The joy of hands-on design, implementation and operation of technical gadgets that spring from the imagination can be the beginning of an engineering career. As that engineering career progresses, the amount of hands-on work often diminishes, and the technical depth earned from enduring many soldering iron burns is traded for technical breadth and managerial responsibility. Engineers who take this career path will find themselves managing organizations responsible for projects that are well outside of their areas of expertise. How do they decide, at business-relevant speed, which projects merit access to organizational resources?
The Buck Starts Here
In a position with responsibility for determining which projects are funded and why, it is important to be able to quickly evaluate the technical ideas behind the projects to gauge which investments will produce an impact significant enough to justify the opportunity cost. And the decision must be made even if the ideas do not lie squarely within one’s area of expertise. Fortunately, there is a straightforward path towards that decision. The path starts with breaking the decision-making process into three steps:
- Does the idea make any sense?
- Is the technical plan complete and credible?
- Does the potential return on investment match the opportunity cost?
Let’s take the first step.
What Are the Rules?
Ideas make sense in the context of the governing rules. Any new idea that lives in the physical world must obey the laws of physics, including conservation of energy, the three laws of thermodynamics, Maxwell’s equations, etc. And any new idea that lives in the infosphere is bound to the principles of information theory, such as Shannon’s noisy channel coding theorem and the Nyquist-Shannon sampling theorem. Not to say that the understanding of these laws and theories never changes — often a new insight or interpretation applied to a law or theory is what leads to a significant innovation.
When Fourier first published his transform algorithm in 1822, it revolutionized the understanding and analysis of everything from crystallography to information processing. But the methods of calculation remained pretty much the same until 1965, when Cooley and Tukey published their paper that led to an explosion of computer-based applications. The math didn’t change; how the math was applied changed, and that changed the world.
Likewise, the MP3 audio coding format introduced in 1991 essentially created the music streaming market by compressing high-quality audio with almost no discernable effect, reducing the required bit rate by about an order of magnitude compared to CDs. MP3 doesn’t violate the Nyquist-Shannon sampling theorem, rather it reinterprets the boundary conditions of the sampling through the lens of a human psychoacoustic model.
But it is surprising (or maybe not!) how many new ideas do blatantly violate the rules. How can anyone tell without going through a complete mathematical analysis?
In the physical world, look for where energy is stored and how power flows. Does the system seek the minimum energy solution, or does it magically create structure and organization? How does the power get in and out of the circuit? Do the claims of efficiency line up with where power is gained and lost in the circuit? Can the circuit handle the wasted power without melting or self-destructing? These principles apply across electrical and mechanical systems alike.
In the infosphere, information really is power, so follow how it flows and where it is gained and lost. Does an algorithm collect enough information to operate? Does it increase information content, and if so, how? Is information conserved? Where is information lost, and what impact does that have on the algorithm’s output? Answering these questions goes a long way towards a good assessment of the idea.
What’s the Game Plan?
The next step is to examine the proposed technical plan to judge if it is complete and credible. Ask the person pitching the idea to break down the process, circuit, system, and/or algorithm into its basic steps or components and tell you which one(s) they are improving and by how much. Frequently the person pitching the idea will be surprised at how much this exercise clarifies their thought process, and sometimes it can even inspire a different approach.
Now also is the time to make sure the proposed idea does not duplicate research that already is being done. Emergence of a new technology usually is accompanied by a rapid increase in research projects and publications on the topic, as happened with nanotechnology, quantum, terahertz sensing, and a number of other technologies. Is it really an impactful new idea, or is it an incremental improvement hoping to ride the wave of hype? Does the proposed technology already exist? Scan technical publications, commercial trade magazines and catalogs, patents and patent applications, and make full use of online tools such as IEEE Xplore, the Defense Technical Information Center (DTIC), arXiv, ResearchGate, and USPTO.gov to aid your search.
Even if the idea is good and the technical plan is complete and credible, can the team execute it? Experience shows that paper credentials of the team members rarely tell the whole story. Team success on prior research projects can help but also does not guarantee results on the current project. Instead, try to determine if the team completely understands the objective and impact of the project. The specifics outlined in the original technical plan always change over the course of a development project. If the team can stay focused on the objective and impact, the project will be a success.
None of this process exists in a vacuum. If the idea lives in an area that is too far outside the comfort zone, get another opinion from a trusted colleague or subject matter expert. If the idea is just too good to pass up but the team is lacking, get them the help they need by connecting them with other experienced researchers, successful teams, or colleagues and consultants outside the organization. A mentor with experience making similar decisions and a good understanding of organizational structure, processes and objectives can be an enormous help.
Where’s the Moneyline?
The last step is to assess the potential return against the investment opportunity cost. Every organization has a business or technical roadmap that manifests in different ways, so evaluating return on investment generates different questions, depending on where the project lives. Corporate labs are interested in things like how does this project contribute to a current product? Does it create a new product, or even better a new line of business? Does the team have strong collaborators in the appropriate business area? For a research group, how does this project accelerate the research roadmap? Does it open up new avenues for exploration? For a funding agency, how much or how fast does this proposal advance technology towards program goals or should the budget be reserved for something more relevant? Does it accelerate the technology roadmap, or even better does it make a large enough leap to render the current roadmap obsolete? Is the transition plan realistic? Does the researcher have a transition partner on board who has put skin in the game?
If the project does align with your roadmaps, assess the idea’s impact at the system level before the final sign off. Many innovations that make significant improvements in speed, performance, efficiency, or cost of one step or component can drive the need for additional support — circuitry, data conversion, cooling — that can offset the gains or in some cases make overall performance worse. If the project does not enable significant improvements in system performance or change pricing enough to have a positive impact on customer demand, then the investment might not be worthwhile.
Summary
Trading technical depth for technical breadth and outward focus is a natural occurrence as an engineering career advances. With a strong background in basic laws and theories and good situational awareness of the existence and maturity of the technology ecosystem, it is possible to assess new ideas at business-relevant speed without having to be a specialist in everything. So it is important to develop and maintain the ability to map concepts and ideas onto fundamental principles and understand where the ideas fit in the world to make that engineering career more successful and satisfying.
The author would like to thank Dr. Patricia Neuman, Sc.D. and Dr. Scott Bukofsky, Ph.D. for their valuable contributions.
