status quoi? - part i

tired of lionization

"she's too old for breaking and too young to tame"
-kris kistofferson, from the song sister sinead

the older i get the less i understand reverence of authority or eminence.  when i was a student, i assumed that those who rose to eminence must have some special wisdom - they often acted as if they did, and others seemed to hang on their every word, so i gave them the benefit of the doubt even if i couldn't see it.  now i'm pretty convinced that there's nothing to this.  some eminent people are wise, and some are full of shit.  just like everyone else.

there are so many messages out there reinforcing the idea that high status people have so much wisdom to offer.  every time a conference stops all parallel programming for a famous person's keynote, every special issue with only invited submissions by senior people sharing their wisdom, every collection of intellectual leaders' opinions on random questions at The Edge - they all send this message.   

it's not that eminent people never have useful advice to give, or important experiences we can all learn from.  it's just that we should judge this on a case by case basis, rather than assuming it.  the knee-jerk assumption that eminent people should be listened to, detached from the actual value of what they're saying, is the problem.  if eminent people are just using their eminence to reinforce existing incentives and hierarchies (even if they do so in ways that seem benevolent and generous), rather than challenging them, then maybe we should listen to them less.  those of us who are more senior and regularly find ourselves being given too much deference should find ways to challenge this dynamic. 

i'm shocked at how often i hear grown-up people with tenured jobs and fancy titles say things like "i know he's a terrible choice but how could we have said no to Mr. Bigshot?" in contrast, i've now met dozens of early career researchers who have actually stood up to the Mr. Bigshots of their fields, or to the power structures more generally, and pointed out glaring flaws in the system.  the fact that people in precarious positions are more willing to do this than are the leaders in our field should be a wake-up call.

i'm embarrassed to say that it took me a long time to trust my own judgment and not just assume that eminent people earned their eminence.  which is why i'm so impressed by the early career researchers i meet these days who have the courage to question this.  those who trust their own perception of things, who see the problems with the status quo, and who decide for themselves who deserves their respect.  i have no idea where they got the wisdom and courage to see these things and point them out, but i am in awe.

i wanted to write a series of blog posts featuring a few of the people i've met who are challenging the conventional wisdom and inspiring others.  but instead of telling you what i think of them, i wanted to give them a chance to share their insights in their own words.  i contacted a few early career researchers i've had the chance to get to know who have impressed me, and who are not affiliated with me or my lab (though i am collaborating on group projects with some of them).  there are many more role models than those featured here, and i encourage you to join me in amplifying them and their messages, however you can.

i asked each of these people "what are the blind spots in your field - what issues should we be tackling that we aren't paying enough attention to?"  here are their answers, in three parts, which i will post in three separate blog posts this week.

Part 1: Ivy Onyeador, Hannah Fraser, Anne Scheel, and Felix Cheung

Ivy Onyeador

There are a number of issues we need to be tackling, and for many of them, we’re paying plenty of attention, or at least engaging in lots of discussion. I think what is missing sometimes is a big picture strategy or goal that we could collectively put our efforts toward that would address the multitude of issues we’re facing.

I think we should be figuring out how to create abundance. As academics in the US, we operate in a context marked by scarcity. Some people are tenured and have lots of resources, but too many people feel they have to be hyper focused on trying to secure resources constantly. Operating in this way breeds insecurity and pettiness, narrows our vision, and pulls us away from our values and ultimate purpose. At core, I think a lot of the issues we need to tackle (e.g., inadequate pay for graduate students, adjuncts and even some professors; the unnecessarily steep competition for publications, funding, tenure track jobs, etc.; how unhappy way too many people are; many diversity and inclusion issues) have a common cause, the denominator is too small. Our initial impulse is to figure out how to operate with limited resources, and we do, but to truly address any of these issues, we need more investment. I think working to secure more resources, for instance, organizing and lobbying to increase state support in higher education, is something more academics should consider.

Hannah Fraser

Ecology is a fascinating field inhabited by passionate people who are genuinely doing their best to to understand the world around us and how to preserve it. However, there is a disconnect between the way this research is conducted and how it is described and interpreted. The vast majority of research in ecology is conducted in an exploratory manner, it's very rare that hypotheses are overtly described and when asked what their hypotheses are, ecologists often insist that they have none. However, the resultant articles are written in a way that implies that the research confirms well justified expectations and, despite the preliminary nature of the results of exploratory work, direct replications are virtually unheard of and deliberate conceptual replications are rare. Published research is treated as truth and any contradictions in the literature are attributed to environmental variation rather than the increased false discovery rate that accompanies exploratory research.

Anne Scheel

In psychology we've been used to having our cake and eating it: Discover a phenomenon and confirm your theoretical explanation for it in just one JPSP paper with a total N of less than 200! We've since learned that the cake wasn't really there, that we need larger N and that most manipulations are not as clever as we thought. But I think the full implications of the message haven't sunk in yet: Way more of what we've been taught needs to be burnt to the ground questioned and potentially rebuilt. We learned to slap layers of ill-defined, implausible, internally inconsistent (but quantifiable!) concepts onto each other, moving so far away from the real world that we fail to recognise that cookie-depleting our ego probably doesn't cause our marriages to break and that a 6-month-old infant probably doesn't have a concept of ‘good’ and ‘evil’. We invent EPFSEA* for phenomena we haven't bothered to describe in any reasonable detail, or to even establish that they're real**!

Let's go back to empiricism. Let's look at those phenomena that made us want to do science in the first place. What's going on? Is it real? Can we describe it? Can we identify necessary and sufficient conditions for it to occur? Can we manipulate it? Each of these questions is a step in a research programme that might take a lot of effort and time -- and require tools that often aren't taught in quantitative psych programmes (qualitative methods, concept formation, ...). They'll feel like baby steps that we prefer to ignore or treat as a dull check-box exercise before we can do real science, testing hypotheses. I think that most of our 'real' science is futile in lieu of the baby steps. And I worry that we're not willing to really embrace baby-step science and its consequences for our everyday research -- a system fed on a diet of illusory cake won't switch to bread crumbs easily.

PS Many others have made similar and better points before (and I’m a cake offender myself!). But I think more of us need to pay more attention to the problem.

* Extremely Premature but Fancy-Sounding Explanations with Acronyms

** Go-to example: newborn imitation
 

Felix Cheung

White hat bias; causal inference; and global/real world relevance.

 

1. White hat bias refers to the tendency to misrepresent information in ways that support a righteous goal (in the authors' mind). I think this can be seen in research on income inequality and related fields. In daily speech, income inequality carries a heavy negative connotation of unfairness, and it can seem like the 'right' thing to do to keep saying how bad income inequality is. But we need to keep in mind that the common operationalization of income inequality in research is not a measure of unfairness, but a measure of income differences (Gini). I am willing to say that some income differences can be fair and just (astronauts with years of specialized training should make more than a clerk). Of course, there are also income differences that are driven by economic injustice. The problem is that the common measure (e.g., Gini) is only a measure of income differences but not income unfairness. In short, income inequality in research is not exactly the same as income inequality in daily speech.

 

Prior research has found mixed results on the link between income inequality and well-being. However, it is not hard to read papers on income inequality citing only papers that found negative effects in the introduction. I have heard of anecdotes of researchers saying something along the line of "if I find that income inequality is good, there's no way I am publishing that". If we want to tackle important real world problems based on data, we must let the data speak. This is why pre-registration is so important, especially in areas that can be controversial.

 

2. Causal inference. I think sometimes, when we use observational studies, we can be too comfortable studying 'associations', and not causal relations. There are powerful designs within observational studies that when applied appropriately, can get us closer to causal inference. Methods, such as natural experiment, regression discontinuity design, Mendalian randomization, and convergent cross mapping, all hold promise to improve causal inference. Of course, some of these methods have already been used in psychological studies, but I would love to see more of them.

 

3. Psychology has a strong real world relevance, and this is partly reflected in the media attention that psychological studies can get. Many of our studies already have strong real world applications (e.g., clinical psych). However, I think we can do more. I currently work in a public health department, and I heard multiple stories of how the entire field was mobilized to tackle major health issues, such as tobacco control, vaccination, and epidemic outbreak. These efforts have saved many lives. If we want to elevate the real world relevance of our field, I believe we can do so by mobilizing our field to focus on major global issues that are having heavy impact on people's thoughts and behaviors (e.g., refugee crisis, social unrest around the globe, violations of basic human rights, denial of science [e.g., in the form of anti-vaccination or anti-climate change]). It is not going to be easy to study these topics (e.g., you cannot use college student samples to study them), and it would mean building strong collaborative partnerships with local governments and international institutions. 

 

 

Part 2 is now up here

 

Part 3 is now up here