Personal models of value in science - high level and pragmatic
Insofar as I have experienced the world (hardly, like everyone else), my most recurring visions of my career have involved scientific research. I was driven here by excitement and curiosity in a vague form, as well as by some competitiveness and the appeal of academic life. As time treads on, I find myself more inclined to direct my life and research choices by an internal system of value. Choices must be made after all. There may be no one correct choice, that’s clear, but there are poor choices. The purpose of a value system is to help make those choices.
The presence of a choice can remain hidden at times, especially to an early career researcher. Typically we are handed specific projects to work on, led to collaborate with X and Y, or are completely caught up with the day to day deliberations of research, and there is often little feeling of steering our own ship. I have a suspicion that this can hold us back, because if we are not careful we may not develop the skill of guiding our own research agenda before it is rather late in the day. Sometimes I find myself in need of a new research project, and in this moment it becomes blatantly clear how much choice there is and how important a part of the process these choices are. I view it as my duty to myself to ensure these choices are not made by inertia, and that I am constantly and consciously working to improve my ability to guide my research at a high level.
External factors will always play a role in how we perceive our work - our reputation, the lauding of colleagues, prizes and so on. It seems hard to abstain from desiring these temptations altogether. However, given the inevitably enormous role luck plays in most of these outcomes, I think our choice of research path cannot be motivated thus, at least in the early years.
Hence, the internal system of value.
What does an internal system of value look like? Well, that’s up to you. Personally, I want a really effective internal model of value which maximises my satisfaction and sense of purpose. It is only natural that I look to others whom I admire, and try to absorb parts of their value models. This act of proactively trying to absorb other mental models of research - both mechanical and high level - is something I am consciously dedicating more time to, and motivated this piece of writing.
A few pieces of my current model of value, which I absorbed from here or there:
- Excitement and curiosity - can I clearly explain to myself and others why the topic is really cool?
- Level of mystery - am I actually working to explain something which is poorly understood, or just fine tuning the details of a research program that is mostly resolved?
- Potential relative benefit of my contribution - is the topic likely to benefit from my particular contribution? how many people are working on the topic and for how many years, and how much progress have they made - can I find a new angle?
These examples are all high level, and I will refer to this as the high level model of value. There is a more tangible, and specific, sense of importance - a personal distinction between preferred research directions and less valued ones - which seems to develop with experience and exposure. This seems to be very important for actually make important pragmatic research choices using an internal model of value. Without it, I can philosophise and try to weigh different options according to the criteria above, but no concrete answer is likely to pop out. At some point it seems likely we need to defer to some more pragmatic machinery which isn’t afraid to speak to the options directly. Let’s call this the pragmatic model for value.
A pragmatic model for value is akin to a taste in wine, or film, or cheese, or people. It is a system for making distinctions, constructing priority, and delivering judgement. While people will go to great measures to defend their taste, there is no right or wrong, no one true taste. We might act as though there is, but there isn’t. I believe we do so, leaving aside social pressure and elitism, because a taste, like a pragmatic model for value, helps us make decisions more effectively. However arbitrary it may be, it introduces invaluable constraints that allow our collective set of choices and proceedings to develop coherence and recognisable structure. It is something like the effect that bounds on thought might have on the capacity for structured coherent thought and understanding in humans - to quote Chomsky, “Far from bewailing the existence of mysteries-for-humans, we should be extremely grateful for it. With no limit to abduction, our cognitive capacities would also have no scope… Without rules, there can be no genuinely creative activity, even when creative work challenges and revises prevailing rules.”
I don’t know how much you can do to directly influence how your pragmatic model of value grows. Given the innumerable amount of effectively arbitrary distinctions that must be made, it seems unlikely that we can do this all by the power of reason and higher judgement.
Rather, I think a proactive pursuit of a clear internal high level model for value might offer a kind of splint for the development of the pragmatic model. The pragmatic model will take many twists and turns, and I want it to, but I also want it to develop in a way that maximises by satisfaction and my sense of purpose. I want the high level model to be the skeleton, with the pragmatic model forming the rest of the body, and which must interact with the outside world.
Beyond constraining my pragmatic model by a high level model, a concern I have is the possibility of a total failure to generate any pragmatic model in any form - through lack of effort, or forgetfulness and becoming too engrossed in the day-to-day grind of research. I don’t know if this is even possible. I imagine many people have a tendency to go too far in the other direction, and develop a taste which constrains too much rather than too little. Whether or not it is a real problem, I see no harm in spending time actively trying to develop the pragmatic model.
I will list a few ideas for how to do develop a pragmatic model for value. I aim to be as concrete as possible and give specific examples.
Absorption. The purpose of having an advisor is largely to absorb their scientific knowhow. Generally this doesn’t mean technical bits and pieces, calculation methods, and so on, but rather the fundamental skills of research, including their sense of taste in problems, methods, and their model for decision making. Importantly, the same goal can be held with other colleagues and admired scientists. Once I decided to consciously think about it this way, I was much more proactive in spotting ways in which other models were different to my own, or where mine was completely lacking - I think I have learned a lot more from my interactions with others after taking this stance. One example of how I implement this is I now try to reflect after a meeting - understand the takeaways, what I learned, summarise new ideas we had and how they arose, and so on - writing all of this in my research log. I am forced to wrestle with the ideas and understand the decisions that were made, extracting some part of the other parties model each time. This extends far beyond the pragmatic model for value.
Exploration - reading widely, working on a range of topics. Naturally, having a pragmatic sense of what you value in science is helped by having a meaningful exposure to a variety of topics, methods, experiments, and people. It’s unclear to me if somebody is more likely to succeed in a research career by relentlessly exploring new topics, hoping to find a niche which scores highly in terms of value and their impact, or by specialising early in one technique, and praying that it is valued sufficiently highly at the right time. Regardless, I am drawn to the first approach through sheer love of agency.
Targeted training. If you want to run, you should probably run. If you want to swim, you need to go in the water. Additional strength and conditioning training is important but at the end of the day you will bottle the main event without targeted on-the-ground practice. I think the same can be said of pragmatic research decision making. Time is finite and research doesn’t always progress quickly, so opportunities to test out our pragmatic models for making high level pivotal decisions might seem few and far between (as a PhD student). Yet, we can always spend time each week brainstorming new research ideas, practicing idea generation, and then prioritise them. It is also a lot of fun to sit down and think about what you would work on if you suddenly had infinite resources and indefinite guaranteed job security.