Dear Mitch (and All),

The thread on avant-garde design research has given rise to a great deal of off-list conversation. After my last post, several notes pointed me to books that exemplify the kind of research in William Nordhaus’s article. One example is Craeft by Alexander Langlands (2019). 

Your latest post — copied below — raises a profound question:

How we can increase research of the kind we see in Nordhaus (1998)?

The term "avant-garde" began in the military with the description of the advance guard of an army, breaking new territory and taking the lead in conquest. The Oxford English Dictionary (2020) defines avant-garde as "1. The foremost part of an army the vanguard or van. 2. The pioneers or innovators in any art in a particular period. Also attributive or as adj.” While the military usage has become less common over the years, the concept of leadership and breakthrough remains. Where the avant-garde leads, the rest follow. The original usage dates in English to the late 1400s. While the usage shifted to the arts and humanities, the concepts of leadership, direction, and progress remain central. The current usage dates to the 1800s.

Merriam-Webster’s (2020) defines the avant-garde in its current usage as “an intelligentsia that develops new or experimental concepts especially in the arts.” It gives several synonyms: advanced, avant, cutting-edge, progressive, and state-of-the-art.

The concept of the avant-garde is that of genuine conceptual development. Simply proposing a new idea is not enough. A real avant-garde influences its field with a genuine contribution. We may debate the nature of genuine contributions in any field — in the arts, ambiguity and critical reception make it far more difficult to determine the nature of an important contribution than may be the case in the sciences. Even in the sciences, however, many research findings lead to extensive debate. The hope is that the result of this debate leads to deeper understanding in the field and better answers to the research questions we ask. 

This is the hallmark of William Nordhaus’s work. Nordhaus often has bold ideas — and he developed the technical skill to bring his bold ideas to fruition. The article on lighting is only one example. In 2002, for example, Nordhaus once again returned to what he described as “Mesopotamian economics” to estimate the cost of a war in Iraq before the war began. Nordhaus (2002) estimated that such a war would cost up to 1.9 trillion dollars. While this exceeded projections and estimates from the Bush administration, it was remarkably accurate — and close to the 2007 estimates of the Congressional Budget Office (Reuters Staff 2007)  

Nordhaus returned to the topic of lighting a few years later with another groundbreaking article, “Using luminosity data as a proxy for economic statistics.” (Xi and Nordhaus 2011: 8589–8594). Together with Xi Chen, he also developed the massive G-Econ research project, “devoted to developing a geophysically based data set on economic activity for the world.”

Nordhaus’s capacity to generate avant-garde research rests on the technical mastery and advanced research skills that permit him to carry out his bold ideas. Nordhaus starts with sometimes astonishing hypotheses. He ends with evidence and a sound argument to demonstrate that the hypotheses are valid, correct, or useful. Or — as scientists often learn — he discovers that they may not be  valid, correct, or useful. In either case, the research contributes to the field.

Another great example of avant-garde research was Albert Einstein’s (1998 [1905]) paper on Brownian motion. You can see it in John Stachel’s great collection of Einstein’s five papers in Einstein’s Miraculous Year. (For a short summary, see: APS News 2020)

In 1905, the idea of atomic theory was still an open question in the discipline of physics. When Einstein wrote his paper on Brownian motion, many physicists did not believe in the physical reality of atomic theory. Some conceded that the idea of the atom made heuristic sense because it made physical calculations easier — but they felt nevertheless that the notion of the atom was itself incorrect or unproven. 

To examine the question of atomic theory as a physical fact, Einstein went back to the observation of Brownian motion. Robert Brown was the Scottish botanist who had described the phenomenon of small random fluctuations in liquid media in 1827. Einstein began with this, arguing from carefully observed empirical data. He used well known facts. Some were so well established that he didn’t even need citations: these were well established facts on which all physicists and chemists agreed. From facts that everyone had seen and to which everyone assented, Einstein argued that one must conclude that atoms are a physical reality. What made this paper an example of avant-garde research is Einstein’s ability to use facts that everyone had seen and on which everyone agreed to settle a heated controversy at the heart of his discipline.  

When editor Max Planck — who would himself win the Nobel Prize — published this paper in the journal Annalen der Physik, many physicists disagreed. Within a few years after the paper appeared, the entire field of physics had accepted atomic theory as a physical reality.

Physicist Jeremy Bernstein (1993:15) wrote an interesting article that effectively asks how to distinguish avant-garde research from nonsense. 

“The year is 1905. I am a professor of physics at the University of Bern. For many years I have been teaching probably from the same set of notes respectable courses based on what is for me the familiar and comfortable physics of the nineteenth century. I teach the mechanics of Newton the relatively modern theories of electricity and magnetism of James Clerk Maxwell along with good solid nineteenth-century thermodynamics. I believe that atoms exist although I am troubled occasionally by the question that around the turn of the century Ernst Mach asked Ludwig Boltzmann: ‘Have you seen one?’ All in all it is a good comfortable life. Then with no warning at all a series of physics papers begins arriving in the mail. They carry the return address of the Swiss National Patent Office in Bern. The covering letter identifies their author as a patent examiner -- a technical expert ‘third class’ — of whom I have never heard. He does not even have a doctoral title. Upon browsing through the papers I discover that this doctorless unknown is claiming — using totally unfamiliar kinds of reasoning — that essentially all of the physics I have been teaching is wrong. Not just wrong in a few minor details but fundamentally wrong. What would my reaction be? What should it have been? In short how could I then have known that the author of these papers — the twenty-six-year-old Albert Einstein was not a crank?”

Bernstein answers the question through the course of the article. Toward the end, he notes “All of us who have tried to work in a deep science know just how hard it is to get to the frontier — just how much devoted training is involved. Even Einstein went through this apprenticeship. The notes he took in H. F. Weber's l887-88 lectures at the Swiss Federal Polytechnic School in Zurich still exist. They are the notes of a conscientious student with a clear understanding of the physics that preceded his own.” (Bernstein 1993: 27) 

While Bernstein doesn’t use the term “avant-garde research,” he does speak of the research frontier. He proposes several criteria that distinguish crank research from the genuine avant-garde. Interesting, Bernstein first discusses the avant-garde in art, literature, and music, giving three well known examples, Nude Descending a Staircase by Marcel Duchamp, Finnegans Wake by James Joyce, and 4’33” by John Cage. For avant-garde research, Bernstein (1993:17-23) offers two central criteria, correspondence and predictiveness. 

Correspondence, for Bernstein (1993:18) states “that any proposal for a radically new theory in physics or in any other science contain a clear explanation of why the precedent science worked. What new domain of experience is being explored by the new science and how does it meld with the old?” He describes this as “an important benchmark for distinguishing real science from its imitations.” 

The “second criterion that genuine science should satisfy is predictiveness. Real scientific ideas cry out to be tested in laboratories. Einstein’s 1905 papers are ... full of predictions.” (Bernstein 1993:20)

There is no single criterion that applies to every form of serious research. For example, Nordhaus’s 1998 paper on light makes no predictions. It is nevertheless possible to measure his claims against the real world: this measurement takes the place of prediction.

Avant-garde research may not reveal great truths of change the course of science. From time to time, we find charming minor cases of avant-garde research. The New York Times recently reported an intriguing physics paper. Even though the problem is minor, involving the conservation of angular momentum in the spin of a football forward pass, the science was difficult. Physicists worked on the problem for several decades to find the answer. (Chang 2020. See also: Price 2020)

Design is filled with problems that call for solutions. Some are minor. Some involve the daily flow of work. While some design involves creating or inventing things that don’t yet exist, a great deal of design involves redesign — and massive amounts of design work involve applying existing design solutions in different yet predictable circumstances. A case in point is the situation in which working designers execute a corporate design program across signage, stationery, packaging, press releases, and advertisements. Once the corporate design program is established, it may be used across thousands of different items that are reproduced in tens of millions of examples. None of this is avant-garde. 

But design also entails serious problems where avant-garde research might well generate new, useful, and surprising solutions. That’s what Mitch looks for when he writes: “...we should not be afraid to be more accountable to one another or to challenge our future selves. Rather, we should be emboldened.”

What do we need to do if we are to be accountable and to challenge our future selves to engage in genuinely avant-garde research? This kind of work requires technical mastery — the work of a Nordhaus, an Einstein, or the team of Price, Moss and Gay.

In my view, there are four key factors that will make a difference. The first two challenges we face involve training researchers with the capacity for avant-garde research. This requires mastery, and it requires providing people with the kind of education that will engender the understanding that leads to correspondence.   

To achieve this, we must improve the quality of doctoral education and the quality of doctoral supervision.

The second two factors involve the articles that convey our research, and the way we handle articles in our journals. 

To achieve this, we must teach better research writing skills, and we must improve the quality of journal reviewing.

There are many more issues to consider — but until we develop a strong corps of researchers, we will have difficulty with an avant-garde. The original idea of the avant-garde involved an army corps able to send a vanguard force into new territory — perhaps to scout, perhaps to engage the lead elements of the opposing force that constitutes an army’s “problem.” The concept of avant-garde research requires a well trained, competent corps of researchers able to scout, to forage, and to address challenges in a serious way. 

We are developing good young researchers, but nowhere near enough of them. In comparison with fields such as economics or physics, we produce very few PhD graduates. But a second issue comes up. There is more involved than the number of graduates. Very few PhD graduates in economics go on to win a Nobel Prize as Nordhaus did. There have been tens of thousands of PhD graduates in the different fields of economics — even more graduates in the fields of philosophy, mathematics, and the social sciences in which Nobel laureates in economics have studied. Of these, only 86 individuals have won the Nobel Prize. What makes the difference is a field large enough with enough solid PhD programs to provide a corps from which a vanguard can emerge. (Since the late 1800s, there have been several hundred thousand PhD graduates in physics, physical chemistry, biophysics, mathematical physics, mathematics, and related fields. Of these, 215 individuals have won the Nobel Prize in physics.) We simply do not have enough excellent PhD programs in design that ensure that every graduate possesses the basic skills required for competent research. While we have more good PhD graduates than ever before, the explosion of doctoral programs means that they are a tiny fraction of the PhD degrees awarded in different design fields. Without a large corps of competent researchers, we cannot hope for an avant-garde able to generate bold ideas and push them forward to achieve a contribution. We lack what sports coaches call a deep bench.

When we have built the field out enough to generate more avant-garde research based on skill and mastery, then we come to the question of writing it up and getting it published. At this point, I’ve written far more than I originally planned to write, so I’ll save that for another day.

Warm wishes,

Ken

—

References

APS News. 2005. American Physical Society News February 2005, Vol. 14, No. 2. “This Month in Physics History: Einstein and Brownian Motion” URL: https://www.aps.org/publications/apsnews/200502/history.cfm <https://www.aps.org/publications/apsnews/200502/history.cfm>  Accessed 2020 October 18.

Bernstein Jeremy. 1993. “How Can We Be Sure That Albert Einstein Was Not A Crank?” Cranks Quarks and the Cosmos. New York: Basic Books. pp. 15-27. (A copy will be available at this URL through November 1: https://www.academia.edu/44325878/Bernstein_1997_Einstein_Crank <https://www.academia.edu/44325878/Bernstein_1997_Einstein_Crank> )

Chang, Kenneth. 2020. “Why a Perfect Spiral Football Pass Doesn’t Break the Laws of Physics.” New York Times. URL: 
https://www.nytimes.com/2020/10/16/science/football-pass-physics.html <https://www.nytimes.com/2020/10/16/science/football-pass-physics.html>  Accessed 2020 October 19.

Einstein, Albert. 1998. [1905]. “Einstein on Brownian Motion.” Including the reprint text of “On the Motion of Small Particles Suspended in Liquids at Rest Required by the Molecular-Kinetic Theory of Heat.” In Einstein’s Miraculous Year. Five Papers That Changed the Face of Physics. Edited and Introduced by John Stachel. Princeton, New Jersey: Princeton University Press, pp. 73-98.

Langlands, Alexander. 2019. Cræft: An Inquiry Into the Origins and True Meaning of Traditional Crafts. New York: W. W. Norton.

Merriam-Webster’s Online. 2020. “Avant-Garde.” URL: https://www.merriam-webster.com/dictionary/avant-garde <https://www.merriam-webster.com/dictionary/avant-garde> Accessed 2020 October 18.

Nordhaus, William D. 1998. Do Real-Output and Real-Wage Measures Capture Reality? The History of Lighting Suggests Not. Cowles Foundation Paper No. 957. New Haven, Connecticut: Cowles Foundation for Economic Research at Yale University. Originally published in: The Economics of New Goods, edited by Timothy F. Bresnahan and Robert J. Gordon. 1997. National Bureau of Economic Research Studies in Income and Wealth, Vol. 58, Chicago: University of Chicago Press, pp. 29-70. Available at URL: https://www.nber.org/chapters/c6064.pdf <https://www.nber.org/chapters/c6064.pdf>  Date accessed 2020 October 15.

Nordhaus, William D. 2002. The Economic Consequences of a War with Iraq. Working Paper 9361. Cambridge, Massachusetts: National Bureau of Economic Research. URL: http://www.nber.org/papers/w9361 <http://www.nber.org/papers/w9361> Accessed: 2020 October 18.

Nordhaus, William. 2020. The G-Econ Project. URL: https://sites.google.com/site/williamdnordhaus/gecon <https://sites.google.com/site/williamdnordhaus/gecon> Accessed 2020 October 18.

Oxford English Dictionary Online. 2020. “Avant-garde.” URL: https://www.oed.com/view/Entry/13610 <https://www.oed.com/view/Entry/13610> Accessed 2020 October 18.

Price, Richard H., William C. Moss, and T.J. Gay. 2020. “The paradox of the tight spiral pass in American football: Insights from an analytic approximate solution.” American Journal of Physics, Vol. 88, p. 753 (2020) DOI: https://doi.org/10.1119/10.0001632 <https://doi.org/10.1119/10.0001632>

Reuters Staff. 2007. “U.S. CBO estimates $2.4 trillion long-term war costs.” October 24, 2007. URL: https://www.reuters.com/article/us-iraq-usa-funding-idUSN2450753720071024 <https://www.reuters.com/article/us-iraq-usa-funding-idUSN2450753720071024> Accessed 2020 October 18.

Xi, Chen and William D. Nordhaus. 2011. “Using luminosity data as a proxy for economic statistics.” Proceedings of the National Academy of Science, May 24, 2011, Vol. 108, No. 21, pp. 8589–8594 DOI: www.pnas.org/cgi/doi/10.1073/pnas.1017031108 <http://www.pnas.org/cgi/doi/10.1073/pnas.1017031108>

—

Ken Friedman, Ph.D., D.Sc. (hc), FDRS | Editor-in-Chief | 设计 She Ji. The Journal of Design, Economics, and Innovation | Published by Tongji University in Cooperation with Elsevier | URL: http://www.journals.elsevier.com/she-ji-the-journal-of-design-economics-and-innovation/ <http://www.journals.elsevier.com/she-ji-the-journal-of-design-economics-and-innovation/>

Chair Professor of Design Innovation Studies | College of Design and Innovation | Tongji University | Shanghai, China ||| Visiting Professor | Faculty of Engineering | Lund University ||| Email  [log in to unmask] <mailto:[log in to unmask]> | Academia https://tongji.academia.edu/KenFriedman <https://tongji.academia.edu/KenFriedman> | D&I http://tjdi.tongji.edu.cn <http://tjdi.tongji.edu.cn/> 

—

Mitch Sipus wrote:

—snip—

Yes. Yes. Yes. I'm thrilled you see the light (ahem), as Nordhaus's 1998 publication is a sublime example of what we, as designers, could accomplish through our own research. In his own words, "making a complete reckoning of the impact of new and improved consumer goods on our living standards is an epic task."  He is not alone in the pursuit. We are here too.

But are we equipped for the task?

An interesting aspect of Nordhaus's work on light, was that he revitalized perhaps the most ancient and banal economic indicator, the price value of labor. Nordhaus needed a creative solution to correlate and project the impact of product design to society, and the price value of labor - though a roughly hewn measure - enabled him to make projections both backward and forward in time. It is here, through the weaving of creativity, materiality, classical economics and longitudinal thinking that I find the work to be just short of bliss. Yet it also shows that the economists have an advantage here... and we could perhaps borrow a little of their approach in our own scholarship.

While design research can be liberating in its future-forward focus as the 'science of the artificial,' I have long found it difficult to extrapolate the greater implications of most research efforts. The great variance across research products can be refreshing, but the more dissertations I’ve read in the field, the less certain I am to define it. The third leg, as Ken describes of the scientific method, is a rigor in research design made possible partly because assessment criteria are formulated via the initial stages of observation. We have many frameworks, but we do not have shared modular units of assessment criteria equivalent to the price-value of labor. As we design forward - projecting new concepts into the world through making things - what do we have of common standards, units and criteria for assessment? Do we have an approach to build criteria? If so, do we share common standards and tactics to transition knowledge across silos of research? I argue that we do not, and this undermines the maturation of our field as a research discipline.

Industry, today, tends to rely on criteria such usability, accessibility, or adoption - these have a clear footing in the demands of business. We also see modules emerge in technical research settings - like the 7 point Likert scale or the Technology Readiness Scale (TRL).  But in the domain of more academic design research that touches humanities, environmentalism, and social change - what are the measures? What are the demands of our research community? Suddenly the conversation explodes to topics like frameworks or big debates on what is design. Frameworks for sustainability and social justice abound. Design is this and that. Every PhD has a framework. This can be all well and good, but note, Nordhaus wasn’t assessing light as a moral object or relying on a philosophical framework. His work was powerful because the assessment was granular. Equipped with the labor function, he could examine how a set of product iterations changed the history of human labor, and by extension, the quality of life over time  – thus satisfying the greater demand of his research field.

So I question, by what means can we also systematically extrapolate upon the findings of design research with a little more precision and a little less preference?  There are probably 70,000 design frameworks created in the last 50 years that sit on dusty shelves - so maybe we too, can take the risk to get more granular? This does not sound like a popular sentiment, yet granularity also demands accountability, driving our field to do better research and to generate stronger research. Research that moves mountains.

We might all agree that transportation design for example, is not merely about aesthetics, or about miles per gallon in an era of climate change. To design forward, can we thus borrow and build forward leading measures of impact by which we can compare our designs across the whole span of categories? Be it the years of sunlight captured in fossil fuels, the carbon units that deplete the atmosphere, or the impact on human lifespan distributed across our future generations via the scalar modification of automobile infrastructure?  In contrast, I've heard 15 years of critiques about various sustainable design works "lacking a certain soulfulness." What does that even mean?

More broadly, are we yet in a position - as a community - to carry out the work, to build some standardized and shared evaluatory mechanisms of design in the world, through which we build a more rigorous research discipline? Of course, that isn't something to which everyone would agree that we need, or should pursue. Yet without such an approach, how can one really justify any body of research in design as avant garde or not avant garde? Like Ken, we can examine the rigour of structure and method. But to look at such work and make inferences on how it matters in the universe? We suddenly default to the artistic tradition of speculative critique.

Decades ago, the notion of design as a research field was awkward and poorly defined. No doubt the argument that we should together build and commit to future-looking indicators to better assess ourselves, and our works, perhaps generates the same feelings. But we should not be afraid to be more accountable to one another or to challenge our future selves. Rather, we should be emboldened.
—snip—

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