“If you study whatever you are studying in great depth, that will pay a dividend...”

[Satinder]: Art let us begin by asking you about your educational background and work experience.

I received a Bachelors, Masters, and PhD in Mathematics and Physics from the City College of the City University of New York followed by a two year post-doctoral fellowship at U. Texas at Dallas.

I entered seismic petroleum research in 1978, working at Cities Service Oil Company in Tulsa, Sohio-BP in Dallas, Schlumberger Cambridge Research and Arco for 15 years before joining U. of Houston in August 2000.

[Satinder]: Your background is basically in Math and Physics?

Yes.

[Satinder]: So how come you decided to switch over to geophysics?

I needed to earn a living. (laughter) . There were very few jobs in physics, at that time — and working as a post-doc in Dallas, a vibrant center of oil company and oil service companies, it was natural to see if it was possible to work on interesting and challenging problems and also earn a steady and reasonable income. I’ve been enormously fortunate to have had the opportunity to research fundamental prioritized seismic physics problems while enjoying the benefits of working for the petroleum industry.

[Bill]: Your work has been unique, beyond even the best minds in our business. The management you’re talking about obviously saw the uniqueness, as opposed to just the standard repetition. It’s hard to look back at this point and see who would doubt the conclusions you’ve come up with, but I can see at certain points you must have been seen as something of a heretic.

Many thanks for those kind words. Oh yes, a heretic. Early on I was naïve and surprised by how much opposition to new thinking there would be from both academic and industry geo-scientists, mathematicians and physicists. Human nature, inertia, egos, fear of being superseded, and collisions of ambition account for some of the resistance and negativism. Now, I’ve come to believe that new ideas will have a concomitant and expected resistance, to understand, predict and anticipate it. If you want most people to think well of your efforts; go into mild variation of current thinking research, which by the way is a useful and necessary enterprise, but different from developing fundamental new concepts and step change capability.

In hindsight, I’m even more impressed when I think about the amount of support we did (and do) receive, in particular the depth, extent and duration of support we received from management — not necessarily universal support, but all you need is enough to carry forward the program. Among those we are grateful to are: Hamid Al-Hakeem, Jack Golden, Jamie Robertson, Jim O’Connell, Dodd DeCamp, Phil Christie, David Campbell, Bill Clement, James Martin, Ken Tubman, Reid Smith, Bee Bednar, Craig Cooper, Andre Romanelli Rosa, Lincoln Guardado, Vandemir Oliveira, Paulo Siston, and Jurandyr Schmidt for providing the support and environment necessary to carry out long-range high impact prioritized research.

In our experiences these enlightened and courageous managers shared a certain scale of inner-character, imagination, of confidence, a fascination (rather than fear) of new visions of what might be possible, and those traits often propelled their own careers with rise within the company.

The supportive management I’m describing were often geologists or geologically oriented — they just had a certain personal openness and orientation because they had this kind of courage and flexibility and willingness to support those ready to be “the first to walk into a dark room”.

Many Mathematicians and Physicists are not necessarily better suited than others to do creative things. It surprised me to come to this way of thinking. They are often attracted to their discipline because things seem reasonable and ordered. One can move away from the trouble of the real world, to a world where if you add one to both sides of the equation and integrate, it all works, it’s all fair. The real worlds often not fair, people get hurt. Math can be an escape to a world of fairness. However, when you do really creative things, it doesn’t come from math and physics alone. Most mathematicians and physicists like most people in general, want comfort in the current format, in the current framework. To do creative things you have to jump outside that framework, where logic cannot take you, and trust your intuition, to attempt to reach a superseding framework. It’s your humanness that separates you from merely manipulating formulas and it is intuition and feeling that are both the source of inertia and creativity. In my view, math–physics capability and knowledge of geosciences is a necessary but far from sufficient condition for significant creative contribution.

With the inverse scattering multiple attenuation research, we didn’t start with rigor to begin with, it largely began as a loose set of guesses and, then we sought a mathematical expression for that thinking, and refinement of concepts by testing and evaluation. “If this is sort of how the internal multiple might start to be created in a forward scattering series maybe this is how it starts to be removed in the inverse ...now can we express that thought as a guessed formula and evaluate its validity, and refine and rethink the concept if necessary...that’s how it started.” It became clear that the inverse scattering series had the potential to remove multiples and image/invert primaries at depth without the traditional need for a velocity model. Mining that potential into stable and practical algorithms is far from trivial. The entire series promises to input all your data at once and output the earth...unfortunately that doesn’t converge, in practice... how to cajole and finesse useful information from that overall series gave rise to a staged and task specific subseries strategy: locate where free surface multiple removal, internal multiple removal, imaging primaries, inverting primaries are located within the series...that strategy has been useful and impactful.

When you take a step where there is no framework, you trust in your humanness. It’s your humanness that gives you your edge. There are computer programs now that can do mathematics better than we can, it can arrange equations, and it can solve equations. Our edge is first of all understanding what it means, interpreting it, and going where that manipulation can’t go because there is no logic step yet. I think we need to educate and require that our students have strong capabilities in the tools, but they should also trust their intuition. Gut feel, that’s what gives you the edge. Roger Penrose, a professor at Oxford, wrote “The Emperors New Mind”, a book which demonstrates that it is impossible for a computer to match the human mind now, because our physics is fundamentally inadequate to describe the human mind. There’s a part of creativity that has to do with taking a step that you can’t explain. In our field there is a big component of non-rigor to it at the beginning, then others come and fancy it up and make themselves happy, that often takes years. There’s an obvious important place for rigorous mathematics, to clearly understand the assumptions and conditions behind your algorithm- but if you’re trying to take a step that will provide a significant new concept, and potential capability, I know of no step that first came from only deriving things.

[Satinder]: Art, I was looking at your research interests, and it says, “Research and development of new seismic technology that enables exploration and production of hydrocarbons, a prioritized list of problems is identified which is felt will have the highest impact”. So what is your prioritized list and what kind of problems are you working on?

In general, imaging at depth and delineating large contrast targets, with complex geometry, beneath a complex overburden such as basalt, salt, karsted sediments and volcanics are outstanding and highest priority issues for E&P and hence, are at the top of our list. For example, we hear from Oil Company operations people that imaging beneath salt was, and is, their biggest obstacle to current effectiveness in deep water GOM. That’s something we didn’t have particular knowledge of; we certainly didn’t have knowledge of velocity analysis. We were involved in development of migration -inversion theory, which along with all current depth accurate imaging techniques assumes an adequate velocity is achievable. We were spending a lot of time on multiples, 10 or 12 years, we could have continued, that would be an easy road. We chose not to do that. That would be boring. It’s not dangerous anymore. There’s a bit of excitement in hearing today at the DL talk “you’re going to get the accurate depth image when you haven’t got the velocity, before or after, give me a break!” Those same people thought it impossible to attenuate all multiples without knowing the subsurface... now it’s an industry standard. It was hard to fathom that that could be possible back then. Now we are pursuing imaging and inversion at the correct depth beneath complex media, without the detailed velocity: It’s intriguing, it is relevant, and most important it is very highest priority for E&P and it deserves our attention. In exploration and production you want more effective capability, not solving insignificant problems that publish useless papers, with low priority issues/parameters. If you are solving the most significant science, stepping out, then you are having a step improvement in prediction and a step reduction in risk. There’s an alignment between the interests of science and the petroleum industry; because they are both best served by solving prioritized problems. A drill is empirical, it’s experiment. All your mathematics and all your models don’t mean anything until you do your experiment, it isn’t science until then. To paraphrase Francis Bacon and Albert Einstein, all the chicken scratching on the blackboard is philosophy until you experiment, and for us, the experiment is the drill. There’s a very high bar for exploration and production, it has to be effective. It has to move the drill from a less to a more reliable location.

Publishing papers is a walk in the park, producing truly new and impactful methods and algorithms is another thing altogether.

[Satinder]: My next question is about Bob Stolt. You spent a lot of time with him. He came up with this FK algorithm at a very opportune time. It helped people to migrate data quickly. Could you tell us something more about Bob Stolt, what is he working on now?

After his FK paper, Stolt made pioneering contributions to migration-inversion and inverse scattering multiple attenuation. He published a paper just last year on data reconstruction, extrapolating, and interpolating data with a better model. Stolt is very deep, very capable, enormously productive and creative and very quiet. I often have a need to explain to people what we do, when someone doesn’t understand I feel it necessary to try to make it clearer. Stolt has a confidence that, he understands, and if you don’t understand perhaps that’s your problem. It’s refreshing to see. Working together with Stolt is a special privilege; it also provides a good balance to that issue for me.

[Bill]: I followed your interaction with Berkhout. I was very impressed with your reply after he acknowledged that you were correct.

His acknowledgement, at the SEG and EAGE, speaks to his integrity. Berkhout is an example of a person with a lot of physical intuition. In our personal history, we had a bit of an adversarial relationship early on. People found it amusing and entertaining. We sat down and decided to collaborate. Guus supported and encouraged that and was very proactive in that cooperation.

An opportunity was arranged for me to be a visiting professor in Delft University. He was a very gracious and warm host to my family, and me while we were in Delft. The thing that impressed me the most was when I would work one on one with Berkhout in Delft, was that he was just a regular guy struggling with some kind of concept he could not quite write down. He has a lot of creativity. He has made numerous significant theoretical contributions, and he makes sure they are applied and impactful. We learned things from their group, and vice versa, about the nature of multiples. Each group got stronger. First of all we were competing, even though it was cooperative, we were competing. And we both drove harder to the internal multiple on field data because we knew the other one was after it.

[Bill]: The main controversy was the need for the background field?

That’s right, which he dropped. So now we are at a similar juncture on that point. There are still substantive differences between our methods for multiples, beyond that point. When you can isolate the reflector in your data where an internal multiple has its downward reflection there are computational advantages to his approach...when you are interested in attenuating all internal multiples without any interpretive intervention, or picking reflectors or anything else, the inverse scattering internal demultiple algorithm is the method of choice. Both methods belong in your toolbox.

In our current research, we’re saying you don’t need the background velocity detail to get a detailed image in depth. As you could see there were quite a few people in the audience today who were not comfortable with that assertion. At the least, we know it’s new when there is that degree of discomfort.

[Bill]: I think the discomfort today was in the lack of background field for the depth image.

Right. Because that’s new. 12 years ago if you said you were going to predict the multiples without any information about the earth, you were going to have a section with the data and a section with the ringing from the salt predicted without knowing top or bottom of salt they would have thought you were insane. Fifteen years ago processing primaries were conceptually more advanced than processing multiples; now that situation is reversed. Free surface and internal multiples can be attenuated today with absolutely no subsurface information whatsoever about the heterogeneous and/or anisotropic earth by arranging certain distinct additive and multiplicative communications between the entire recorded wavefield . Multiplicative communication is the key.

Current leading-edge imaging methods, once you have settled on your velocity model, only allow additive communication between events that have experienced the same reflector and, hence, an inadequate velocity model will result in an inadequate image in depth. Our current research seeks to extend the vision and capability to processing primaries that we earlier provided for removing multiples. Allowing other specific types of distinct additive and multiplicative communication between ALL primaries at once, contains the conceptual possibility of imaging and inverting all primaries, at their correct spatial locations, without knowing or determining an adequate velocity model. This provides a totally new vision for primaries aimed at addressing our currently most significant and intractable E&P problems. That some might find this unbelievable today and not deserving their attention and support is not surprising; what is truly amazing to me is the breadth and depth of industry support world-wide and direct industry collaboration we have received. That’s an extremely optimistic and positive note about the petroleum industry.

In our early history Migration -Inversion, a form of migration before AVO, was received with the biggest negative blowback, both from people in migration and people in AVO. They made it very clear, in the strongest terms possible, just how crazy we were. Today, it’s just another industry common practice.

[Bill]: You’re saying the migration people didn’t really believe the amplitudes they came up with?

There are people and there are people. There are people who are sort of the real researchers, and then there are sort of the followers. The followers tend to be dogmatic. There’s a leader and then there are people who might get some business out of it, and they are not always of the same character, they’re running a business. The followers tend to be more rigid than the person who pioneered the idea. They get this idea and implemented it, and their career is depending on it. They themselves are not creative capable, they are protégés in some way. Many migration people stated “they were not interested in amplitudes” and the AVO mantra was “ we can ignore multi-D effects on propagation and reflection , because our 1D model is closer to the real 3D world, (since both are odd numbers), than 2D is to 3D. Come back with Migration-Inversion when you are doing 3D processing”. The guys who are really doing new things more often than not can accept other new things. That’s a big test of the mettle of a scientist. You first demonstrate your respect of science by trying to improve upon it. The toughest test is to know that you yourself will be superseded. Of course we don’t try to make that easy, we try to keep moving, but it’s going to happen. Everything we do has assumptions including all the things we said at the DL talk today, and we make them, acknowledge them and argue for their reasonableness. Today’s reasonable assumption is invariably tomorrow’s high obstacle to effectiveness.

[Bill]: I don’t think anyone would ever accuse you of being an obstacle. I think people would accuse you of testing their ability to think beyond the box.

Bill thanks for that and your other wonderful compliments.

In real research you have to be prepared to fail. Stolt and I worked on something in the late 70’s and early 80’s that we eventually decided was intractable . If you’re really in the new research business, that’s something for managers to understand, and also in universities. If everyone were showing progress, I would say, “Where’s the failures?” If you’re not failing you’re not taking chances. You’ve got to have some rate of failing. Stolt and I, separately, he was at Stanford, I was at Cities Service Oil, were looking for a closed form solution to the simplest multi D earth: velocity varying in x and z. Just find an algorithm for that type of model , without small earth property changes or other linear assumptions, which didn’t require a series. We worked very hard, looked all over the world, and tried to solve it ourselves, and couldn’t find a solution. We shut it down; you’ve got to know when it’s enough. When you do that it isn’t a waste of time. We learned a lot of things, which were tools for other problems. How do you in a tenure system, or an industry judging of research, allow for people who have potential big steps within them to have the flexibility to fail. If you’re not allowing that, it’s only going to be small variations that you are going to get. You’ve got to have the right people, you give some people too much freedom, they’ll go sit on the beach and drink pina coladas. I had a great manager at Arco, Al-Hakeem: he said “why should we send you to Brazil, if I think of what’s best for Arco for next year, I shouldn’t send you to Brazil. But If I think what’s best for Arco for the next ten years, it makes sense. It will give you a place to think.” It was that, and I am indebted to him. All of the multiple research had its origin there.

[Bill]: Is it your perspective that companies have all changed for the worse now?

I think the oil companies are moving in the wrong direction in general; too much short term thinking on research and technology development, too much outsourcing -there are several hopeful exceptions, however, and reason for measured optimism. You don’t outsource what you consider critical to your business success and competitive advantage. On the other hand, I have also been extremely encouraged, and frankly positively surprised, by the broad and extensive industry support of our efforts within the Mission-Oriented Seismic Research Program at UH. Speaks volumes about the interest that exists within the industry for supporting fundamental research when it focuses on relevant issues that have the potential of providing significant increased effectiveness and reduced risk.

I also think that there isn’t an overabundance of new thinking from researchers overall, rather more complaining about lack of support. In my own experience, I have never seen a single creative approach that could provide, if successful, an increased capability-that would not find support within the industry. I have also found that industry by and large want Universities to be Universities, concentrate on the core educational and research responsibility, on fundamentals, to be aware of industry issues and to be responsive but not too responsive to industry needs.

[Bill]: I don’t think there is much time allowed. The reliance is upon people like yourself, and the students that you have.

There is also a certain bit of responsibility to the turning off of research, that’s the responsibility of the researchers. Even if researchers are actually working on relevant problems they are still looked upon suspiciously by operations. Operations have pressure, they need something done now, and for them a great thing a week from now is useless. On the other hand, researchers that either oversell, hiding assumptions and prerequisites, solve irrelevant and low priority, or convenient problems, and publishing useless but resume expanding papers, or try to masquerade technical service as research, also give support to short-sighted near term thinking that damages the development of relevant and differential capability.

[Bill]: Do you interact with the majors in terms of how you might change concepts of sampling in acquisition?

First we look at a new concept for intrinsic capability given perfect data conditions. Then we start to take away perfection to bring realism in. If it remains robust, what different kinds of acquisition would enhance effectiveness? Is it achievable, that is, does it have an added cost that makes it unrealistic, or is the added cost more than offset by increased effectiveness with increased reliability and reduced risk. We get involved in all aspects. We are dealing with all levels of the seismic experiment because these new methods put a higher bar on our expectations.

[Bill]: When you speak about multinationals, the majors, do they come directly to you with their problems?

We don’t see their data. How we figure out what to work on is, for example, Shell might say “we have a problem with deghosting ocean bottom pressure measurements”, so we check around to see if this is Shell’s problem, or is it a universal problem. We are not looking at people’s anecdotal problems or personal problems. It has to be global high priority problem for the industry. They don’t show us the data, that is, they might show us the data as an example of the problem, but they don’t give us the data. We provide code, but it’s research prototype code. We don’t provide production strength code; it’s research code that has been tested on field data. We don’t do tech service. A lot of universities are doing tech service, that’s generally a maltreatment of graduate students. If you have a code and you’re a professor, and some company wants to get their data processed, the faculty will use the graduate students as essentially processors. Processing data once is an education, but processing it routinely is not an education and has little or no research value. The company that comes to the university to have this done, can save money, graduate students are not in the top tax bracket, and further, the company can write it off as an educational expense, a tax write-off. You go to a contractor, you pay for that service. They do it to save money. The professor is a hero because he brings money in. The only victim is the student, because the student is not getting an education. Universities lose their way when they only measure success by number of papers published and how much money they’re bringing in. As professors we need to be vigilant to the role and responsibility of a university in our society.

[Satinder]: You worked for Arco for a long time. What prompted you to join the University of Houston?

I always wanted to be a professor; it was my original interest, maybe a bit naïve early on. Joining the University of Houston was a wonderful opportunity for me.

[Satinder]: You’ve given a number of talks on the research work that you’ve done, how different is it lecturing now as an SEG distinguished lecturer versus the normal lectures that you give?

I think the objective of the distinguished lecturer tour is to speak to the average SEG member, and that’s a challenge when the activity is very technical. If you really know what you’re doing you can explain it to an intelligent farmer, to quote someone with whom I once worked. If you understand the machinery there, there is a way of explaining what it is trying to do, without the math and the physics, just give some sense of why this new possibility is there. It’s a wonderful part of the tour; you get to see people you haven’t seen for years, meet new people, see wonderful places, and see places you haven’t seen at all. The difficult part is you are away from your family a long time, weeks at a time. What I’ve done at most universities and would have done here if there were more time is I give the DL talk, and then I have a separate talk which is more technical. I would like to return to Calgary just to do that.

[Satinder]: What are your other interests, apart from geophysics?

Family. I think my happiest moment is when my whole family, all four boys and my wife and I, are around the table together. One is in New York, two are at Texas A&M, one is at home; it gives me a good feeling. We like music, we like dancing, we like African and Brazilian music; we have drums in the house. When the music goes on, we all dance; I don’t know how to dance, I don’t want to know. To dance to steps is like painting by numbers.

We spend time outdoors, we like to run. If I think of where we are now, how amazingly fortunate we are, I’ve got a good job, good salary, healthy family, 30 years ago I never would have imagined my life having this positive turn. I’ve been very fortunate. Working on exciting problems with great people. Not too bad.

[Satinder]: In the next five years where do you think you’ll be going?

Although I enjoy being the director of the research program, it’s not as much fun as doing science. I’m not doing enough; I’m watching people doing more science around me than I’m doing. I’m going to be looking to hire a junior faculty who will be groomed quickly to take over that position, and I’ll go into the background to just work. When I do work, it’s a very disturbing and wondrous thing. You get so confused, I bite my nails. Everything gets all mixed up and you think you don’t understand anything. The only good thing is sometimes when it comes together, if it does, you have a better understanding, and that’s such a rush. You’re the first to see that thing, that’s such a wondrous thing. If you are really struggling because you are doing real research, you have sympathy with students who are struggling. There is no way you can feel they are stupid and don’t get the point, because you don’t get the point either. These people at universities who are taken with their own brilliance are people who stopped working, if they ever worked. When a student comes and says they don’t understand something, and you don’t understand what you are doing, you can say “I know it’s hard just keep trying”. You are not quick to say “stupid”. If you are so smart then why are you struggling? I struggled when I was in school. I had a very rough background; I was a leader in a Puerto Rican street gang in New York City. I worked very hard to make up for things; I was very fortunate I had a public education that allowed me to do that when I got my act together. It’s always been a struggle; I worked very hard in undergraduate, very hard in graduate, and very hard now. Nothing comes easy to me. So when I see students working hard and struggling, how could you not empathize?

[Satinder]: What advice would you give young people who are just entering their profession?

That’s a tough one. When I go and speak at universities on this tour, I tell them I don’t really have a crystal ball about what their livelihood, you know, oil, environment etc will be. It’s hard to know. The only thing I’m pretty sure of, if they study whatever they are studying in great depth that will pay a dividend. First off they’ll learn how you do that. The simplest thing is deep and difficult if you think hard enough. They can transfer that to other things. I think we should give them PhD’s in seismic physics, but show them how to solve problems that haven’t been solved. That’s a transferable thing. Don’t assume that they will be in the narrow place that we provide them, but make sure they understand that what we are doing exemplifies a process, rather than is the process.

[Satinder]: Thank you very much for giving us your time Art. It’s been a pleasure talking with you.

I appreciate it, thank you.