Consequential Research

I was heavily influenced by two documents I read back in the 1970s. The first was an independent study project I did while working on my Ph.D. My advisor had me read Design of water-resource systems: New techniques for relating economic objectives, engineering analysis, and governmental planning by the Harvard Water Program (Maass et al. 1962). This was the greatest thing I had ever read. With the methods in this book and a computer, I could solve all sorts of water problems. I just had to define the objective function, some constraints, and a few coefficients and I could improve the world. I just could not wait to get to work.

I eventually went to work at the U.S. Army Corps of Engineers Waterways Experiment Station in Vicksburg, Mississippi, and started solving the world’s water problems. The Corps, being a practical organization, was interested in research that had some payback, so I did an analysis of the optimization studies I found in the literature. I wanted to show the great return-on-investment for my proposed work. I contacted the authors of many of the papers I had read. The typical response I received went something like this, “We actually did not implement the results of our paper. We could not determine the coefficients exactly, and the folks who would have implemented our solution did not completely trust it.”

The second important document was, “How to Plan an Inconsequential Research Project” (Ettinger 1965). In it, Ettinger noted that doing research with consequences was potentially dangerous, and the water profession had developed methods to protect it from consequences while maintaining funding. Among the techniques he described was the anecdote:

A bystander passes a drunk on all fours on the sidewalk under a street light looking for a $20 bill. After failing to find it, he asks the drunk where he had lost the money. The drunk says “over there in that vacant lot.” Bystander asks, “Why aren’t we looking there?” Drunk says, “There are rocks and broken glass in the lot and the light is much better here on the corner.”

(Ettinger 1965).

The similarity between the drunk and researchers forcing real-world problems to fit their optimization modelers struck me. Nevertheless, I have spent a good bit of my career trying to use optimization where I thought it made sense. In 1985, at the “Battle of the Network Models,” I made a prediction that in a few years, we would all be using optimization to solve all sorts of water problems. It was not the first time, nor last time, I was wrong.

Over the years, I have become a critic of much of the research on applying optimization to solve water problems. Some view me as a knuckle-dragging Neanderthal opposed to progress. I see myself more as the young boy in the “Emperor’s New Clothes,” who points out that in spite of all the high praise for his clothes, the emperor is really naked.

This sometimes makes me look like a hypocrite since I have worked on several optimization models for my employer, Bentley Systems, and we have users of those products. There I find myself spending a lot of time making certain that users know the assumptions and limitations that go into the products. Not having optimization tools is much less of a problem than using such tools without knowing its assumptions and limitations. I admit that optimization has been the least consequential portion of my life’s work, although I still pursue it.

There are those who will claim that their optimization has saved millions and millions of dollars over the years, but I am skeptical. First, the optimal solution is often compared with awful baseline solutions. Second, if an optimization saves, for example, $8 million and the original solution was reasonable, the optimal solution also reduced the benefits of the project by something like $7.9 or $8.1 million. Third, the optimizations are based on some sort of forecast and it saves money by removing any safety factors, so that the price of an optimal solution is a system that may fail 50% of the time.

These optimization researchers are very intelligent, even brilliant; they are some of the brightest people I have known. Someone would need to drive a railroad spike into their brains to bring their intelligence down to merely smart. The problem lies in the fact that the problem being solved needs to be formulated along the lines ofwith and without multiobjective or uncertainty considerations.

Somewhere between the real-world problem and these expressions, important aspects of the problem are invariably lost. Researchers often do not even realize the limitations in the assumptions they make and do not appreciate it when reviewers point them out. Worse yet, papers that get published with hidden limitations serve as the basis for future papers with similar limitations.

I am frequently asked by bright young graduate students for advice about their research. My usual response is, “If your advisor suggests a project in optimization, run, do not walk out of your advisor’s office. Get away. Do not try to save your advisor. He already drank the Kool-Aid. Run. Save yourself.”

I understand the attraction of optimization. If you work in this area, you do not need to develop any new theories, collect any field data, or conduct any lab analyses; and it is very difficult for anyone to prove you wrong. Usually, a typical research project consists of the following steps:

With optimization projects, a researcher can skip Steps 2, 4, 5, 6, 8, and not do much with Step 9.

Usually a researcher in this area will define a problem, read the literature, select a method, modify the problem so that it fits the method, write a program, and publish a paper. The problem lies in the step of modifying the problem to fit the method. This usually involves some (often hidden) assumptions that can result in meaningless or even misleading solutions. This would not be problematic if the researcher carefully pointed out the limitations in the solution. Instead, the assumptions and limitations are incorporated in a publication and becomes the starting point for the next researcher, who has as little appreciation of the problem as the first researcher.

Some of the fatal limitations that get passed down through water distribution research include

Virtually every optimization paper has one or more of these limitations, usually without mentioning them.

In spite of the preceding observations, there is a place for research in applying optimization to water problems. However, a few years back, I looked at the papers on water distribution published in the Journal of Water Resources Planning and Management and found that more than half were on optimization. There seems to be an inordinate amount of work in this area.

Not all research in the past few decades has been inconsequential. Some great work has been done by outstanding individuals. I want to highlight what I consider some great examples of consequential research. I wish I could name them all, but this paper would be too long and I would miss many anyway. My apologies to those I left out.

First, there is the work of individuals on numerical solvers, most notably Ezio Todini and Lew Rossman, but there were many others, building on the work of Hardy Cross. However, this work is more numerical hydraulics and somewhat foundational but orthogonal to planning and management support that I want to focus on.

Next, comes my honorable mention list, which would include work by Walter Grayman, Mirjian Blokker, Bob Clark, Mark LeChevalier, Angus Simpson, and their associates. These individuals based their work on sound experiments, solid theory, and integration of results into engineering practice—the necessary steps for consequential research.

Finally, I have developed a list of what I consider to be the top five research works in the past few decades in water distribution planning and management. These represent not individual papers but a body of work over several years with numerous collaborators.

Fifth: Kobus Van Zyl and students, who conducted experiments and developed theoretical models to understand the relationship between pressure and water system leaks.

Fourth: Joby Boxall and Stewart Husbands and associates, who developed models to explain solids motion in water distribution systems, based on experimental data.

Third: Martin Lambert and students, who took a problem of excessive head loss in real pipes with soft boundary layers and conducted experiments to understand how these films behaved in ways that are not explained by standard approaches to head loss.

Second: Yehuda Kleiner and Balvant Rajani, who advanced our understanding of why pipes break and how to use those predictions in managing water main replacement.

First: Steve Buchberger and students, who collected extensive data on water use patterns, formulated a theoretically sound Poisson rectangular pulse model to explain water consumption patterns and worked to see the results of this research incorporated in water engineering practice. That is consequential research at its best.

The best work consists of identifying a real world problem, collecting and analyzing data that has not been collected before, formulating sound models to describe the underlying processes, rigorously testing that model, and providing insights to practicing engineers dealing with the original problems.

Years ago, I lamented the gap that existed between water research and practice. Over the years, I have seen that gap grow to the extent that practicing engineers and researchers have essentially no hope in communicating because they do not even speak the same language. If the two groups do not communicate better, we are faced with the prospect of more and more inconsequential research.

Although I closely follow the water and sewer hydraulics literature, I learned the most from listening to people like James Knox, when I worked at the City of Austin, and Tony Gangemi, when I worked at Pennsylvania American Water Company, than from any journal. They were senior system operators with no engineering degrees who taught me so much. I wish that all prospective researchers would be required to serve an apprenticeship at a water utility or consulting firm, learning the basics before getting into their thesis work. Of course, that will never happen for a variety of reasons. However, we can do better.

As a first step, I have a homework assignment for readers. If you are in a research environment, find the engineers and operators in the local water/sewer utilities and invite one or two of them to lunch. Talk with them about what they are doing. Better yet, listen to what they are doing. You will get all sorts of research ideas over lunch and when you need some help getting data, you may find you have a needed friend working for the water utility.

Similarly, if you are working for a water utility or a consulting firm, make friends with several faculty members at the local university. Offer to buy them lunch. Do not be concerned about the fact that they have Ph.Ds. They are more afraid of you than you are of them. Someday, that relationship you build will pay off.

Not all research can be ground breaking or award winning or even consequential, but an excessive amount of what gets published seems inconsequential, primarily because it ignores real-world considerations. By looking at the way the aforementioned top researchers approached their work, young researchers can produce more consequential work.