eventually succeed in killing all the ingenuity left in our research, so you won’t be the only ones to feel miserable working in a corseted hamster race environment).

Finding something that will reward efforts

Let’s face it, I am not going to revolutionize ecological research in a matter of three years, and neither is it my objective. As every good PhD supervisor knows, what matters when you conduct a research project is managing your students’ expectations and helping them to get on a realistic path that will deliver some rewards along the way, in the middle of the difficulties that come with the job of being a newbie in an expert field. So I am trying to apply this to myself and to find a simple enough path that uses my own natural and acquired research skills, which unlike a PhD student I am also lucky enough as an experienced researcher to already know roughly what they are.

But I also want to bring something new to the field by transferring stuff from another one, otherwise what is the point ? The best way to do this, I find, is to take stock of what have been successful experiences for me so far and to apply similar recipes. Namely, in my case doing theory with the assistance of big computers, and approaching some known problems by calculating new funky things using methods unknown of in that field. I’ve done this kind of transfer from fluid dynamics to astro several times (e.g. here, where I applied an SO(3) decomposition of turbulent structure functions to thermal convection with anisotropic solar turbulence in mind, something which paid off ~10 years later when I came up with new phenomenological scaling laws for solar surface turbulence that appear to fit the actual data quite well, and there, where we developed some methods at the cutting edge of hydrodynamic pipe flow and boundary layer research to understand magnetic-field generation in accretion disks, something which is also now, quite unexpectedly I must say, starting to pay off in the context of understanding magnetized black hole accretion).

These “transfer” experiences to astrophysics have been some of the most fulfilling, enjoyable and fluent projects I have worked on in my career, so check box one above and are likely to get somewhere in finite time. Fortunately, being able to ask interesting and meaningful theoretical questions to supercomputers also happens to be something that colleagues in ecology appear to be in demand of, so fits the bill of bringing some added value to the field. We’ll see in future posts what exact questions we’ll approach this way, but for the time being identifying a methodology and tools with which I am fluent and appear to be of interest to my new colleagues is already like finding a little rock in the middle of the river to cross it. It’s not yet a large bridge, but it serves the purpose.

Using short-term projects as a springboard

Finally I am in this for the long haul, and I want to make sure what I am getting into now doesn’t fizzle out once the initial excitement is gone. So although I want to find a project that gets somewhere in finite time, I also find it imperative to start thinking long term: where is that first project going to take us, how to best use my time in these first years to create a virtuous loop, what are we going to build that could then be further developed, expanded on, enriched ? In the past, as a scientific butterfly I didn’t always think through my projects in such terms, and occasionally I found myself bored, or wondering what was next only to come up with no answer relatively quickly, after just a handful of years. Call this experience, or maturity, but I think I have learned from this and I woud like to avoid getting into dead-ends too quickly in my new future. So in the context of getting into computational ecology, I am spending a lot of time thinking about what the tools I am going to start developing may lead to in terms of applicability: stability and sensitivity analysis, optimisation, data assimilation, using simulations as virtual experiments / field data all seem to be good threads for the future, and also happen to be right down my alley considering my past experience in astro, including, yes horrified reader, with actual observations.

Gold nuggets and grizzly bears

By now, readers will have understood that I am getting into computational ecology on supercomputing scales (I’ll talk more about the environmental aspects and impacts of this plan in the future), where I hope to import some methods and tools I am familiar with in astro. It is exciting enough to me for the time being because it doesn’t look like so much of this has been happening in the field so far and I know what I can bring, and the potential that comes with that. It honestly looks a bit like a wild west eldorado, hopefully with a lot of gold nuggets and few or no grizzly bears. In astro, there are way too many grizzly bears and way too few gold nuggets left.

I know this is also going to get me somewhere (I think I have surveyed the theoretical ecology landscape sufficiently by now to see the potentialities and open spaces), my new colleagues in Moulis appear to be in demand of, and interested in this kind of approach, and it opens up plenty of complementarities and perspectives for the longer term to build bridges with more applied, and important research topics in ecology.

To bring today’s musing to a conclusion: I am aware that I am spending a lot of time talking meta in this blog for the time being, but if you think about it, we are not talking about a transition between low-qualifications jobs here, but between complex scientific research fields, that is going to have consequences for the rest of my career. It takes an awful lot of time to acquaint oneself with a new field, to build some credentials as a naïve outsider, and to make plans that make sense before starting anything. And, even though I am under no tangible external pressure to succeed for the time being, I really don’t want to fail miserably either, especially considering the psychological rut I am still trying to extract myself from. As always, I feel like I am my most demanding and worst (best ?) own reviewer and evaluator. Taking the time to open up on these matters with you, readers, going from the general to the particular, simply reflects the time it takes me to personally think through this transition carefully. Only time will tell, but I also think this is the right way to proceed, at least for me.