2001 WARK LECTURE

Reflections on the application of fundamental research to practical problems

presented by Dr Ken McCracken FAA FTSE
7 December 2001

In the early years of the 20th century Sir Ian Wark was one of the Australian scientists who proved that science could give Australia what we now call 'competitive advantage'. His work in the refining of zinc, and of others like de Bavay, and Hooke, led to the concept that industrial science was important. The public and governments took note. I feel particularly honoured that the Academy has awarded me with the medal that commemorates Sir Ian’s contribution to Australian society.

This award has personal significance to me in other ways. When I matriculated in 1949 I was too young to go to university, so I worked for a year as the 'laboratory boy' in the research department of the Electrolytic Zinc Works, in Risdon, Tasmania. Sir Ian’s work was the basis of a great part of the processes at the Zinc Works, and I gained a very clear understanding that the work of a good leader of scientists can result in economic wealth and employment. I learned of 'Wark’s law' that prescribed the manner in which Zn is deposited in an electrolytic cell. To my young mind, scientific laws were all named after people who were well and truly dead – eg, Newton, Boyle and Maxwell. That an important scientific law had been discovered by a contemporary Australian made a strong impact on a timid 16-year-old.

The ethos of that research laboratory gave me an entirely new perspective on science. I learnt many important lessons that were of immense use in my career in NASA, CSIRO, and elsewhere. And the timid 16-year-old even managed to make a significant impact upon the Zinc Works.

Showing perhaps some precocious leaning towards my later life in space research, I built a rocket in my spare time. The great day came. The launch facility was made from the construction material of last resort – zinc ingots. It was located in a derelict factory building looking out on the Derwent River. The building had been used for about 20 years to process the fine, brown zinc concentrate, and every horizontal surface was covered with centimetres of fine dust. Computations show that there were tons of the stuff on the roof girders.

The wick was lit. We stepped back 5 metres for safety. There was an enormous explosion. A 25-kilogram zinc ingot landed at my feet. Then 2 seconds later a great choking cloud of Zn concentrate fell on us. A great cloud of the stuff rolled out of the end of the building and down the hill towards the Derwent. The fire brigade was there within minutes. All work on the production line stopped for 30 minutes.

There were two remarkable outcomes of this event. First, I was not, I repeat, not fired on the spot. Second, and more remarkably, absolutely nothing was said to me about it by my boss, or anyone else in management. It seems that the view was 'boys will be boys'. It made me ponder as to what my superiors had done in their youth.

Twenty years later I was employed by CSIRO to establish a new division. My first office was in Port Melbourne, just a short distance from that of Sir Ian Wark. I got to know him, and admired his quiet dignity and interest in the science going on around him. He was an excellent model of how the 'senior scientist' can assist the young, and I was privileged to learn that skill from him.

Looking back on the 50 years since those days as a laboratory boy, I believe that a great deal of my success has been due to the fact that I have chosen to work in two very different fields of science. One was quite fundamental, the other highly applied. One field is a branch of solar physics, as part of which I designed and built seven instruments that were flown on NASA satellites. The other field is geophysics as applied to the discovery of buried ore bodies. My work in each field then fed my work in the other, and this continues today.

To illustrate this symbiotic relationship between fundamental and applied science, let me briefly describe three research programs I have been involved in that have led to worldwide commercial applications.

First, however, a small recollection. In the late 1960s (goaded by the mis-application of science in the 1960s nickel boom) CSIRO decided to set up a division to conduct research into mineral exploration geophysics. Victor Burgmann, the physicist member of the CSIRO Executive, said 'let's find a space scientist who can use the new space technologies to that end'. Hence my appointment. Apart from my year at the Zinc Works, I knew nothing about the mineral industry.

Starting in 1970, two other space research colleagues and I developed technology to detect deeply buried ore bodies. We used an electromagnetic technique (that saw its genesis in my work from the 1960s) on the properties of the solar wind that blows away from the sun. It was conceptually quite different from the previous technology. It was widely scorned at first by the experts in the exploration community. Furthermore, it was totally dependent upon a computer chip – a form of technology that was still five years in the future when we started the design in 1970. I knew of its promise from space exploration – the concept was unheard of in the wider scientific community.

SIROTEM, as our new technique was called, went on to be the most commonly used exploration instrument of its kind in the world. I am completely certain that it was our prior experience in space exploration that led to its being developed and used so successfully in Australia.

About the same time, some other colleagues and I started working on 'remote sensing'. Aerial photography had been used by the mining and mapping industries for 40 years, and there was an almost universal view that images taken from 800 kilometres above the Earth would be useless compared to them. The experts had their own name for our activities – 'remote non-sensing'. Having built satellites, taught optics to the toughest bunch of students in the world at MIT, and with a knowledge of inertial navigation and signal processing, it was clear to me that the satellite images would get much, much better. In addition, my physics told me that our critics had failed to understand the major limitation of aerial photography, which is totally eliminated using satellite images. These days satellite and other remote sensing is a key technology worldwide, and Australian industries and the Australian environment have benefited greatly from our pioneering research in Australia.

In 1990 I received a phone call from one of my colleagues. He asked whether I would like to assist BHP in the development of an airborne system to map the Earth’s gravity to an unprecedented accuracy and spatial resolution. I replied that I didn’t know anything about measuring gravity. The reply to that was, 'That’s why we want you to help us'.

That was the start of what became known as Project Falcon. A worldwide search located a technology invented at the cost of US$400m for use by the US Navy, who then decided they didn’t want to use it. It was offered to petroleum and mineral companies worldwide. They all took off like startled rabbits. They decided that it was seriously flawed, and that it could never become a practical exploration technology.

My BHP colleagues and I were not so certain about that. We thought that by using the US technology in a different manner, we might improve its accuracy 100-fold. Our backgrounds in space science and engineering let us see the promise none of the 'experts' could see. Project Falcon was certainly very difficult, and BHP only succeeded because it assembled a team of the highest quality in signal processing, digital electronics, applied mathematics, legal expertise, and above all, project management. Note in particular that none of the BHP team had ever built a gravity measuring instrument, but they understood the needs of the explorer. That was probably the major factor in our success – we understood the need at the most detailed level, and we carried no technological baggage.

The first two of these examples of applied research have contributed to many major mineral discoveries. They have given Australian explorers a competitive edge in a business in which there are no second prizes. The third technology has only been in practical use for two years, and already it has made important discoveries. The commercial value of the mines discovered using these three technologies is in the many billions of dollars, and it will continue to grow with time.

In my 'spare time', I have continued my studies of the physics of the sun, and the manner in which the solar wind undergoes a supersonic shock when it runs into the interstellar medium far, far beyond the orbit of Pluto; and the symbiotic relationship continues. I am finding that the science and techniques I learned in the mining industry have allowed me to unravel aspects of solar physics that have long defied understanding. That is leading me into that very controversial area – why the Earth is suffering 'global warming'. Will this fundamental research lead me to another area of applied science?

So, with that background, let me make some comments upon the state of science and applied science in Australia.

There is an unreal belief among economists, politicians and the media that applied science is easy. That it is just a matter of some magical thing they call 'focus'; that the scientists in their 'sheltered workshops' just need a dose of 'modern management'. You know, as occurred in One-Tel, HIH Insurance, and so on – whip the troops, turn the thumb screws, and all manner of commercial benefits will flow. As a cow farmer, and scientist, I think I am qualified to say that’s bull.

Each of the three innovations I have described took at least 10 years to reach commercial viability. Extremely talented people did the work, and each project started from a high level of science and technology – they were far from cold starts.

Each project went through truly horrible times – nothing would work. Mega million dollar failures were staring us in the face, but persistence, and in each case, a management that gave us the space and time to sort it out, delivered exceptional outcomes.

These days I am used as a visitor, and in the 2- and 5-year reviews of a number of CRCs. I am extremely supportive of the CRC concept – it has many excellent attributes that will shape the research community in Australia far into the future. It often results in research organisations with the same attributes that led to the three successes outlined above. However I have three concerns.

Firstly, I assure you that the existing concept that all CRCs should be self-supporting after 14 years will preclude most of them from making the types of advances my colleagues and I made. They will 'mine' their existing intellectual capital, and will often have insufficient time or resources to replace it. Of course a few will be self supporting in the short term, but they will be the exceptions, and their cash flow may dwindle as their intellectual capital is used up. There is a vital need to provide continuation of federal funding for the fundamental research component in the best CRCs. Then they will be able to replenish their intellectual capital, and to capture technology from strange places as my colleagues and I were able to do.

Secondly, the taxation deductions for R&D in Australia are totally inadequate. It can take 10 years or more to deliver real competitive advantage through the research. Remember, the risk of technical and commercial failure are both high. The current levels of deduction are derisory in view of those stark truths.

Thirdly, I believe that the size of many CRCs is sub-critical, and that they are often too tightly focused for truly innovative R&D. They are certainly able to perform incremental research, however, their staff selection criteria and research management goals mitigate against the lateral thinking and cross-fertilisation that is the key to real innovation.

Thus, I have great doubt that someone like me would be hired by one of the modern, highly-focused research organisations that are now the vogue in Australia. Each time I was hired to do things in Australia it was precisely because I didn’t know much about the technical task in question. As the modern saying goes, 'I was not carrying any baggage'. I don’t think I would even make it to interview these days.

Science has repeatedly given Australian industry 'competitive advantage'. In the mining industry I give the examples of the work of Wark himself, Alan Walsh and atomic absorption, John Watt and stream analysis, and the three technologies I have spoken of tonight. In all six cases the research was performed by someone who was outside the industry, and the research was not focused in the modern manner.

The research model that led to all of them no longer exists – some would say it has been discredited. I disagree, and will watch with interest to see the extent to which the new model produces 'step function' advances as in the six cases just mentioned. The new CRC model is certainly good, but it can and must be improved. Let us learn from the history of the successes of the past to further enhance the probability of successes in the future. In so doing, we will continue the tradition set by Sir Ian Wark, and others, in the 19th and early 20th centuries.