Many professionals, old and young, feel that their work has to be perfect in order to be considered worthwhile. While intellectually everyone knows that this is not the case, it becomes common practice to judge oneself against the illusive standard of what one thinks would be perfection. Although, this constant comparison to perfection and lack of self-confidence in work that is good and productive can work against the success of a professional. This article discusses how to accept a lack of perfection and encourages the production of good work.
So, to get down to business. The first thing we should observe is that the younger person, the new professional, carries around in his or her mind this notion of perfection, that work has to be perfect in order for one to make a major contribution. As you will have read before, that’s just simply not the case, nor could it ever be the case. We judge ourselves by the accomplishments of professionals with many years of practice, or against the work of wunderkind geniuses, Mozarts of the different professions. Many of us feel that unless the work is of such caliber as theirs, it is simply not worth pursuing.
Nothing could be further from the truth. The reality is that most of the work that any of us do in our lifetimes is, at best, modest in its quality, temporary in its influence and, ultimately, forgotten. Certainly, we will have inspired moments. But the vast majority of our work product will be average. If you don’t believe that, try doing two simple observational experiments:
Go through the scientific literature of the most highly regarded journals in your field. Look at the papers and rate them as you personally perceive their importance. If you feel that you are biased because of the authors, you should try doing it double blind, so you don’t know the authors.
Furthermore, should you want to escape the era of work which you are examining, turn to look at journals that were published say 20 years ago.
Now do the same thing but for papers in a far less prestigious journal. Do the same exercise for papers of the same type. Again, score these papers on your perception of their importance and, perhaps, on other attributes.
If you are like the rest of us, you’ll be surprised. The truth of the matter is that the papers in the highly reputed journals are about the same in perceived importance as the papers in the less reputable journals.
The reality is that the vast work-product of science is really a collection of information, dotted occasionally with important papers. Furthermore, the importance of these key papers may not be apparent to you, your colleagues, or even to the profession at the time the papers are published. Years may have to go by before the paper is recognized as influential.
If a researcher’s work product is destined to be just ‘modest,’ then what should one strive for?
What should be the goal of your work? If perfection is not attainable, then what?
What an important question. If you can’t have perfection, then what should you do? Answering this question can take a lifetime, but you don’t have a lifetime to practice. Should you only work on first order problems, or should you accept second-order problems, which you can then solve and master? Or should you continue to work on first order problems and be satisfied with what you can do as long as it’s your best work? These are pretty hard questions to answer.
It’s important to realize that first-order problems are always more interesting than second-order ones. So, when you have a chance, work on first-order problems. You may not do as well or be the first, but at the end of your career, you won’t feel that you have wasted precious minutes on what may turn out to be trivial.
Now, for the really tough question. How perfect should your efforts be? After all, you could spend years and years working out the details of one aspect of a first order problem, doing the work so splendidly and perfectly that you essentially ‘nail it.’ Or, you might want to forego perfection and depth in one narrow area and do smaller bits of work in a variety of different aspects of such first-order problems. In that case, you may feel yourself to be a dilettante doing work in an opportunistic, superficial way. And, in a profound sense, you may be right.
There’s probably no right answer to the foregoing question. Some guidance might be taken from S.S. Stevens, who would have recommended working on the first-order problem (for sure), but also working on a variety of aspects. Stevens’ two favorite phrases were:
As a first approximation, Stevens would never say definitively that the value of ‘so and so’ (i.e., the exponent of the power function for sensory magnitude) was ‘X’. Rather, at what seemed at first to be an affectation, Stevens would use the word approximation. However, that was the message. Despite years of experience and research, Stevens was instructing students that he and his colleagues were not measuring the precise value of the parameter, but just estimating it. And the lesson was, of course, deeper. Since Stevens was by then a 60+ year-old Harvard professor, directing Harvard’s Laboratory of Psychophysics, and not an amateur, this ‘affectation’ was teaching us that research tries to determine what’s going on in the world, how the world works. The message was that the research was good but not perfect. It wasn’t worth being more perfect than the estimate. And, nature wouldn’t let that happen anyway. There was always noise, the random variability of behavior, the monkey wrench that nature throws into our best laid plans.
It’s hard enough to know even the first significant digit. In science, there’s always a desire to probe deeper, to make measurements, to be precise. In Stevens’ world, this precision was nonsense. One might measure precisely, but that didn’t mean that one knew the precise value of a natural parameter. Stevens’ work on perceived sensory magnitude (P) to physical intensity (I) generated an equation of the form P = kIn. It was the exponent n that was of interest. According to Stevens, despite all the effort that researchers might make, it would be sufficient to learn whether n was 0.3 or 0.4. More precision than that was fooling oneself.
What strategies of life work should you adopt?
What should you do? Really, very simply, match your efforts to the problem. If you’re young, don’t get it into your head that your work is so important. Like your writing, it’s not. You may wish on a star, on a hundred stars, on the grave of your great grandparents, or on the latest edition of some obscure scientific journal that you want to be great. Just aim for being good.
And, the practical advice here? Think about your problem and think about what’s enough to satisfy the really smart people in your field . Think long and hard about what you’re doing. And then do just enough to prove to yourself and to others that you have established a fact. Establishment means that you convince others that you have discovered some aspect of nature. Don’t belabor your discovery with 20 different ways of proving the validity of what you’ve discovered. Recognize that you’re mortal, that undoubtedly, in the next ten years, people are either going to forget this fact, incorporate your findings into the general pool of knowledge, or dis-prove you. So, when you think about these three outcomes, do enough of the right research and writing to establish what you have found. And, don’t overdo it.
When you can do a simple experiment, don’t do a complicated, multi-factorial experiment with interactions. It just won’t pay out. Of course, when you need interactions as part of your work, then by all means do so, but don’t make the experiment overly complicated.
When you can establish the finding with 100 people, don’t do 1,000 people just to get the extra precision. Precision is just that… how ‘tight’ your measurement is going to be. But, you’re only human. Don’t strive to be perfect. You’re not G-d. And, the universe isn’t going to come apart if you only have the first significant digit.
When you can establish the finding with a simple table and simple statistics, you don’t need togo for the fancy, esoteric analyses. Plotting data often tells a simpler story than regression modeling with all its statistics. In the end, people will judge with their own eyes and their own mind, not with SPSS®, Systat®, or SAS®. For you readers not familiar with these acronyms, they are the names of well-known, off-the-shelf statistical packages that can provide more statistics in 30 seconds than you may ever want to know.
If it can’t be perfect, how much imperfection is allowable?
If it doesn’t pay to do the perfect, then just how much imperfection should you accept? After all, when the work is too filled with errors, too rife with ‘garbage’, and sim-ply too imperfect, it shouldn’t be accepted. But then how do you know when ‘enough is enough?’ You cannot emotionally judge your own work. It’s hard even for the most experienced researchers, the most polished writers, the most profound thinkers, to judge their own creations.
Every science has its own set of rules, norms for what is acceptable and what is not acceptable. Furthermore, ‘not acceptable’ is, itself, a continuum. There is that level just below acceptable where a slight modification of the study in one small direction might make the difference. Then, there is the world of bias-filled research, which is hard to save unless one wants to do major surgery on the research, and, even then, it’s not certain whether one can achieve adequacy. And, finally, there is the world of work that, at least in one’s opinion, is simply garbage, not salvageable, and not even worth thinking about. The hard thing to accept, especially when you are starting out in science, is that these three categories of sub-par work (below acceptable, biased, garbage) are not fixed categories. They vary by the science, by individual scientists, and by cultural norms of the day. That’s why journals have several reviewers. What one person thinks is garbage another may swear is excellent.