Harry Deckman

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ORAL HISTORIES

Interviewed by

David Zierler

Interview date

September 25, 2020

Location

Teleconference

See catalog record for this interview.

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Interview of Harry Deckman by David Zierler on 2020 September 25,
Niels Bohr Library & Archives, American Institute of Physics,
College Park, MD USA,
www.aip.org/history-programs/niels-bohr-library/oral-histories/46332

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Abstract

In this interview Harry Deckman, recently retired as Senior Scientific Advisor at ExxonMobil Corporate Strategic Research, explains the many research and consulting facets of this work, and the collaborations he has participated in over his career which has tracked with technical and geopolitical developments. Deckman emphasizes ExxonMobil’s commitment to research in non-petroleum energy sources in parallel with finding new oil and gas reserves. He discusses: his childhood outside of Cleveland; early interests in science and the excellent public school offerings he received; undergraduate education at Case Western where he focused on solid state physics; his decision to go to Iowa State for his PhD, where Constantine Stassis supervised his thesis research on magnetic neutron scattering; his initial appointment in Exxon’s Corporate Research Lab to work on laser fusion, the impetus of this research in light of the energy crisis of the 1970s, and the many experiments and collaborations in the Lab that mixed basic and applied science, including the demonstration that laser plasma could be a source for X-ray lithography; the rise of soft matter physics as a discrete subfield, and the impact of the information revolution in the 1980s on his research agenda and his focused interest in absorbed molecules and studying isotherms and transport; his work with novel reactors and coupled waves in geoscience, and why his work in carbon dioxide separations marked a major turning point in his career both as a fascinating area of research and because of the imperative at Exxon to address carbon emissions; his work on hydrocarbons and their value as an affordable energy source; his interests, in retirement, to continue searching for solutions for greenhouse gas mitigation strategies.

Zierler:

That's a regular day, or that's a productive day?

Deckman:

That's a regular day. Productive is if you want it by ten o'clock in the morning. So, we imaged a whole lot of samples at the time. We had a lot of materials work going on. At the lab Tom Tiedje had invented amorphous semiconductor superlattices and Theodore Moustakas was exploring a wide variety of other superlattice compositions. He was synthesizing gallium arsenide superlattices along with tungsten carbide metal lattice structures and diamond-like films. Later I will focus on the study of one of these materials that changed my life. One of my early Science articles was a study of molybdenum disulfide catalysts. Moly disulfide is a layered structure that with a promoter forms the basis for several hydrotreating catalysts. What we did was image catalytic sites. Layers exposed at the edge of the posts can be decorated with promoters and also converted to rag structures which are present in actual catalysts. So, it turns out it gave you very microscopic images of what happens at catalytic sights of one of the hydrotreating catalysts of the day. For the Science article we studied the structures, the catalytic activity, and the optical absorption, correlating the findings which became a cottage industry internally for a while.

Another big transition occurred with the vision of one of our directors, Peter Eisenberger. He had driven the lab to take a strong position in beamline science. He had the vision that you could use the synchrotron to create a new three dimensional X-ray microscopy technology; microtomography. At that time, there was no microtomography, period. It hadn't been done. When we started to look at that, it became obvious why. When you worked it out, for the desired resolution and the size of samples of interest, the data required would be equivalent to all the data collected in the hospitals in the United States when the acquisition was occurring. A little on the large size. Today, that would not be true. This is old school. If you used the existing Shepp-Logan algorithm to invert the data set, we estimated it would tie up our Cray supercomputer for two months. That was going to be a bit of a challenge, and that was if the data was good. It also required a detector with unprecedented resolution and data volumes. So, teeny tiny problems were in our way. So we divided and conquered. The algorithm was done by Brian Flannery. If you ever looked at Numerical Recipes in C, and look at the author list, you'll see a Flannery on it, that's Brian. He successfully made direct Fourier inversion work. This idea had been out there and had been tried by many others who failed to make it work. We knew it was going to be at least a thousand times faster than the Shepp-Logan algorithm, but lots of artifacts can contaminate the inverted volume. Let's not get into the whole story about how it was avoided.

Zierler:

What do you mean by artifacts?

It was compelling to me at the time. It suddenly opened a door to a bunch of areas I only tangentially knew about. There were people in the lab working on zeolites and molecular confinement effects were known to occur in them. With zeolites, you can synthesize well defined molecular channels with characteristic sizes ranging from ~3-10 angstroms. Typically zeolites are crystalline aluminosilicate networks with pores and cage sizes defined to fractions of an angstrom. You can make all kinds of architectures out of them. Exxon and ExxonMobil are famous for them in reality. There is a huge number of structures you can study that are going to have different molecular selectivity, diffusion, and equilibrium characteristics. So, I began to think about the type of selective molecular separations that would occur if we made a membrane out of them? Nobody had made a large area zeolite membrane at that point in time. The way we approached the synthesis of a zeolite membrane was with an adaptation of some of the microfabrication techniques we have discussed. We trapped a monolayer of them at the air water interface of a Langmuir-Blodgett trough, compressed them with surfactant, lifted them on a substrate coated with a release agent, spun coated a polyimide diffusion barrier on top, ion beam etched to expose the surface of the zeolites, released the film containing the zeolite monolayer surrounded by the diffusion barrier and studied transport. Again, we got lucky. We chose to microfabricate the membrane using a MFI zeolite, which has a pore size a little over 5.5 angstroms, and tried to separate two molecules that are chemically identical, para-xylene and ortho-xylene having molecular sizes of approximately 5.5 and 6.5 angstroms. One would expect that ortho xylene would be size excluded and have a lower diffusion coefficient compared to para-xylene. We got a ~2-fold separation factor. That excited us very much, and led us to start a much larger project trying to make zeolite membranes in a more industrially viable manner and have impact on the business.

Zierler:

What was the big promise here, Harry? What was exciting?

Deckman:

Well, what was exciting was that we thought we could change one of the major petrochemical processes in the world. You and I are wearing a product made from para-xylene; its polyester. At that time Exxon I think was the largest producer of para-xylene in the world. As we go forward there will be lots of these different vignettes and you can see which ones you want. This vignette is simply that with a lot of work, improvement and scale-up we might take a petrochemical process that had been put in place for quite a while, over 40 years, and completely improve it. The hope was we would reduce the capital required as well as the energy consumed. Early on we also did something that should be part of many research programs. What we did after we got the initial result and became excited we then said let's step back and take a look and see what this thing could be. To do that, we went about doing what I call "zero order economics." It's something I try to teach and may not do a very good job here, because I normally do a much longer version. I do think it's something that should be used in industrial settings, and also when you're trying to change the world in different ways. In particular when there's something that you're after, or if there's a tangible outcome, or it's something you think people should try to do. In the end, economics is usually going to determine what happens. I think it's something that most people are unfamiliar with. It's not taught in lots of curriculums. I had to learn it on the job. So, I think it's something physicists could stand to learn a little more about. You don't want to become an economist. You don't want to spend all your time doing this, but you want to know who and what you're about, if you can. So, my method is, first of all, dream the dream. Step one. You don't do that; you'll never get anywhere. Try to think what the best possible outcome is like. At this point I haven't done economics. But then put some realism in. Okay, now we have dreamed the dream, and it's time to put a bit of realism to it. The next step is to make the best physical model of the implementation that you can think of. What would it look like? All the bells and whistles, all the dirt, and the nasty things you normally don't want to think about. Put them in. You'd be surprised. You have to scrounge around to find costs, but you can find them from many places. They're available. Details become important. When you break it down, what are things going to cost? In the case, of xylene isomer separation it involved a process concept, a flowsheet, an estimation of the heat and material balance, along with a rough idea of equipment and energy required. Later we'll come back to other examples in which you can do this. One works out some crude estimate of economics and sees what this thing looks like. Does this look like an interesting idea? Does this move the needle in some way? Basically, if you like it, then try to go forward. If not, try to think of a new idea, or modify it. A lot of things I have done have passed this screening and entered development. As you go through development, you retest it many times. So, almost every research project aimed at a development should have iterations of zero order economics before a formal more detailed first order economic study is done. These are often called research guidance economics. So, I'll give you a proposition today. I just invented a 12% efficient solar cell. Congratulations. I just did it. Can I sell it, or do I have to pay someone to take it? You can answer that question. I know the answer to that question. I think you know what my answer is. The answer is you're going to have to pay someone to take it, because of the land and balance of systems cost when compared to economics for present day silicon solar cells. You can't even give it away, because silicon is that cheap and that good. That's where we are today. It isn't that you don't work on something that's less than 12%, efficiency because most organic semiconductors are less than 12%. I'm not saying you stop that. But you certainly want to be aware that you need improvements, or you have to find a niche market. You think about what else it could be. There are many examples. I picked on this one just for fun.

Returning to the zero-order economic analysis that we did to frame results of our initial experiments using a microfabricated membrane to separate para-xylene, we began with an analysis of the base case: i.e. how were the commercial plants configured to produce the valuable para-xylene isomer used to make polyester. Para-xylene plants in this era utilized molecular separation technologies to remove and purify para-xylene from a mixed xylene isomer / ethyl- benzene stream. The remaining ethyl-benzene was catalytically destroyed and the ortho and meta-xylene isomers were catalytically reisomerized to make more para-xylene. When you catalytically run an isomerization reaction, you can only convert ~20% of the ortho and meta xylene stream into para-xylene because of the equilibrium that produces the other isomers. Thermodynamics gets in your way. The xylenes plant basically isomerizes, separates, then goes back and re-isomerizes, separates, and keeps going until you consume all the otho and meta isomers and produce only the valuable para isomer. So, in the commercial process there is a big, big recycle. Once we studied the base case, our analysis showed that if we could combine separation with isomerization to overcome the equilibrium limit, we could really lower the capital cost, Opex costs and energy consumed. We might be able to make streams that have 30-70% para-xylene in them. That looked to be very attractive. To do that, you'd have to have a membrane that would operate a ten bar or higher, at a temperature of 250-350 centigrade. That told us what type of technology we had to develop. With our initial analysis we were able to convince our chemical company that this was worth the trip. Like everything, the first time out of the box, you have to start small and grow the idea. So, we launched a journey, and it was towards a targeted goal. Gradually this built into a big project. They understood this was high risk. They were willing to take on an extremely high-risk proposition where you had to create everything from scratch. The point was their economics came out like ours. The value proposition was there if we could do it. So, they were willing to back a multiyear effort with a goal to create a scalable defect free high temperature MFI zeolite membrane. A huge amount of material science work ensued with the development of all kinds of clever hydrothermal synthesis techniques and all kinds of inventions. I'm going to try to speed up because we're going to run out of time, so I'm going to skip a lot of stuff. I'm going to pick one of the inventions we made along the trip. A couple of things I'll highlight. One is in characterization. The earliest synthesis routes yielded membranes with a significant number of defects in them. So, you're not going to see the real or intrinsic performance, if you have a number of micron size holes or cracks. You see a lot of nonselective transport through micron holes or cracks in the membrane. We had to devise a way of figuring out what the defect flow was and correct our transport data for it. We invented a modality called perm porosimetry, where you use capillary condensation of a vapor introduced in a carrier stream to block helium transport, and watch the helium flow through the membrane decrease as the activity of the vapor is increased. As you continue to increase the activity of the vapor you move up the capillary condensation curve and block selective transport through the small zeolite pores. This isolates the contribution to the transport from large nonselective defects. Initially we used the Wicke-Kallenbach method to measure multi-component membrane transport. This method is commonly used by academics and introduces a vapor in the feed to a membrane using a carrier gas sent through a bubbler. Early screening studies had a mixture of xylene isomers in the bubbler, a nitrogen carrier gas, and a helium stream was used to sweep the vapor permeating through the membrane into a gas chromatograph. As we started to go to higher pressures and tested different carrier and sweep gasses we learned that the permeances were moving all over the map. Results depended upon what carrier gas was used and were anomalously sensitive to the transmembrane pressure. This shouldn't have happened. We eventually determined that this was due to a mutual diffusion effect. Diffusion is driven by a difference in chemical potential of gasses on opposite sides of the membrane. As gasses transmit across a membrane into a support, there will be a mutual diffusion effect that puts mass transfer resistances in the way. For high flux membranes the support mass transfer resistance can significantly alter the performance. So, my comment is there's a significant number of people who academically use this method without realizing the pitfalls that you get. You've got to be very careful. We published ways of mitigating this problem, as well as other tricks to accurately measure selective permeances for high flux membranes. As we moved down the development path, finally we did devise synthesis techniques that produced defect free membranes and got the performance we were hoping. The time and effort that it had taken to get to this point in the development was larger than anticipated at the beginning. We then began looking at the next step: scale-up and saw how big it would be and the resource commitment that would be needed. I think everybody agreed that it was about the right point to stop this effort.

There were several parallel membrane efforts we did at the time. I'll pick a couple of them and try and get through them fast. One involved the invention of a pressure drop membrane reactor. It came out of a PhD thesis for which I was a co-advisor. This was a simple idea. Take a sol gel, and cast it as a thin film on a porous support and a deposit palladium or platinum catalyst in the 50-100 angstrom pore structure in the inorganic thin film formed from the sol gel. At high temperature these catalysts would be expected to be able to dehydrogenate ethane to make ethylene, or propane to make propylene. Even at high temperature ethane and propane conversions are equilibrium limited with conversions increasing with decreasing pressure. You don't build catalytic reactors at one bar because of the required residence time and the volume they get to. You build them at high pressure. However with a nanoporous sol gel membrane you can have high flux with high pressure on one side and low pressure on the opposite face. The question becomes would the conversion of an ethane or propane feed be closer to the thermodynamic limit for the high pressure side or the low pressure side. We found and ultimately were able to model the result that the conversion comes close and could even exceed the conversion expected for the low pressure side. Exxon Chemicals spent a lot of time studying our results and performing research guidance economic calculations to determine if this reactor technology could displace the incumbent steam cracking technology. It came very close. It was a little bit better, but it wasn't advantaged enough because of all the development costs. The reason I chose to talk about this was the physics that came out of the PhD thesis that studied gas transport through sol gel membranes in great detail. One of the first studies in the thesis was high temperature pressure driven transport of single component non-reactive gasses through the 50-100 angstrom pore structure in the sol gel membranes. One would expect the transport would match a simple Knudsen diffusion model with the permeance scaling as the reciprocal of the square root of the molecular weight of the gas. That is what's supposed to occur. When we looked at it, we found that the scaling was close but it was definitely not right. Well, we were kind of excited by it, and finally made our own model, and came up with what we thought was the answer, it was basically that the molecules were inelastically colliding with the walls and hanging up for several picoseconds per collision. We were almost going to write it up, and then performed an extremely thorough literature search, and discovered that Langmuir had discovered this in the 1930s. It had just been forgotten. It's a small point in that you too can publish in the Physical Review, and be a Nobel laureate, and get yourself forgotten in all the textbooks. I kid you not, we could not find a textbook reference to it since the time it was published. Maybe it is there but we just couldn't find it. Another type of study examined multi-component transport through the support structure that has micron sized holes using a variation of the Wicke-Kallenbach method. We flowed an argon-oxygen mixture on one side, and nitrogen on the other side of the membrane. We were able to do an argon-oxygen separation with high selectivity with one micron pores! From a molecular perspective you could drive a truck through those micron sized pores. How did you get molecular selectivity through something like that? Well, we already were wise to the idea that this might be due to mutual diffusion effects. We went back and used the governing equations to confirm that this was indeed due to mutual diffusion. We named the effect atmolysis. Again, we decided we'd look through the old literature and once again found that this had been also discovered (back in the 1940s). Not the same separation, but close to it. A lot of history can be buried and often hard to find.

Another interesting thing we came up with was a surface catalyzed hydrogen spillover membrane. Kind of a simple structure. Take polyethylene, actually a garbage bag, coat it with a physical vapor deposited (PVD) platinum island catalyst film , and then cover them with a thin layer of silicon monoxide. So, what can you do with this structure? Well, our idea was to flow hydrogen on the polyethylene side and let it diffuse through the polyethylene to the platinum. We postulated the hydrogen would be expected to activate on the platinum catalyst and spillover through the silicon monoxide film to the outer surface where it would be able to drive a hydrogenation reaction. Hydrogen spillover physics from platinum catalysts to the surface of a support was something other scientists who had been in our lab were famous for. What was new was the hypothesis that the activated hydrogen would permeate through the silicon monoxide film as atomic hydrogen to the opposite side where it would be reactive enough to hydrogenate an olefin. In our initial tests using cyclohexane as the olefin we were able to hydrogenate it to cyclohexane. The question was; was somehow cyclohexane getting back to the platinum in a way that we didn't know? So, the next thing we did was to add thiophene to the cyclohexene feed. What's thiophene? Thiophene is a sulfur compound and is almost a quantitative poison for platinum killing the catalytic activity. The amount of thiophene we added would have killed more than 10⁶ to 10⁹ more catalytic sights than we had. I think we nuked it yet the hydrogenation went on. So, we were proud of that one. It was very interesting. We did not pursue this because here we did our own zero order economics, and we came up with the area needed. What we were getting was one reaction per platinum sight per second, which is not bad, but that's not fast enough when you had to scale this up as a membrane, not as a high surface area catalyst. Catalysts can have 100-1000 square meters of surface area per gram. As such a gram of catalyst can have 100-100 times as much catalytic activity as a square meter of a surface catalyzed membrane, so there was a little bit of mismatch.

Next thing I want to get to is some work we did with novel reactors. Today this would be called process intensification, but what we were doing was saying if we took things to physics limits: — really high temperatures and short resonance times. What could you do with a reactor that would dramatically shrink its footprint? Can you make really small compact reactors? What conversion could occur with short resonance times? Milliseconds or microseconds. We also wanted to do this on an industrial scale. So, we started with an idea. How could we do this?

Okay. I also have other sides to me, I know quite a bit of geoscience and have worked in geoscience areas within the corporation. This will be a story about something that we did not start whatsoever. It was an idea that came from Exxon’s Upstream Research Company and was proceeding into early field testing before we even got involved. It was called coupled waves. The idea behind coupled waves was to use electrokinetic coupling to convert an electromagnetic wave into a seismic wave. Kind of an interesting idea. The embodiment being tested placed long electrodes on the surface of the Earth to drive oscillating currents and hence electromagnetic waves deep into the ground. Electrokinetic coupling then produces a seismic wave that can propagate back to the surface of the Earth. With long duration data acquisition, data stacking to reduce noise, and advanced seismic processing the hope was that you could get an image of the resistivity in a reservoir with seismic resolution. Why do you care about a resistivity image? Because resistivity logging generally tells you if there's oil or water in the formation. So, you care about that. Full field scale tests were being done with electrodes that were hundreds to thousands of meters long that injected hundred kilowatts to several megawatts of a Golay sequence of current pulses. Looking at this process more microscopically current pulses flowed through the brine filled pore spaces of the rocks in the ground. They propagate as an electromagnetic wave from the surface where the current is injected. Locally in the pore space of the rock the electrokinetic coupling coefficient between the oscillating current and the brine in the pores causes the fluid (brine) to move. That's what electrokinetic coupling does. It basically says if I pass a current through a fluid in a porous medium, I can cause it to move. That's classical electrokinetics. The motion of the fluid couples to the rock matrix and launches a seismic wave. In more scientific terms this coupling of the fluid motion to the rock matrix is known as poro-elasticity or Biot theory. As such electrokinetics and poro-elasticity are responsible for the generation of the seismic wave at the surface. The amplitude of the returning seismic wave was expected to be very small, but possibly detectable. In the initial testing with targets as deep as ~1,000 feet it actually worked and imaged gas pockets. Pretty cool. There was one catch. They were getting surprisingly large signals, much larger than they were predicting. How'd that come about? They asked us to take a look at it and that is how we got involved. First thing we thought, well maybe the electrokinetic coupling coefficients of rocks was wrong because nobody had ever really studied electrokinetics of rocks. So, we got a lot of types of rocks, studied them, and we found some anomalies that weren't quite right compared to what people thought should happen, but they wouldn't explain what had occurred in the field. Thus far, we were empty. We then took on the hard problem which was to see in a laboratory setting the rock matrix motion due to poroelasticity. In the laboratory, with the low voltages that can be applied without generating gas or doing other things we expected rock matrix motions of ~10 femtometers. That’s 10 x 10 ^-15 meters or equivalently a few nuclear radii. To measure that, we applied a small AC voltage across a core sample and used a fancy AC fiberoptic interferometer to record the oscillatory motion on one rock face (i.e. the rock matrix motion). To get an acceptable signal to noise ratio we acquired data and signal averaged for several days and in some cases a week. We aren't going into all the technology that was used, but, lo and behold, we found a rock matrix motion of 10-100 times greater than expected. This looked very much like what was being reported from the field. The answer came from one of my collaborators, Eric Herbolzheimer who showed that this was due to the boundary conditions for fluid flow in and out of the sample. Examples of fluid flow boundary conditions are squirt flow where fluid flows out of the face of the rock or no squirt where fluid is sealed into the core and the fluid pressure can build up at the end of the core. The theory showed that if they're symmetric on all sides in most cases you will have very little response with only the momentum of the fluid coupling to generate a rock matrix response. However, with the right thicknesses and asymmetric boundary conditions, you get a pressure buildup at one side and a large response. We referred to this as a “breathing rock” effect. The idea that rocks could breathe was a very cool effect that explained both the lab and field data.

I want to start a transition, and it's a transition that takes us to many of my research efforts going on today. Around 2000, my research efforts start to become more and more focused on CO₂, particularly CO₂ separations.

My research on CO₂ capture was an evolutionary path. It starts with the problem of economically producing large high CO₂ content gas fields found throughout Southeast Asia. Often these offshore gas fields contain~70% CO₂. Our thought process involved answering the question: what could you do about this CO₂? The project we devised was aimed at separating CO₂ on an offshore platform as gas came out of the reservoir and re-injecting the separated CO₂. Conventionally, you can do it with cryogenic separation, but the kit is really big and is not practical in an offshore environment. People had looked at it for decades before we got involved, so we said, is there any new science or technology options that could enable this? We went about evaluating a variety of process concepts using advanced separation technologies, built screening models, and evaluated zero order economics. Eventually we settled on a concept built using fundamental data to predict how membranes that had for the most part never been synthesized would operate to separate CO₂ at high pressures. The models were built on molecular transport theory that predicted high pressure transport behavior of a membrane using a theoretical formulation that for the most part had not been discussed in the literature. Under high pressure conditions the loading in a membrane is well outside the Henry’s law limit. Most of the literature had addressed models of transport in the Henry's law limit, however industrially you're not in the Henry's law limit. A Henry’s law treatment of transport can be accurate at low pressure and a low loading limit of the adsorption isotherm. However a different treatment is needed for high pressure transport problems. We developed the needed treatment of high pressure membrane transport and used it to predict the selectivity and permeance of a variety of inorganic membranes from fundamental measurements of adsorption isotherms and transport diffusion coefficients. Our predictions were well above the upper bound limits for the tradeoff between selectivity and permeance that Robesen had illustrated for all kinds of existing polymer membranes. Plots put together by Robesen implied that there is a line bounding the tradeoff between selectivity and permeance. Our calculations said that a variety of inorganic membranes would cross the line by a whole bunch. It was enough to launch a high risk development project. The chances of it succeeding would not be great, but what you're after could be worth the trip. The Upstream Research Company agreed to it and handled it as a breakthrough project — a high risk high reward research / development project. Initially there were several challenges you had to get over. There were no gas separation membranes that had been made for high pressure operation. Several of the process concepts required operating pressures of 3000 PSI. Concomitantly no inorganic membrane had been tested under these extreme conditions. We started by synthesizing and exploring the transport through three different types of inorganic membranes: silica, carbon, zeolites. We gradually rejected two of the three. The amorphous silica was rejected because synthesis and transport studies had advanced to the point at which questions about fouling and degradation had to be addressed. We found out that hydroxyls that were present in the amorphous silica membranes led to irreversible degredation that couldn’t be stopped. So, we published a lot of papers around that. In collaboration with the Japanese ceramics company NGK, we settled on something that looked viable: high silica crystalline DDR membranes. Our choice of DDR was a result of a deep scientific understanding of the transport physics and the recognition of how it would offer an advantaged opportunity. DDR is a zeolite that is sometimes referred to as a clathrasil structure. We did a lot of work studying the hydrothermal synthesis of DDR as well as fundamental measurements to characterize adsorption isotherms and transport diffusion coefficients of DDR powders that were produced. Technology to synthesize DDR membranes was developed internally as well as with another company. Initially the DDR membranes had a lot of defects and defect flow had to be characterized and corrected for using several of the methods that I have mentioned. For high flux membranes corrections had to be made for mass transfer resistance in the hydrodynamic boundary layer on the feed side as well as that in the porous support on which they were synthesized. Ultimately the testing program showed that it was possible to make low defect density high flux DDR membranes enabling meaningful high pressure testing up to pressures around 3000 PSI. The testing results were in reasonable agreement with the model. There was a little deviation which we attribute to how the diffusion coefficient changed at high pressure but overall the agreement was impressive. They were pretty close to the commercial target we were looking at. The issue was that there was a significant scale up required, and at that point the company was making a lot of discoveries in natural gas that did not have the high amount of associated CO₂. They had lower development costs, so there was a commercial decision to stop the program, which is a legitimate call. We were a long ways off yet. We had gotten to the point of creating inorganic membrane technology in the lab that had never existed and whose performance tended to match our original models.

I would like to transition to another idea where we worked with Georgia Tech to take carbon capture head on. I will begin by trying to explain how this concept worked. It is one idea amongst a larger family of ideas to address CO₂ that I have been involved with.

Zierler:

Harry I want to ask also — again, this is your perspective. When you start to take on carbon capture head on, to what extent is this a compelling scientific program to work on, and to what extent is this really where the company is headed, and you're doing your part to get there?

Deckman:

I think it is both. To me, it's compelling from a dual challenge point of view, and from lots of points of view the company is quite literally taking on many challenges in carbon capture. In the research phase the lab has been exploring a wide variety of separation technologies ranging from various types of adsorption and absorption processes to electrochemical separations including fuel cells. I would like to focus on an idea that a gentleman named Ron Chance and myself collaboratively worked on with Bill Koros and Ryan Lively from Georgia Tech. Ron Chance and I had collaborated on the high pressure natural gas separations we discussed and for us the idea grew out of that work. I'll try to explain the idea and hopefully I can do it in a short fashion without a cartoon. It starts with the idea of a hollow fiber contactor that looks very much like a hollow fiber membrane module used for gas separations. The difference is that it is impermeable and one side contains an adsorbent that can remove CO₂ from a flowing gas stream.

As such the concept for the contactor was a bundle of impermeable 100-1000 micron diameter hollow fibers. In this configuration we can pass water or steam on one side, and flue gas on the other. Due to the impermeable wall the two don't contact each other. On the side where the flue gas will flow we required a coating of a selective high capacity CO₂ absorbent, such as a zeolite. There are many other adsorbent options and metal organic frameworks would be another. They weren't around when we were doing this, so we wouldn't have been able to use them. In use there is an absorption step in which a flue gas is passed on one side of the hollow fiber, where the absorbent loads up as it removes CO₂ from the flue gas. This adsorption step is stopped before an adsorption wave breaks through and deleteriously affects CO₂ capture efficiency. The adsorbed CO₂ is released by a temperature swing desorption in which you send pressurized hot water or steam, through the opposite side of the module, driving a thermal wave along the length of the fibers. As one end gets hot, it desorbs the CO₂, and basically it rolls an adsorption wave down the column. It pushes down the column, just like a chromatographic column, and you're going to roll it right out of the contactor. You're going to create a thermal wave that literally heat exchanges and moves down the fiber bundle. So, what you're doing while you're sending hot water or steam in one end, you're pushing cold water out the other end. When you have desorbed the CO₂ and pushed it out you can send a little bit of cold water into the front of the column, and can start the next absorption step at the cold end. You basically cycle this around. It's a cyclic temperature swing absorption process that in principle can capture CO₂ from flue gas. This idea was simultaneously arrived at by the Georgia Tech team and us (myself and Ron Chance). It could be because we were talking to each other. It could be that it was just the right time. We did however get together and collaboratively work on it. One of Bill Koros’s bright students, a gentleman named Ryan Lively, who's now a professor at Georgia Tech, took on the fabrication of this device. We kind of knew that it was a herculean effort, especially for a PhD thesis. Without even worrying about the chemical engineering aspects, this was an extreme material science challenge. But at the end, let's just say, credit to Ryan he made a prototype device.

It worked with dry flue gas. We knew we did not have an absorbent at that time that would work on wet flue gas. The only absorbents we had that we thought would work were basically not going to perform well in wet environments. Ryan did successfully demonstrate the whole idea with this limitation. What's happened over time is Georgia Tech has gone back and reworked on this. They've taken a derivative from this idea to the National Carbon Capture Center. Recently MOF adsorbent materials have advanced to the point that they might enable the use of this concept in wet flue gas and one of my colleagues is exploring this in a collaborative program. These are examples of discontinuous innovation.

Another discontinuous innovation story is the rebirth of the RONCO reactor concepts. A derivative of the RONCO reactors is currently being explored in the lab to make syngas for process concepts that have low carbon footprints. This rebirth is due to one of the original RONCO team members, Frank Herschkowitz and I am only a small contributor to it. Scientifically this rebirth is due to a combination of the understandings of high temperature short contact time chemistry processes coming from RONCO reactor studies married with a new physical understanding of thermal waves in swing adsorption processes. There are also new drivers; the importance of ways of mitigating CO₂ emissions and the possible role hydrogen may play in the energy mix in the future.

Yet another type of discontinuous innovation story involves a rebirth with a very significant modification of the original idea. As I mentioned, we had originally developed a DDR membrane to remove CO₂ from raw natural gas. We began thinking about rapid cycle swing adsorption processes and estimated how DDR would behave in a pressure swing adsorption process for bulk removal of CO₂ from raw natural gas. It looked like it had potential and we worked with our Upstream Research Company partnering to begin exploring this. The exploration led to a broad suite of ideas to take contaminants out of raw natural gas with all kinds of rapid swing adsorption cycles involving not only pressure swing, but also temperature swing, purged pressure swing cycles, and a variety of hybridizations of these. The team grew as we explored removal of different contaminants such as CO₂, H₂S, and water; different mechanical valve and hardware options; and potential pathways by which we might commercialize the suite of technologies being considered. Some advantages of this suite of technologies come from the fact that these ideas provide a significant process intensification; reducing space and weight footprint, and in many cases the CO₂ footprint. From a science perspective that does not fully credit engineering challenges, the essence of what's been going on has involved devising ways of finding molecularly selective fouling resistant absorbents and structures that have great mass transfer characteristics and incorporating them into cycles and marrying them with mechanical valves. It's involved quite a bit of experimental work and development because we have gone through a lot of candidate processes and gas purification targets over time. In particular this has involved synthesizing a large number of candidate adsorbents and making a large number of measurements to characterize their diffusion coefficients and their competitive adsorption isotherms. An advance in computational chemistry that happened during this development changed a significant fraction of the experimental workflow. One of my colleagues, Peter Ravikovitch has driven our application of this and has moved us to the point that for certain classes of absorbents, the computational chemistry is so accurate that we no longer have to measure equilibrium properties. We of course experimentally validated this approach with well characterized model systems before stopping work measuring equilibrium transport properties. In many cases the computational chemistry approach even provides a good model of kinetic behavior. For fouling behavior, you still do an experiment because you can't predict fouling. Nobody's gotten there yet, but you can do a lot of stuff. The other thing that changed during this development effort that I have a little role in, but others have carried much farther, is process simulations. Advances in the ability to simulate processes have taken us to the point that we now do model guided scale-up predicting how field scale demonstrations and commercial units will run. So, you start from fundamental isotherms, transport diffusion coefficients, mass transfer equations, and you can basically solve the complete differential equation set to predict how it's going to behave and scale up. That's a world of difference from where life has been we can now reliably do model guided scale-up. Right now, the company has formally announced the construction of a demonstration unit that is the culmination of the work. The announced unit is incorporated into a gas processing plant and is testing rigorous (sub ppm level) dehydration. I can also say without going farther that variants of these ideas are under consideration for flue gas capture.

Oh, it's my pleasure.