Dear All,

Recent notes on the new journal Design Science, and issue announcements for existing journals point to an issue from a recent thread that deserves further comment. I’d been thinking of this when Terry Love posted a valuable suggestion in reply to the thread titled: “Re: Request - resources on double column setting of books.” Terry pointed to the need for significant and useful research that doesn’t seem to exist. It may exist, but no one has pointed to it. The information Terry seeks is an example of valuable research that might improve design practice. It would not be groundbreaking work, and it wouldn’t necessarily shape a new paradigm or new ways of seeing and conceiving design — and it would nevertheless fill in some significant and useful gaps in the knowledge of the field.

That set me to thinking once again about the issue of new insights and the question of how rare it is that journal articles present major new insights.   

In the thread titled “Re: What is evidence in design and design research?” Don Norman posted a comment on the fact that papers with major new insights in design are rare, as they are in most fields. Don wrote, “As someone who has worked in and read papers in numerous fields, including electrical engineering, computer science, economics, psychology, cognitive science and yes, even design, ​let me add that in every field, most of the huge mass of published papers add little insights. I have asked my colleagues in other fields (e.g., physics, literature, music). They all agree.”

But he goes on to add that most papers remain useful even though they may not offer major new insights: “The mass of papers are useful, I might add. They fill in the details, add new examples or refute old studies. But, on the whole, they are small, and when a new paradigm emerges, they disappear from memory, even if the total sum of those small efforts is what triggered the new paradigm. […] Amazing, but new insights are rare indeed. It is the rare paper that rises above the herd and surveys the entire landscape, understands where it is going, and moves the entire discipline forward (or occasionally in an entirely new direction). Rare in design? Yes, but rare in every discipline.”

Don’s comment is reasonable and important. Few papers in any field add genuine insight to what we currently know. That is the struggle of any field, especially the struggle for any robust field.

It took decades of patient work for Johannes Kepler to develop his laws of planetary motion at a time when prior observations could be used to justify either the Ptolemaic, Tychonian, or Copernican versions of the solar system. By the 20th century, there were so many advances in physics taking place at such speed that one Nobel laureate called it an era in which even second-rate physicists could do first-rate work. Today, physicists are back to patient, painstaking work as they seek new insights. 

Design is not like physics. There are few fundamental laws, and much of what we do involves patient observations and careful descriptions. We have too few of these, and too little substantive empirical work. There is a great deal of applicable science, both natural science and social science, and too little being done to link what is known about the physical world or the human world to what we do in design. The notion that some act of genius will lead to genuine insight without a foundation in patient work resembles the idea that astrologers were producing genuine insight into the universe while Tycho Brahe and Johannes Kepler were struggling away to create serious information. (Full disclosure: Kepler sometimes used his observation to cast horoscopes, even though he thought astrology could not yield valid predictions.) 

The point of Don’s post is that most science is normal science. Great paradigm shifts and new insights are rare. Most research is normal, and most of what most of us do most of the time is to fill in tiny gaps in the foundations and structure of any field. Even the distinguished and insightful in any field spend most of their time on modest, solid achievements. Part of this involves the preparation that anyone who ever has an insight requires to find those few rare moments — as Louis Pasteur notably said, “Chance favours the prepared mind.” All that ordinary work is the preparation.

It is easy to claim an insight. It is difficult to show that the insight describes a world of events as they are or demonstrates a process or way of working that others can use. The purpose of many articles is to check claims, to test insights, and to find out patiently how the world works. 

Those thousands of minor and slightly tedious articles do have a use. "The mass of papers are useful,” Don adds, “They fill in the details, add new examples or refute old studies. But, on the whole, they are small, and when a new paradigm emerges, they disappear from memory, even if the total sum of those small efforts is what triggered the new paradigm.”

There is more to insight than simply making a claim or talking about a great new idea. The real challenge is to publish the work so that others can understand it, test it or try it — adopt it, adapt it, or apply it to their own work. What makes research useful is that a good article allows us to make use of the question, the method, or the findings.

Einstein advanced the field of physics by publishing his insights so that others could use them. Along with most physicists, Einstein published some minor papers. He even made a few mistakes. But there is a difference. Einstein built his revolutionary insights on useful prior work.   

Evidence creates useful information. Evidence allows us to debate the issues so that we can decide whether or not there is anything useful to consider. Every field requires evidence and usefulness. Insight emerges on the basis of these foundations. This slow, patient evolution and the mastery of past results is exactly why science makes progress, and this is why and how researchers occasionally manage to achieve the genuine insights that lead to paradigm shift. 

In a useful and informative essay titled “How Can We Be Sure that Albert Einstein Was Not a Crank?”, physicist Jeremy Bernstein (1993: 14-27) shows the use of all those ordinary articles in the development of Einstein’s work. 

Bernstein describes two principles, correspondence and predictiveness. Correspondence is the relationship between any body of work and the work that comes before it. Predictiveness is the quality of any work that allows us to predict what will happen in specific cases. This allows us to make plans. Design is different to physics, but there are relationships in which the concept of predictiveness applies to both fields. 

If we claim that others can use the skills, ideas, or concepts we develop, we are making a predictive claim. We are saying that those who use our ideas, techniques, or processes will achieve better results than if they do not. That is a prediction. If results are not better or at least good compared with the other ideas, techniques, or processes, the prediction is wrong. This is worth considering when anyone claims to offer new insights, better processes, or revolutionary ideas.

When I find myself feeling sad that new insight is so difficult to achieve, I think of how many centuries it takes to move from a Copernicus or a Kepler to an Einstein. Without that work, there are no giants, and it is only through this process of useful accumulation that any generation can stand on the shoulders of giants to see farther.  

Those who wish to read Bernstein’s article for themselves will find it at the top of the “teaching papers” section of my Academia.edu page at URL:

https://swinburne.academia.edu/KenFriedman 

Researchers must put research to work to find accessible insight. Using the work requires information and evidence.     

This, in turn, requires publishing our work for scrutiny and debate in peer reviewed journals. This is a research list, and most of us read peer-reviwed journals. The articles that David and Don are criticising appear in those journals — they may lack deep insight, and they may not be revolutionary, but they are useful. That is the first step.

Ken

Ken Friedman, PhD, DSc (hc), FDRS | Editor-in-Chief | 设计 She Ji. The Journal of Design, Economics, and Innovation | Published by Elsevier in Cooperation with Tongji University Press | Launching in 2015

Chair Professor of Design Innovation Studies | College of Design and Innovation | Tongji University | Shanghai, China ||| University Distinguished Professor | Centre for Design Innovation | Swinburne University of Technology | Melbourne, Australia

—

Reference

Bernstein, Jeremy. 1993. Cranks, Quarks and the Cosmos. New York: Basic Books.

--

Don Norman wrote:

—snip— 

Where I was sitting at that grumpy moment was reflecting on a large pile of published papers that added so little new insights.

I sympathize with David. The worst part is that his complaint ​appears to be universal. It is not restricted to design

​As someone who has worked in and read papers in numerous fields, including electrical engineering, computer science, economics, psychology, cognitive science and yes, even design, ​let me add that in every field, most of the huge mass of published papers add little insights.  I have asked my colleagues in other fields (e.g., physics, literature, music). They all agree.

The mass of papers are useful, I might add. They fill in the details, add new examples or refute old studies. But, on the whole, they are small, and when a new paradigm emerges, they disappear from memory, even if the total sum of those small efforts is what triggered the new paradigm.

Amazing, but new insights are rare indeed. It is the rare paper that rises above the herd and surveys the entire landscape, understands where it is going, and moves the entire discipline forward (or occasionally in an entirely new direction). Rare in design? Yes, but rare in every discipline.

—snip—
 
 


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