Heinrich Edgar Arnold Laue
Participating in local science fairs was a highlight of my school years, teaching me about scientific investigation and discovery from a young age. A design-focused project greatly influenced my decision to pursue a career in engineering, and I only recently started appreciating the link between my experience at science fairs and my present passion for research, writing, and public speaking.
Editor’s Note
In this issue of IEEE Antennas and Propagation Magazine, Dr. Heinrich Edgar Arnold Laue contributes an interesting article on the topic of innovation as a balance between novelty and conventionality. Dr. Laue is one of the 2022 IEEE Antennas and Propagation Society (AP-S) Young Professional Ambassadors as well as serving as the Students and Young Professionals Coordinator for the IEEE South Africa AP/MTT/EMC Joint Chapter. This article looks into a practical approach for introducing new ideas into a conventional domain, leading to innovation. It is a must-read for all young researchers on how to innovate and make an impact.
We have many more exciting articles planned for this column in future issues. Anyone who would like to contribute to the “Young Professionals” column or has any suggestions on topics of interest may contact me at cjreddy@ieee.org. Follow us on LinkedIn, at https://www.linkedin.com/company/ieee-aps-yp, for the latest updates and events that are of interest to AP-S Young Professionals.
My biggest challenge during science fairs was coming up with an idea for a project. I always wanted to come up with my own idea and refused to simply repeat an existing experiment. I mostly had no idea where to start and would spend not only days and weeks but months trying to come up with a topic. The problem, I suspect, was that I was trying to pull new ideas out of thin air. I should probably have spent more time reading scientific literature than scouring the depths of my own mind.
When conducting research, you are faced with a similar challenge of coming up with new hypotheses and making new discoveries. More generally, innovation—coming up with an idea for a business or a product, for example—requires some form of novelty.
But how are new ideas generated? Theories of creativity, the study of how innovation works, indicate that innovation happens when existing ideas are combined in new ways [1], [2], [3]. New ideas grow not simply from existing ones but from existing ideas brought together in new ways. If I knew this earlier, I would probably have approached my search for science fair topics differently.
Economist Martin Weitzman [3] likens innovation to the cultivation of new botanical varieties from old ones. We often talk of the cross-pollination of ideas, which turns out to be a perfect analogy—existing ideas coming together to breed new ones.
However, Weitzman points out that with the vast amounts of knowledge available today, the challenge lies not primarily in finding new ways of combining ideas but rather in identifying those combinations that are actually useful. He quotes the famous mathematician, physicist, and philosopher Henri Poincaré [3], who said the following in the context of mathematical creativity:
To create consists precisely in not making useless combinations and in making those which are useful and which are only a small minority. Invention is discernment, choice. … Among chosen combinations the most fertile will often be those formed of elements drawn from domains which are far apart. Not that I mean as sufficing for invention the bringing together of objects as disparate as possible. Most combinations so formed would be entirely sterile. But certain among them, very rare, are the most fruitful of all. … The true work of the inventor consists in choosing among these combinations so as to eliminate the useless ones or rather to avoid the trouble of making them, and the rules which must guide this choice are extremely fine and delicate.
What are these delicate guiding principles that Poincaré speaks of that can maximize our chances of finding useful combinations of ideas? One possible guiding principle is to understand the balance between novelty and conventionality that is required for innovation. Novel combinations can be defined as ideas “drawn from domains which are far apart,” whereas conventional combinations stick to closely related domains as per the established convention. Having only novel combinations of ideas will clearly not suffice as you will end up with a mixed bag of mostly “sterile” combinations. On the other hand, sticking only to ideas that are conventionally considered closely related will prevent you from discovering the “most fertile” combinations.
The most useful ideas will often proceed from a careful balance between novelty and conventionality, from exploring foreign lands yet staying close to home. Getting this balance just right greatly increases your chances of making not only discoveries but impactful ones.
In 2013, a sociologist, an economist, and two data scientists, Uzzi et al. [1], came together to investigate how conventionality and novelty must be balanced to generate high-impact, i.e., highly cited, scientific research.
They found that high-impact articles are highly conventional yet with a dash of completely unexpected novelty. In other words, articles that tend to be cited often are firmly rooted in convention with a hint of something completely new and unexpected.
To determine this, they considered the pairwise combinations of all of the references in a particular article. They would take two references and determine how often their respective journals appear together in the wider literature. Journals that are cited together often are considered a conventional pairing. Think, for example, of the closely related IEEE Transactions on Antennas and Propagation (TAP) [4] and IEEE Transactions on Microwave Theory and Techniques [5]. Journals that are not cited together often (e.g., TAP and Life Sciences) are considered a novel pairing. In this way, the combination of sources in an article was used as a proxy for the combination of ideas that informed the findings of the article.
The highest impact articles had overwhelmingly conventional combinations of sources and yet a few highly unconventional combinations. Such articles had almost twice the probability of being highly cited or high-impact articles [1].
In line with Poincaré’s observations, balancing novelty and conventionality in practice turns out to be quite challenging. Instead of novelty and conventionality bearing equal weight, the optimal balance is heavily skewed toward conventionality. Imagine not simply an acrobat walking a tightrope but a tightrope walker with an exceedingly heavy load on one end of his balance pole.
In the remainder of the article, we will consider a practical approach to achieving this balance for high-impact innovation. We will then briefly consider the novel field of compressive antenna arrays as an example. Finally, we will consider some more personal applications and see how being both a specialist and a generalist can benefit your career.
Figure 1 presents an approach to balancing novelty and conventionality to maximize your chances of discovering useful new ideas. Let us consider each of these points in more detail.
Figure 1. The proposed methodology for high-impact innovation.
As the adage goes, you need to learn the rules before you can break them. Before you can start taking inspiration from other domains, you need to be well grounded in your own.
The obvious scenario is where you are making contributions in your own specialty. Clearly, you need to master the fundamentals of your own discipline before making any kind of novel contribution. The less obvious scenario is the converse, where you wish to apply an idea from your domain to a foreign domain, especially if you are not an expert in that other domain. In that case, you will need to first spend a significant amount of time mastering the fundamentals of the foreign domain. Alternatively, you can collaborate with an expert in that field. Remember the skewed balance toward conventionality—it is much easier to apply a foreign idea to your own domain than to apply an idea from your domain to someone else’s.
For example, making contributions to the field of antennas requires a solid understanding of the conventional properties of antennas, such as gain, directivity, return loss, sidelobe level (SLL), etc. You can easily take inspiration from the most obscure source, for example, something you see in nature, and still design a new antenna that is measurably better in conventional terms. But imagine a biologist trying to design an antenna without extensive training in electromagnetics—that is a different story.
As you bury yourself deeply in your own domain, don’t forget to look up! Be curious about other domains and look further for inspiration. Do you see how difficult this balance is, how novelty and conventionality want to pull you in seemingly opposite directions?
I believe that the best way to look further is to develop a general curiosity. In practical terms, this could mean reading more widely—not necessarily just journal articles but even high-quality journalism can broaden your horizons. (This is how I discovered several of the sources in this article!) Going even further, you could find inspiration in nature or the arts. Biomimicry is an obvious example here. Even more profoundly, first-hand accounts tell of Einstein finding inspiration in music not only as a distraction but possibly even as an integral part of his intuition into physics [2].
In terms of your social and professional networks, do not restrict yourself to your own specialization but have a wide range of acquaintances from different specialties, and you might pick up something interesting.
Again, there is no restriction in terms of where you find inspiration. Clearly, there is no guarantee that you will find inspiration for antenna design while reading a book on politics, but do not make that the point. Simply develop a general curiosity for things both technical and nontechnical, and you will be well positioned to catch inspiration when it passes you by.
When you find an idea in a foreign domain that you want to apply in your own domain, study its context and assumptions. The level to which you will need to master that topic will differ, but the key is to have a deep enough knowledge to identify the assumptions that might not hold in your own domain. The challenge is that such assumptions may be regarded as almost self-evident in the foreign domain, and you might have to delve quite deeply to uncover them. An example of such a scenario is discussed in the case study on compressive antenna arrays to follow.
Once you have identified a foreign idea to apply to your domain, properly taking its context and assumptions into account, the next step is to translate that idea to your domain.
Recognize that there may be differences in terminology. Perhaps this idea has already been tried in your domain, only under a different name. Or perhaps something better already exists!
One of the most important steps is to contextualize the idea in your domain. Contextualization in this case means linking your idea to the existing body of knowledge—helping your idea find a home. If it feels like there is nothing else to compare your idea to, you have likely not developed the idea enough yet. Ultimately, you will have to find something to compare to in order to demonstrate why your idea is superior. In particular, you need to make use of the conventional performance measures you identified in step one because they might differ from those of the foreign domain.
When you have studied the foreign idea with its context and assumptions, translated it to your domain, contextualized it, and established any differences in performance measures, then you can finally apply the new idea to the old domain.
Initially, you may have all sorts of lofty ideas, but they may not all turn out as expected. The real insight and the real contribution might be something completely different from what you had expected, and it might turn out that your idea from the other domain was nothing more than a fresh perspective that led to a new insight. If this happens, don’t hold on too strongly to your initial ideas, but be open to a change in direction. An incremental but real contribution is much more useful than a big but naive idea.
The key to balancing novelty and conventionality is to apply the correct weight to each. While you need to be rigorous with your conventionality, you need to be flexible with your novelty. Hold conventionality firmly in your left hand and novelty loosely in your right. Maintain the discipline and rigor of conventionality and the childlike curiosity of novelty. They are not mutually exclusive but complimentary.
I learned many of these lessons from my journey to the field of compressive antenna arrays. When I first started looking at the topic, the field was little more than the suggestion to apply the sub-Nyquist sampling scheme called compressive sensing (CS) from signal processing to antenna arrays. While there are many other applications of CS in electromagnetics, compressive arrays specifically look at reducing the number of samples/signals in an antenna array. Figure 2 shows a recent example of a prototype compressive array with four antenna elements and two outputs or subarrays [6].
Figure 2. A prototype compressive array. (Source: Taken from [6].)
Following the aforementioned outline, I first had to be well grounded in my own domain and understand antenna arrays in conventional terms. I had to understand that antenna arrays are traditionally designed based on measures like gain, beamwidth, SLL, and steering range before even considering the performance measures of a particular application, like direction finding, for example.
Second, I looked further to the foreign idea of CS for inspiration. I was lucky because the idea of applying CS to antenna arrays had already been proposed.
Third, I studied the context and assumptions behind CS. I needed to develop a working knowledge of CS [7]. Delving into the derivations of CS, I discovered that some of the fundamental theorems rely on the assumption of a large number of samples, which clearly did not apply to antenna arrays, which often have small numbers of elements [8]. This meant that the standard random sampling scheme, where you weigh and combine samples with random Gaussian compression weights, would not work for moderately sized antenna arrays.
Fourth, I had to translate and contextualize the idea of a compressive sampling process to antenna arrays.
By carefully comparing CS and antenna arrays, I realized that, under the right conditions, the concept of coherence in CS translates to SLL in antenna arrays. This allowed me to adapt a coherence-optimization algorithm to minimize SLL in compressive arrays [9]. I could now design compressive arrays with my newly developed SLL-minimization algorithm.
To contextualize the idea, I searched extensively for conventional antenna arrays to compare my new designs to. I ended up realizing that a compressive array is, in fact, a type of subarray system where an overlapped feed network is used to weigh and combine antenna-element signals [10]. Suddenly, I had a host of conventional techniques to compare to!
Finally, I had to be open to a change in direction. When the process of translation had been completed, very few of my original CS ideas remained, but what did remain was a disruption to the conventional way of thinking. Traditionally, subarrays are designed based on particular feed-network layouts, where the approach is essentially to start with the hardware and see what performance you can get. But the lack of hardware constraints in CS, which allows random and therefore arbitrary compression weights, inspired me to remove all hardware constraints when minimizing SLL and consider hardware implementation only at the very end. This led to a new overlapped feed-network architecture with increased design freedom that opened the door to novel array designs while still allowing fair comparisons to be made to existing techniques [6], [11].
The broader question when it comes to your career is whether you should be a specialist with a deep focus or a generalist with a broad outlook. The findings of Uzzi et al. [1] hint toward the fact that the answer is not either/or but rather a careful balance of both. They note that there may be “advantages to being within the mainstream of a research trajectory, … while being distinctive in one’s creativity”.
Some of the most influential people in history have had multiple interests. These jacks-of-all-trades have always been around with names varying across history. Author Michael Simmons [12] gives an insightful overview of this concept of polymathy, noting how, in generations past, we have had:
In terms of modern polymaths, think of the founders of some of the world’s largest companies. Simmons notes that Bill Gates, Steve Jobs, Warren Buffett, Larry Page, and Jeff Bezos have all been described as polymaths.
He offers a view of modern polymathy as being T-shaped. In other words, you specialize deeply in one domain and yet have a working knowledge across a broad range of disciplines. He draws on a powerful aid, the Pareto principle—a rule of thumb that states that 80% of something’s output is typically a result of only 20% of the input. For example, it will take you a lifetime to become a master in a topic, but within a week, you can have a better working knowledge of that topic than most people.
One can see how such a T-shaped polymathy fits within the conclusions of Uzzi et al. [1]. Deep specialization in one field with a dash of inspiration from a completely different one assumes that you have some working knowledge of the foreign domain you are getting inspiration from.
Ironically, Benjamin Jones [13], one of the coauthors of Uzzi et al. [1], spoke of “the burden of knowledge and the death of the Renaissance man,” referring to the idea that as the store of human knowledge increases, an increasingly large burden of education falls on each successive generation, necessitating ever greater specialization. And yet, with Uzzi, he showed that both breadth and depth is required for innovation.
It turns out that the idea of modern polymathy is somewhat controversial, with some arguing that the burden of knowledge will eventually make it virtually impossible to become an expert in multiple domains [2]. However, making significant contributions to multiple disciplines, as Renaissance men like Leonardo da Vinci and polymaths like Henri Poincaré did, is not the only form of polymathy. This T-shaped model of polymathy, for example, where you are an expert in one domain and an amateur in multiple others, is not inconsistent with the trend in increasing specialization [2]. Another form of polymathy is sequential polymathy, where you dedicate different periods in your life to different disciplines. These broader views of polymathy include many gifted individuals from history as examples [2].
My challenge to you is to cultivate a general curiosity and to realize that everything has the potential to be interesting even if it is outside of your current specialization. If you find yourself in a place of deep specialization and are frustrated with the lack of diversity, don’t despair. Being a specialist does not mean that you cannot also be a generalist. Keep specializing, but also, keep exploring elsewhere—read widely, have obscure hobbies, and make diverse friends. Having a broad range of interests, even as a specialist, may just lead to your greatest breakthroughs.
Heinrich Edgar Arnold Laue (hlaue@ieee.org) is a communications engineer with the Namibia Water Corporation Ltd, Windhoek, Namibia. He is the Students and Young Professionals Coordinator for the IEEE South Africa AP/MTT/EMC Joint Chapter and served as a 2022 IEEE Antennas and Propagation Society Young Professional Ambassador. He is a Member of IEEE.
[1] B. Uzzi, S. Mukherjee, M. Stringer, and B. Jones, “Atypical combinations and scientific impact,” Science, vol. 342, no. 6157, pp. 468–472, Oct. 2013, doi: 10.1126/science.1240474.
[2] R. Root-Bernstein, “Multiple giftedness in adults: The case of polymaths,” in International Handbook on Giftedness, L. V. Shavinina, Ed. New York, NY, USA: Springer, 2009, ch. 42, pp. 853–870.
[3] M. L. Weitzman, “Recombinant growth,” Quart. J. Econ., vol. 113, no. 2, pp. 331–360, May 1998, doi: 10.1162/003355398555595.
[4] IEEE Trans. Antennas Propag. [Online] . Available: https://ieeexplore.ieee.org/xpl/RecentIssue.jsp?punumber=8
[5] IEEE Trans. Microw. Theory Techn. [Online] . Available: https://ieeexplore.ieee.org/xpl/RecentIssue.jsp?punumber=22
[6] H. E. A. Laue and W. P. du Plessis, “Design and analysis of a proof-of-concept checkered-network compressive array,” IEEE Trans. Antennas Propag., vol. 70, no. 9, pp. 7546–7555, Sep. 2022, doi: 10.1109/TAP.2022.3188531.
[7] H. E. A. Laue, “Demystifying compressive sensing [Lecture Notes] ,” IEEE Signal Process. Mag., vol. 34, no. 4, pp. 171–176, Jul. 2017, doi: 10.1109/MSP.2017.2693649.
[8] H. E. A. Laue and W. P. du Plessis, “Compressive direction-finding antenna array,” in Proc. IEEE-APS Topical Conf. Antennas Propag. Wireless Commun. (APWC), Cairns, QLD, Australia, Sep. 19–23, 2016, pp. 158–161, doi: 10.1109/APWC.2016.7738145.
[9] H. E. A. Laue and W. P. du Plessis, “A coherence-based algorithm for optimizing rank-1 Grassmannian codebooks,” IEEE Signal Process. Lett., vol. 24, no. 6, pp. 823–827, Jun. 2017, doi: 10.1109/LSP.2017.2690466.
[10] H. E. A. Laue and W. P. du Plessis, “Numerical optimization of compressive array feed networks,” IEEE Trans. Antennas Propag., vol. 66, no. 7, pp. 3432–3440, Jul. 2018, doi: 10.1109/TAP.2018.2829834.
[11] H. E. A. Laue and W. P. du Plessis, “A checkered network for implementing arbitrary overlapped feed networks,” IEEE Trans. Microw. Theory Techn., vol. 67, no. 11, pp. 4632–4640, Nov. 2019, doi: 10.1109/TMTT.2019.2940223.
[12] M. Simmons, “People who have ‘too many interests’ are more likely to be successful according to research,” Observer Media, New York, NY, USA, Apr. 2018. [Online] . Available: https://observer.com/2018/05/people-with-too-many-interests-more-likely-successful-polymath-entrepreneurship-antifragile/
[13] B. F. Jones, “The burden of knowledge and the death of the Renaissance man: Is innovation getting harder?” Rev. Econ. Stud., vol. 76, no. 1, pp. 283–317, Jan. 2009, doi: 10.1111/j.1467-937X.2008.00531.x.
Digital Object Identifier 10.1109/MAP.2023.3262154