Reuniting natural philosophy and scientific research

Abstract

Scientific research, at its best, involves innovation. My experience over the years is that not all innovations are greeted with the same enthusiasm. Mine have variously garnered initial outrage, widespread adoption, marginal interest, and indifference. This experience reminds me that science is a human endeavour and perhaps not as objective as we might have thought. This article is an attempt to show just how wonderfully human and artistically creative scientific innovation really is. Also, I hope it shows how an appreciation of the artful part of science can affect and enhance the way we do and express our work. The subject of philosophy once included natural philosophy which was the study of why nature works the way it does. Natural philosophy has morphed, over the years, into scientific research, now quite divorced from the liberal arts subject of philosophy. I recommend reconciliation.

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Introduction

It has been my good fortune to be involved in several innovative developments in science, specifically advances related to chemical analysis. In addition to the scientific observations underlying these works, I have also watched the processes involved in the creation of these developments, how they were affected by the characteristics of the people involved, the editorial progression in the publication of the innovations, and their acceptance by the analytical community. I have interpreted the invitation to give a Heritage Lecture as an invitation to look at not just the science I have been part of, but some of the more human and philosophical factors involved. Having done so, it seems to me that having a broader view of what scientific research involves could enrich the work of scientists at all stages in their career.

Like most of the people reading this page, I have a PhD, mine is in chemistry. In some ways it seems archaic that our doctorate degrees stand for Doctor of Philosophy. Except for an undergraduate course in philosophy, I have been essentially unschooled in the philosophical underpinnings of scientific research. I suspect this is pretty much the case for most of us. We got into science because of a curiosity about natural phenomena or perhaps an interest in technological development took hold somewhere along our path. When we got to doing science, with a college project then our PhD thesis, we were guided by senior students and, most particularly by our mentor. We learned to do science the way he or she approached it. Thus, while learning from the behaviour patterns of a successful practitioner, the underlying philosophy of the research goals and methods may not have been brought up very often if at all. Since there are a variety of styles and practices in the mentoring of science graduate students and postdocs, there will be a wide range of approaches to teaching and research. Though I did not take a postdoctoral position, I now see that one of the great advantages of having one is the opportunity to be exposed to at least one other style of approaching scientific research.

Over the years, I became aware of the fact that there is substantial literature relating to the philosophy of science and scientific research. Of course most of us knew of Kuhn's The Structure of Scientific Revolutions¹ in which he categorizes paradigm creators and paradigm fillers. Perhaps my first serious encounter was with C.P. Snow's The Two Cultures and the Scientific Revolution.² However, the book that showed me that a deeper understanding of what science was about could affect how I went about it was Pirsig's Zen and the Art of Motorcycle Maintenance.³ I studied this book in the late 1970's, even involving my research group, considering what he had to say about manuals, gumption traps, theories, and quality. The success of Pirsig's book stimulated several others in that genre, including Hofstadter's Gödel, Escher, Bach, the Eternal Golden Braid.⁴

Perhaps the most eye-opening part of my exploration into this literature was the part where Pirsig quotes Henri Poincaré, the French mathematician, theoretical physicist, engineer, and a philosopher of science, as saying, “If a phenomenon admits of a complete mechanical explanation it will admit of an infinity of others which will account equally well for all the peculiarities disclosed by experiment.” I believe what he was saying was that the finding of a satisfactory explanation for a given set of observations proves the observations to be logically consistent. If that is so, a variety of formalisms could be used to satisfactorily express the observed relationship(s). We will not find an infinite number because we are limited by the formalisms in language and mathematics we have available. However, there have been enough examples of multiple, competing explanations in the past to support the development of Occam's razor as a means to choose among them. In any case, consideration of the non-uniqueness of any explanation (theory) has affected my approach to science ever since and has evolved into some further ideas which I share with you in this paper.

My research and scientific parochialism

The triple quadrupole mass spectrometer

My early work was in electroanalytical chemistry and did not challenge any accepted theories about charge-transfer at electrodes. It was when I wanted to build a computer-controlled analytical instrument that would perform separation and identification under real-time intelligent control that I had my first experience with what I will call scientific parochialism. Rick Yost and I conceived of using a quadrupole mass analyser to perform separation in real time, but then another quadrupole to identify the separated species. For that to work, we needed a way to fragment the selected ions between the two analysers. Our NSF proposal to build such an instrument was soundly denounced for its impossibility and our lack of credentials in mass spectrometry. The Office of Naval Research (ONR) liked the distributed microprocessor controller part of the proposal and gave us a modest grant. Our discovery that the very fragmentation we needed was happening in the tandem quadrupole instrument that Jim Morrison had built to study ion photo-fragmentation of ions was the breakthrough. With Morrison as a co-author, we submitted the first product ion spectra to JACS.⁵ One of the referees wrote a scathing review. Collisional fragmentation of ions at such low kinetic energies was believed have an efficiency of essentially zero, so, from his standpoint, the results were impossible. Fortunately, the support of the other reviewer and a lengthy rebuttal won the day with the editor. Don Hunt and Graham Cooks were quick to see the analytical value of the triple quadrupole and began significant expansions on this concept.

As McLuckey and Cooks subsequently proved,⁶ the reason that low-energy collisional fragmentation did not work in the tandem sector mass spectrometers is that the scattering angle required for sufficient momentum transfer took the product ions off the pathway into the second analyser. The earlier and wrong explanation for the observed fall-off in fragmentation efficiency with collision energy discouraged the people exploring tandem MS from using quadrupole analysers. Arthur Koestler, in The Act of Creation,⁷ asserts that much of scientific creation comes from an individual connecting two concepts previously not considered to be related. That could have happened with the development of low-energy collisional fragmentation of ions since people studying ion-molecule reactions with ion beams had certainly observed ion fragmentation at low energy. However, their interests (and literature) did not overlap those of the people studying fragmentation reactions in sector mass spectrometers. Thus, low-energy fragmentation in an analytical mass spectrometer came about by serendipity instead.

I believe the analytical tandem quadrupole would have been developed eventually but it would have had to overcome the dual barriers of preconceived notions of the fragmentation process and the convincing of grant review panels. The interest of ONR in the computer control system and our interaction with Jim Morrison were serendipitous events which worked out and happily brought me into the field of mass spectrometry.

Electrospray ionization

I was better prepared for the initial reaction to my first work in electrospray ionization (ESI). Again, there was a well-established group working on the fundamental aspects of the process but I was not one of them. One of my students wanted to use ESI-MS to study the formation constant of some Ag⁺ crown complexes. The complex/Ag⁺ response ratios he was getting did not make any sense. Something appeared to result in huge differences in response factors among ions in ESI. Based on my experience with electroanalytical chemistry, specifically the dropping mercury electrode, I imagined a partitioning of surface-active ions between the droplet surface and interior as an explanation.⁸ This is probably a good example of Koestler's confluence of two previously unconnected concepts.

I do not think my equilibrium partition theory paper would have made it into Analytical Chemistry over the strenuous objections of one reviewer and the lukewarm reception of the other if I had not, by that time, developed some credibility in mass spectrometry. Now, the “EPT” theory is widely accepted having been cited 228 times to date and been supported by a variety of additional experiments. Is this now the “correct” explanation? Not if you believe Poincaré, which I do. EPT is a picture that works for us, with an accepted formalism readily understood by most quantitative analysis students. But it is not complete and it is not the real thing. A good way to think of a theory is that it is a metaphor for the actual process. So there must be others that would work now and still more that will accommodate data which EPT eventually will not. We should not be surprised by this; we should expect and welcome it; we should work to make it happen.

Distance-of-flight mass spectrometry

A totally different kind of process accompanied the development of the fledgling concept of distance-of-flight mass spectrometry. In this case, I had to do battle with my own preconceived notions. I did not start out with the concept of distance-of-flight as a means of separating ion masses. I was trying to conceive a way to perform scanless tandem mass spectrometry (MS/MS) so that the complete precursor m/z vs. product m/z map could be produced for each batch of ions extracted from the ion source. If the precursor ions were fragmented collectively, the product ions would have to carry some information about their precursor m/z so they could be correctly assigned. Using a spontaneous method of fragmentation such as high energy collision, electron capture, or photo-fragmentation, the velocity of the product ions would remain essentially that of their precursors. After fragmentation, the product ions would have positions along the flight axis dependent on their precursor m/z. Product ion m/z could then be obtained by orthogonal TOF with the flight time giving the product m/z and the detected position along the original flight axis, the precursor m/z. I presented this concept at the 2003 ASMS meeting in Montreal.⁹ It took me a while to realize that inherent in this simultaneous MS/MS instrument was a new kind of mass analysis, distance-of-flight (DOF), which was used to provide the precursor m/z information. When initial attempts to prototype the whole MS/MS instrument ran out of time and funds, I saw that it would be necessary to first develop DOF MS on its own.

The techniques that brought TOF MS to a mass resolution which now rivals double-focusing sector mass spectrometers are widely appreciated. They are necessary because ions in the acceleration region do not all start from the same position, with the same initial energy, or even with the same direction of motion. Modern instruments employ high-field ion extraction from an orthogonal ion beam to minimize the effects of initial energy dispersion and an ion mirror to correct for the ion energy differences created by different starting positions in the extraction region. Without these focusing methods, TOF MS with gaseous ion sources has mass resolutions in the low hundreds.

DOF MS has the same focus needs, but a necessarily different solution. Instead of focusing isomass ions at the constant flight distance and different flight times, it must focus isomass ions at the same time at their respective flight distances. It was not obvious to me how this would be accomplished. I began by modelling ion flight times and distances using Visual Basic in Excel. For more than a year, I explored a variety of geometries and acceleration techniques and waveforms. The principal obstacle was unlearning “rules” adopted from ion optics in TOF MS instruments. When I finally found the answer, it was both simple and remarkable.^10,11 It was simple because it used the previously known but little used constant momentum method of ion acceleration and an ion mirror. It was remarkable in that the focus achieved was for the initial energy and direction, not for the initial spatial dispersion. Thus it was exactly complementary to the focusing method for TOF MS.

There was no resistance to publication of the DOF MS focusing study. It did not challenge any preconceived theories. However, I did not anticipate the lack of interest in the instrument companies in exploiting these new focusing properties and the compatibility with array detection. I now know that it is because it potentially replaces existing products without offering advantages commensurate with the cost of development. Further development in an academic laboratory would be required before commercial adoption. Since I was retiring and no longer had a lab or funding, it was extremely fortunate that Gary Hieftje at Indiana University was interested in DOF MS as a platform in which to apply the array detector he had been working on with Bonner Denton at University of Arizona and David Koppenaal at PNNL.¹² Thus, in 2009, Gary, David, and I began a collaboration which has resulted in a proof-of-principle atomic DOF MS instrument^13,14 and several innovations involving constant momentum acceleration in TOF MS. These efforts and successes now coming out of the Hieftje laboratory, with PNNL and NSF support, make it more likely that DOF MS will find a significant place in the lexicon of mass analysers and analytical techniques.

The theory of complex mixtures

It seemed to me that a clear advantage of DOF MS lay in the tremendous dynamic range and ion through-put capacity that could be achieved using an array detector with independently auto-ranging elements. An unanswered question was just how much dynamic range is needed and what would be accomplished by having more. The application in greatest need of dynamic range in a single run is the comprehensive GC-MS or LC-MS analysis of complex mixtures. When the MS is operating as a chromatographic detector, the ion detector integration time is short and fixed. There will be hundreds (thousands?) of detectable components and they will be detected as sub-mixtures within heavily overlapped chromatographic peaks.

A quantitative determination of what increased dynamic range could reveal in such analyses requires a knowledge of the distribution of the concentrations (or responses) of components in natural complex mixtures. It had been widely assumed that this distribution was exponential,¹⁵ with the number of components in a given concentration range increasing exponentially as the concentration decreased. However, this distribution had not been verified, and when Nagels studied a chromatographic data set, the exponential model did not produce a satisfactory fit.¹⁶ I began working with the data in the Nagels paper and communicating with Luc Nagels on how the data were obtained and treated. This began a Skype relationship which culminated in a paper¹⁷ that suggests that natural mixtures may have a log-normal (LN) distribution of concentrations. The LN distribution was statistically verified for a variety of mixtures to a high degree of accuracy. In addition, the fraction of responses from the components predicted to lie below the detection limit matched the observed “chemical noise” level in the cases where those data were available.

In this work, a break from statistical methodology was required in order to create an LN fit without knowing how many total components were present. Had I been more highly trained in statistics, I do not think I could have found the relationship which makes it possible to estimate the number of components below the detection limit. From a fit to the LN distribution, it is possible to predict what fraction of components will be observed for any given detection limit and dynamic range. At this point, the response of the analytical community to the usefulness of a “science of complex mixtures” has not been publicly expressed. Time will tell. I believe this approach has much to tell us about mixtures and the methods we use to characterize them.

Conclusions

Looking back over these developments which all involved looking at a scientific problem in various new ways, I have found and list below, some points that are in common and which can help us understand better how new science is created.

Science is a human endeavour, beset by the wonders and foibles of all other human activities. It springs, in large part, from our need to understand why things happen the way they do (curiosity) and from a desire to reduce uncertainty and pain (put knowledge to use). What is not always appreciated is that scientific research is a creative activity, putting observation into useful expression, developing theories, devising new experiments to test and revise the theories, and so on in an endless cycle.

Writing and speaking are essential parts of doing science effectively. One's accomplishments and discoveries cannot be understood, expanded, or implemented without effective communication of the results. This is all the more critical as no one is able to take in more than a few percent of the papers and presentations that might be relevant to her research. Grabbing the attention of the reader/viewer and making the point succinctly and clearly is the main goal. If the paper is about something people have not thought about (such as the concentration distribution of components in a mixture) or have thought about in a different way (such as the equilibrium partition theory of electrospray ionization), one has a special teaching job to do, prizing people from their old patterns to follow the new approach. This will almost certainly take more than one talk or paper to achieve.

Scientific research is not often thought of as a creative activity. We tend to think that nature's secrets are waiting to be discovered and whoever searches for them will find the same thing. If scientific findings are true, that must be so, right? Not entirely. Certainly what we observe must be reproducible by others and the correlations we demonstrate (such as the relationship between ESI response factor and surface activity) should be reliably applicable. However, we don't stop there. We wonder why these relationships are true and we imagine models and pictures and processes that could explain the observed relationship. The dance between devising experiments, developing theories, proving relationships is highly individual as to method, medium, and result.

A major part of scientific research is the testing of existing theories and the development of new ones. Surviving tests of predicted behaviour strengthens a theory and makes it more useful, but it does not prove it correct. Because of this, we should embrace the possibility of new and better explanations, not resist them. Further, it would be better if we did not try to claim any theory as ultimate truth to the public or to each other. The test of a good theory is the degree of its usefulness, not its truth.

I have often thought that as a chemistry professor in research universities, I spent the lion's share of my time doing things for which I had no formal training. I took no courses in education, group management, scientific writing, public speaking, or accounting. And yet my colleagues and I were expected to design and present courses, lead research groups, and in effect run small business enterprises in support of the graduate program of our institutions. At least, I thought, I was trained to do research. But it would really be better to say that I was exposed to a way in which research can be accomplished. None of my mentors introduced me to the literature of the broader methodology or philosophy of scientific research. Now that I have been, to some degree, I am struck by the separation between those who practice science and those who study the way science is practised. This has worked to a remarkable degree, but perhaps not optimally. Is it too late, I wonder, to consider exposing our future graduate students to a bit more of the “Ph” part of their degrees.

Notes and references

1. T. S. Kuhn, The Structure of Scientific Revolutions, University of Chicago Press, Chicago, 1962.
2. C. P. Snow, The Two Cultures and the Scientific Revolution, University Press, Cambridge Eng, 1959.
3. R. M. Pirsig, Zen and the Art of Motorcycle Maintenance: an Inquiry into Values, Morrow, New York, 1974.
4. D. R. Hofstadter, Gödel, Escher, Bach: an Eternal Golden Braid, Basic Books, New York, 1979.
5. R. A. Yost and C. G. Enke, J. Am. Chem. Soc., 1978, 100, 2274–2275,  DOI:10.1021/ja00475a072.
6. S. A. McLuckey and R. G. Cooks, Int. J. Mass Spectrom. Ion Phys., 1983, 423–426.
7. A. Koestler, The Act of Creation, Macmillan, New York, 1964.
8. C. G. Enke, Anal. Chem., 1997, 69, 4885–4893.
9. C. G. Enke, ASMS, Montreal, Canada, 2003.
10. C. G. Enke and G. S. Dobson, Anal. Chem. (Washington, DC, U. S.), 2007, 79, 8650–8661.
11. L. Cassiday, Anal. Chem., 2007, 79, 8830.
12. J. A. Felton, G. D. Schilling, S. J. Ray, R. P. Sperline, M. B. Denton, C. J. Barinaga, D. W. Koppenaal and G. M. Hieftje, J. Anal. At. Spectrom., 2011, 26, 300–304,  10.1039/c0ja00087f.
13. A. W. Graham, S. J. Ray, C. G. Enke, C. J. Barinaga, D. W. Koppenaal and G. M. Hieftje, J. Am. Soc. Mass Spectrom., 2011, 22, 110–117.
14. A.W. Graham, S.J. Ray, C. G. Enke, J. A. Felton, C. J. Barinaga, D. W. Koppenaal and G. M. Hieftje, Anal. Chem., 2011, 83, 8552–8559.
15. A. Fellinger and M. C. Pietrogrande, Anal. Chem., 2001, 73, 618A–626A.
16. L. J. Nagels, W. L. Creten and P. M. Vanpeperstraete, Anal. Chem., 1983, 55, 216–220.
17. C. G. Enke and L. J. Nagels, Anal. Chem., 2011, 83, 2539–2546,  DOI:10.1021/ac102818a.

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