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Priestley Medalist George M. Whitesides' address
LET ME BEGIN with two
opinions.
First, I have never known a time
when chemistry had better opportunities or more important research to work on.
Chemistry is now the natural home of many of the most engaging problems in
fundamental science and of the problems in applied science about which society
cares the most. The Priestley Medal is a lifetime achievement award. Our present
moment has become so interesting, however, that I wish my lifetime were
unachieved and that I were starting over.
Adam Siegel/Whitesides Group
Tiny Pathways By
injecting molten solder into a microfluidic channel and then cooling, it's
possible to make metallic microstructures flexible enough to tie in a knot.
Second, the past is not a
good predictor of the future. What we know now, and how we work now, will not
provide sufficient means to solve these new problems. Chemistry has had a
wonderful 50 years, but new types of problems require new approaches: It is
unlikely that the disciplines that were the favorites of the past—the ones with
which I grew up—will remain the most important in the future. I believe that we
will see major changes—in fact, revolutions—in what chemistry does, and in our
view of what chemistry is, as we move on to these new problems.
WHY AM I HERE? In the second week after I arrived at
Massachusetts Institute of Technology in 1963, I was stopped in the hall by a
small man, a complete stranger, with burning eyes. He grabbed me by my shirt,
shook me, and said, "You are working on it, aren't you?" Confused, I said, "What
is 'it'? And forgive me, but who are you?" He sputtered back: "It? It's the only
problem worth working on in chemistry. It's the norbornyl cation problem!" He
never did tell me his name. (He was Gardner Swain, one of the founders of
physical organic chemistry.)
At that time, I
barely knew what "it" was, and I certainly wasn't working on it. (And in fact, I
never did.) So how, if I missed the only important problem of the time, did I
get here? How did I redeem myself? Some of you may be wondering, and it's only
fair for me to try to answer the question. I will be brief in
answering.
Many scientists and I
share the weakness that we neglect history. For me, "science past"
(specifically, my own past) is history, and much less interesting than "science
future" (the future belonging to those of you who are young), and particularly
so in a time of change. But before elaborating, let me emphasize that it is not
only "I" who am here receiving this honor; it is "we"-the research group. I'm
the poster child for our group.
We—the
group and I—have, I hope, contributed to chemistry in two ways: one scientific
and one social. First, scientifically, we have tried to start things,
particularly in areas of science that were not familiar parts of chemistry at
the time that we (and others) worked on them. Some caught on; others did not.
Some babies are more winning than others.
Among the more winning
ones were dynamic nuclear magnetic resonance (NMR) spectroscopy, the
organometallic chemistry of copper(I) and platinum(II), enzymes as catalysts in
organic synthesis, self-assembly, surface chemistry and self-assembled
monolayers, "materials-by-design" in the guise of wettable surfaces, soft
lithography, microfluidics, microtools for cell biology, and polyvalency in drug
design.
We also worked on other
areas that either did not catch on or, more optimistically, have not yet caught
on. Among these are thiolate-disulfide interchange in biochemistry,
heterogeneous reaction mechanisms of formation of Grignard reagents and of
surface organometallic compounds, protein charge ladders, protein-ligand
binding, complexity and emergence, and using first-world science for problems in
the developing world. It has been great fun. We have, fundamentally, studied
mechanisms and made tools.
The second
area in which we have experimented is social—the organization of the group. As a
matter of necessity in working on problems that require a wide range of skills,
especially in their earliest stages, when we are trying to figure out which way
is up, we have evolved a structure for our group that is unusual for chemistry,
but it works.
We are a large group,
usually about 45 graduate students and postdoctoral fellows, drawn from a wide
variety of disciplinary backgrounds, including many that are not considered to
be "chemistry." All the work in the group is done collaboratively; no one works
in isolation, which is neither much fun nor very productive.
Whitesides
Group
Cell Blocks On a
gold surface painted with tiny geometric patterns of self-assembling
alkanethiols, cow cells can adhere and grow into decidedly nonbiological
shapes.
I do not "manage" the group in any
usual sense of the word. The group is too big for that, and the people in it are
too smart and too independent to take direction gracefully. I'm certainly a part
of the enterprise, but it is more accurate to say that I work for the group,
rather than that the group works for me.
And how do we choose
problems, and how do we recruit members of the group? We choose problems for
many reasons: for curiosity, because they might be important, because there is
money available to work on them, because we think collaborating with someone to
work on them might be fun.
I'll give one example in the
"curiosity" category. In winter, when I lean down to kiss my wife, she
instinctively avoids me, giggling. The reason she does so is that the spark that
comes from tribocharging in New England winters hurts when it goes from lip to
lip: Chapped lips, combined with 30 kV/cm, catches the attention, especially
when often repeated.
This kind of spark is
interesting. It also connects to other questions: Where does lightning come
from? How about the spark between the fingertip and the doorknob after you have
walked across the rug? How does a Van de Graaff generator work? A Xerox machine?
What causes your hair to stand on end when you comb it? (Not that I would know.)
The observation of a curious process that is ubiquitous and—it turns out—not at
all understood, provides the basis for an interesting research problem: contact
electrification.
And the people in our
group? They just come. We have a reputation for welcoming many different types,
and as a result, we get applications from many different types, including—for
this problem of contact electrification—people who understand Maxwell's
equations, polymers, and physical organic chemistry. It seems to work out
without too much planning.
THE
STRUCTURE OF SCIENTIFIC REVOLUTIONS. I have said that I believe and hope that
chemistry is on the verge of a revolution. I subscribe to two theories of
revolution. The first, supported by Freeman Dyson, Peter Gallison, and others,
emphasizes the role of new experimental techniques in enabling scientific
revolutions. In short, this theory holds that new keys open new doors. The role
of scanning tunneling microscopy in nucleating nanoscience is a current example;
so are the contribution of the polymerase chain reaction (PCR) to molecular
genetics, the contribution of organic synthesis to drug development, and of NMR
spectroscopy to organic synthesis. Computers are all-purpose tools that have
changed everything.
The
second theory of scientific revolutions that I find compelling was famously
articulated by Thomas Kuhn. It argues (to simplify a complex story) that
scientific revolutions occur only when there is no way out; that is, when a
field concedes, usually reluctantly, that its current theories are simply
incompatible with its own experimental evidence. The development of quantum
mechanics in the early 1900s was an example; so was the discovery of oxygen
about 200 years ago by Joseph Priestley.
"The Structure of Scientific
Revolutions" is the title of Thomas Kuhn's most famous book, and it has many
lessons for chemistry. Kuhn suggests that activity in science has two principal
forms: so-called normal science, which develops an existing and accepted idea or
scientific paradigm, and discovery, which is the basis of a fundamental change
in thinking; that is, a revolution.
Normal science is
focused on the solution of what Kuhn calls puzzles. These are classes of
problems in which (again to simplify) the answer is already known before the
work starts, in which the answer is not important, and in which the interest
lies entirely or largely in the elegance of the solution. Sudoku puzzles provide
a familiar example; chiral europium shift reagents (to take an example from the
shadows of my childhood) is another.
By
contrast, discovery or revolution is focused on much larger scale questions in
which the answer does matter, in which the strategy to a solution is not known,
and in which it is not even known that there is a solution. The "nature of
sentience" might be such a question; so is "best strategies for global
stewardship."
Courtesy of Felice Frankel
Template Writ Small A
square centimeter of this light-cured, molded microfabric of plastic hosts 3
million bridgelike connections between features as thin as 1 µm.
The scientific community
tends to think that discovery is a more exalted activity than normal science.
Kuhn makes the point—I think quite correctly—that both are essential and that
normal science is required to select, albeit idiosyncratically, specific
scientific puzzles for the intense cultivation that makes clear the fundamental
limitations of science and that occasionally leads to a fundamental
reconsideration of its tenets, that is, to scientific revolution.
OPPORTUNITIES. So, why do I
think that chemistry might now be teetering on the threshold of a revolution?
There are four reasons: First, as a field, we now have—in my view and,
interestingly, in the view of many outside of chemistry—the intellectual
responsibility for solving some of the most interesting problems in science and
technology.
Second, we now have, after
an exceptionally productive period of development, tools that should make
possible at least some of the types of research needed to address these
problems.
Third, for this big work,
chemistry offers a fine balance of skills. We have a unique and useful synthetic
approach to science: When we are faced with a problem, we make something—a new
molecule or material or system—to solve it. We can also assimilate and
disentangle complex systems quantitatively, and we are accustomed to problems
with many moving parts.
Fourth, we are reasonably
certain that we cannot solve these problems knowing only what we now know. Among
the disciplines, chemistry is perhaps most suited to take on many of the
problems that need to be solved because we do better at digesting detail than
does physics, and we are better at quantitative analysis than is biology.
Let me give you
examples of the problems for which chemistry seems so promising for supplying
solutions. The list is, of course, personal, but it makes a point in which I
believe strongly: Nowhere is it written that chemists must work only on
molecules and materials; we can also take on ambitious problems, in Kuhn's sense
of the word.
The Cell and the Nature
of Life. I believe that understanding the cell is ultimately a question of
chemistry and that chemists are, in principle, best qualified to solve it. The
cell is a bag—a bag containing smaller bags and helpfully organizing
spaghetti—filled with a Jell-O of reacting chemicals and somehow able to
replicate itself. Yes, it is important to know the individual reactions that
make the cell what it is, but the bigger problem is understanding why life—the
cell—is dynamically stable as a strongly interconnected network of reactions,
organized in space and time in ways we do not grasp.
Although we presently have no
theory to explain this kind of system, understanding the kinetics of systems of
coupled reactions is the kind of thing that chemists and chemical engineers
are—in principle—uniquely qualified to do.
Energy, the Environment,
and Global Stewardship. The web of reactions that we must understand, if we are
to begin to understand the idea of sustainability—from oil field or coal mine to
refinery to automobile to atmosphere to ocean to mineral—is, remarkably, a
problem similar to that of understanding life: It requires predicting the
behavior. of a web of interacting chemical processes when you tug it at
different points.
J.
Christopher Love/Whitesides Group
Nuovo Egg-Making Place silica nanospheres on glass, puff
palladium onto them, liberate the coated beads from the glass, dissolve the
silica. The result: submicrometer-diameter metallic half-shells.
Here, again, there are
many questions of great but local interest. How does photosynthesis work, and
how can it be improved? What is the best way to sequester CO2? What is the most
cost-effective solar cell?
But the larger question
is that of understanding how it all connects. It is in understanding the
network, the complex system, where we need revolutionary ideas. If one changes
one part of the system—say, if the U.S. and China burn much more coal—then what
happens to other parts, for example, the temperature in Greenland, the global
rates of photosynthesis, and rainfall in Niger? At the moment, we do not know
how to find out, and we do not know how long we have to learn.
The Origin of Life. This problem is
one of the big ones in science. It begins to place life, and us, in the
universe. Most chemists believe, as do I, that life emerged spontaneously from
mixtures of molecules in the prebiotic Earth.
Courtesy of Felice
Frankel
Red
Cross Network Floating on liquid are macroscopic plastic pieces, chemically
treated so that the liquid wets their bottoms and edges and elicits a rapid,
regimenting restructuring.
How? I have no idea. Perhaps
it was by the spontaneous emergence of "simple" autocatalytic cycles and then by
their combination. On the basis of all the chemistry that I know, it seems to me
astonishingly improbable. The idea of an RNA world is a good hint, but it is so
far removed in its complexity from dilute solutions of mixtures of simple
molecules in a hot, reducing ocean under a high pressure of CO2 that I don't
know how to connect the two.
We need a really good new idea. That
idea would, of course, start us down the path toward systems that evolve
autonomously—a revolution indeed.
Molecular Recognition in
Water and the Design of Drugs. One of the most important contributions of
chemistry to society has been through medicine, through the design and synthesis
of drugs. The binding of a small molecule—a drug, ligand, substrate, or
transition state—to a protein is arguably the most fundamental molecular process
in biology.
When I first entered chemistry,
the idea of rational design of drugs, or more modestly and realistically, of
ligands, was an objective we all understood. It still is, and we have made
mostly a kind of negative progress over the intervening years. We do understand
better now than we did then what we don't understand and why the problem remains
so difficult, but we still cannot design ligands.
Our frustrations in this arena
highlight areas in which there are great opportunities for increasing our
fundamental understanding. How do reactants in any process, especially those in
molecular recognition, interact with solvent and especially with water? How
should we think about entropy? Why is water so extraordinary?
Catalysis. Almost
everything in chemistry is catalyzed. Refining petrochemicals, most of complex
synthesis, metabolism, hydration of CO2 in rock, photosynthesis, and uptake of
neurotransmitters—these are just a few examples among an endless list of
chemical processes for which catalysts are central. I am astonished at how
little we still understand about the fundamentals of catalysis and how difficult
it is for us to design new catalysts. This is another wonderful area that will
require something dramatically new!
Adam
Siegel/Whitesides Group
Wet Designs Largish water drops adhere to black,
hydrophilic stripes on a gold surface exposed to a vapor, while small ones form.
on the purple, more hydrophobic stripes.
The Molecular Basis of Sentience.
Memory, thought, and perception ultimately have molecular foundations. It is
certain that molecules and ions are only a part of the story, just as
transistors and electrical currents are only a part of the World Wide Web. But
to understand sentience, we ultimately must try to connect thought to the
simplest components of the brain—to such things as acetylcholine, potassium
ions, proteins, and water—and tell a story that extends from them to "The
Well-Tempered Clavier." It is hard to find a problem that has more to do with
being human; it is also difficult, with our current way of doing business, to
understand where we should begin to take on this problem.
WHY SO SLOW? Over the
course of my career, chemistry has been happy to assemble an ever-more-useful
toolbox—better analytical devices, better synthetic methods, better fibers—and
has been spectacularly good at doing so. But we tend to build the wrench, not
the car. The developments of new organic reactions and of the tactics of complex
organic synthesis, for example, are beautiful to us, but they're important to
society for what they make possible, namely, the synthesis of drugs and other
molecules that solve problems.
Mass spectroscopy is
important, not because it generates a tsunami of data, but because it gives the
isotope ratios that write a historical record of the global temperature.
Electrochemistry is not just ions and electrons and molecules; it is the basis
for batteries and fuel cells.
We now
have at least some of the tools needed to take on these bigger, more ambitious
problems, among the nature of life and understanding climate and the
environment. But so far, chemistry has only slowly begun to sidle up to them.
Why are we so slow? Kuhn has a number of comments on this subject. I quote only
one, and I find it quite comforting because it suggests that we are not so
different from other fields.
Kuhn says: "No part of the
aim of normal science is to call forth new sorts of phenomena; indeed, those
that will not fit the box are often not seen at all. Nor do scientists normally
aim to invent new theories, and they are often intolerant of those invented by
others."
I suggest that chemistry now has
five issues to deal with if it is to move to the exploration of fundamentally
new territories.
What We Know and What We
Don't. We don't know as much as we believe we do. As we begin to think about
ambitious problems, we find that our current theories—of complex, tightly
coupled kinetic networks; of protein-ligand binding; of catalysis; of
dissipative, out-of-equilibrium systems; of liquids and solutions; of
noncovalent interactions; of entropy; and so on—simply do not work. In some
cases, we have ideas why our theories fall short; in others, we don't.
Peer Review. The peer review
system, especially in a time of financial drought, is between conservative and
Luddite. It filters out all the bad ideas, most of the new good ones, and all of
the really unusual ones. There is, of course, an alternative to this
"intolerance" for new ideas, to use Kuhn's term: If chemistry wishes to welcome
new ideas, the peer review system can express that wish.
Capitalism. The current pressures
on publicly traded companies to maximize financial return to stockholders in the
short term are now so intense that it is difficult for these companies—some of
them historically great centers of innovation and fundamental research and, not
incidentally, of jobs in chemistry—to do more than product development.
David Gracias/Whitesides
Group
Make Thyself
On this penny sits a dozen wire- and LED- riddled truncated octahedrons, which
self-assembled, making conductive connections that let current reach the
lights.
There is again, perhaps, a
solution to this problem, and one that has worked spectacularly well in
biomedicine to transfer fundamental academic research into successful commercial
technology: to use start-ups. If a large company is not interested in your new
idea, start your own baby company! Chemistry can learn to do so as well as
biology; it could also help students who want to be entrepreneurs by teaching
them something about how to go about it.
Teaching and Textbooks.
What we teach is often based more on the convenience of what is available in
textbooks than on consideration of what students should learn. What's more,
textbooks are designed to maximize sales, not to prepare students for research
in new and undefined fields. Again, it is for us to choose what we teach. We are
free to ignore the textbooks and to introduce material that prepares students
for new problems. We can also use the Web to trade good ideas for free.
The Academic Social System. We ought to become more
welcoming to new faces. Chemistry needs smart young people, even if—especially
if!—they come from less familiar backgrounds than ours and bring unexpected
points of view.
We might
also consider our undergraduates, whom we tend to treat as little colleagues and
encourage them to create their own curricula. They do so, but with a sensible
eye to minimizing the workload and seldom by volunteering to take the most
demanding subjects. They might benefit-as might chemistry and society-if we
asked them to do more. It is not a criticism of students to say that they may
have to be coerced into working; after all, we write proposals because we have
to, not because we want to.
Finally, we might wonder at our
inconsistency in thinking of graduate students, who are certainly more advanced
than undergraduates, as inexperienced beginners who can learn best by working on
our ideas. We might instead consider that they are younger, smarter, less
bureaucratically encumbered, and more energetic versions of ourselves, and best
able to learn by working on questions that turn them on, even if we might not be
able to answer them or even understand them!
CODA. We are at a wonderful time for
chemistry. It is, I believe, in the position of physics in the 1910s, just
before quantum mechanics made the world impossibly strange, or biology in the
1950s, just before the double helix obliterated the old biology.
Of course, chance and opportunity
favor the prepared mind. And there is a tempo to revolutions. Miss the timing,
and it is you who are up against the wall. Science and society will take on
these big questions and others. Chemists are the natural leaders for much of the
research that needs to be done. But physicists can learn molecular detail, and
biologists can learn differential equations. If we do not wish to work on these
problems, others certainly do. If it is not our revolution, it will be someone
else's.
My colleagues and I are deeply
honored by this award.
from C&ENews March 26, 2007
Volume 85, Number 13 pp. 12-17
==========================
贴个中文的供参考
化学的变革
首先在美国化学会的CEN杂志看到了白边（GM
whitesides）先生的这篇文章，虽然并不是专门讲科研方法，但是字里行间都充满了先生对化学，对科学，对革命创新的理解。本准备自己在假期翻译出来，但是google了一下，台湾的一个学者已经把这篇文章翻译成繁体中文，我稍加整理，贴在自己刚刚开通的博客，特别感谢白边先生和台湾的同仁。另外白边先生在2007年美国ACS化学年会的一篇访谈录（ACS
Nano, 1(2), 73–78, 2007），我们实验室正在翻译，感兴趣的朋友可以留意，过段时间我会发上来。
原文链接http://pubs.acs.org/cen/coverstory/85/8513cover1.html
这是哈佛大学的化学家George M.
Whitesides领取今年(2007)美国化学学会最重要的一个奖章即普利斯特理奖章(Priestley
Medal)时，所给的演讲讲稿。Whitesides教授是一个公认极具有前瞻性的科学家，让我们从这篇文章来看看化学正站在什么样的关键点。
让我先表达两点意见，首先我不知道有任何一个时代具有比现在更好的机会以及更重要的研究课题，化学现在已经很自然的成为基础科学里众多吸引人的问题之中心，同时也是应用科学里社会最关心的问题之焦点。我所得到的普利斯特理奖章(Priestley
Medal)是一个终身成就奖，然而当下却是一个极为有趣的时候，这使得我甚至希望自己毫无成就而可以重新来过一遍！
其次的，过去发生的事并无法对未来做准确的预测，我们现在所知道的以及现在正用来研究的方法，是无法提供我们上述那些新问题的答案。化学已经拥有了美妙的五十年，但是新型态的问题需要新的处理方法，那些我随着长大的时代中热门的领域是不可能在未来仍保持它们的优势的。我相信当我们朝着那些新问题去努力时，对于化学能做些什么以及化学是什么，将会看到重要的改变，或应称之为革命。
我为什么在这里？当我在1963年到达麻省理工学院开始工作的第二个星期，在走廊上被一个瘦小的男子拦下，那是一个目光如炬的陌生人，他抓着我的衬衫并摇着我说：你正在研究〝它〞对吧？，我极度的困惑，我说：〝它〞是什么？，很抱歉，你又是谁？他气急败坏的说：〝它〞？它是化学里唯一值得研究的东西，它就是降樟基阳离子(norbornyl
cation)的问题！他并未告诉我他的名字。(他是Gardner Swain，一位物理有机化学的始祖)
在那个时候我不太了解〝它〞，而且很明显的我也不在做这方面的研究(实际上我从未做过这方面的研究)。你们或许会问，那么为什么我错过了当时唯一值得研究的课题而却能站在这里呢？我又是如何挽救自己的呢？我想让我自己来回答这个问题是最公平的了，我会尽量简短的说明。
许多科学家和我一样都具有忽略历史的缺点，对我而言〝过去的科学〞(专指我的过去)就是历史，它比较不像〝未来的科学〞那么有趣(未来是属于年轻人的)，尤其是在一个变动特别大的时代里。不过在我详细说明之前，我要强调这并不仅仅是〝我〞站在这里接受这项荣誉，应该说是〝我们〞：整个研究团队，我仅仅是那个站在壁报前代表整个研究团队的人。
我以为我们(整个研究团队和我)在化学上有两种型态的贡献，一种是科学的而另一种是社会的。首先，在科学上，那些在当时我们以及其他的人所工作的方向中，尤其是在一些化学里大家不是很熟悉的部份，我们企图去开创一些事情，有些方向成为流行，也有一些方向不能，某些宝贝较一些其它的更受人注意。
在那些较受人注目的其中之一就是核磁共振(NMR)光谱、一价铜与二价铂的有机金属化学、酶在有机合成上的运用、自组装(self-assembly)、表面化学与自组装的单层膜、为可湿性表面(wettable
surfaces)所设计的材料、软刻蚀(soft lithography) 、微流体(microfluidics)
、细胞生物学所应用的微型工具，以及以多价理论(polyvalency)来设计药物。
我们也曾经有些工作没有成为流行，或者乐观的说，尚未成为流行，这其中包括了硫基阴离子与双硫键的交换(thiolate-disulfide
interchange)相关之生物化学，生成格林钠试剂(Grignard reagent)的非均相反应机制，蛋白质的电荷梯(charge
ladders)，蛋白质与配体的结合，特异错综性与出现(complexity and
emergence)，以及运用先进国家的科学来解决开发中国家的问题。这些研究让我们得到很大的快乐，基本上我们研究了许多反应的机制并开发了许多的工具。
另外一个我们实验过的领域就是在社会的层次：我们研究团队的组织。由于我们所工作的领域需要各种型态的技术，尤其是在早期的阶段，因应这样的需求，当我们想要找出正确的方向时，我们逐步发展出一种在化学界少见的团队结构，不论如何这是一个成功的组合。
我们是一个很大的团队，通常包括四十五个研究生和博士后研究员，他们来自于各种不同的专业背景，包括一些甚至于不能称作〝化学〞的领域，团队中所有的工作都是以合作的方式完成，这并不是非常有趣的做法，也不是很有成效的。
我并不是以一种寻常我们所理解的字面意义来〝管理〞这个团队，这个团队实在太大了，它的成员也太聪明以及独立，以至于不易接受指挥。我当然是这个企业的成员，但正确的说我是为这个团队而工作，而非这个团队为我工作。那么我们如何挑选题目以及招募团队的适当人选呢？我们选择问题有许多理由：因为好奇心；因为它们可能很重要；因为我们有足够的钱去研究；因为我们觉得与某人合作可能很有趣。
我将提供一个与〝好奇心〞有关的例子。在冬天的时候当我矮下身去亲吻我的太太时，她总会本能的笑着躲开，原因是新英格兰乾燥的冬天产生的静电在嘴唇之间造成的火花是很痛的：特别是当它发生在乾裂的嘴唇上时，再加上30
kV/cm的电压，这使得人们要很小心，尤其是它会不断重复。
这种形式的火花是很有趣的，它也与其它的一些问题相关：闪电是怎么来的？当你走过地毯开门时在你的手指和门把之间产生的火花又如何？范德格拉夫起电机(译註：指大家熟悉的静电球)是如何运作的？影印机又如何？当你梳头时头髮为何站立？
(我原本也不知道原因。)你常会发现一些常见但很奇怪的现象，结果它的原因并非我们全然了解的，这就提供了我们一个有趣的研究课题：摩擦起电(contact
electrification)。
而那些加入我们团队的人呢？他们就这样来了。我们有一种欢迎各种不同背景的人的声誉，结果是我们常接到具有不同背景的人申请加入，包括了(针对摩擦起电的问题)懂得马克斯威尔方程式(Maxwell’s
equation；译註：指与电磁波有关的方程式)的人，懂得聚合物的人，以及懂得物理有机化学的人。
科学革命的结构。我刚说过我相信并希望化学正处在一个革命的边缘，我认同两种革命的理论，第一个是由佛瑞曼?戴森(Freeman
Dyson)，彼得?盖里森(Peter
Galison)以及其他的一些人所支持的理论，强调新的实验技术的角色，使得科学革命成为可能。简言之，这个理论主张新的钥匙开启新的大门；扫描隧道(scanning
tunneling microscopy)成就了纳米科学，即为一最新的例证；又如聚合酶链反应(polymerase chain
reaction)对分子基因学的影响，有机合成之于药物发展，以及核磁共振仪之于有机合成。电脑则是一项多功能的工具，改变了所有的东西。
另一个令我信服的科学革命的理论是来自于汤玛斯?孔恩(Thomas
Kuhn)著名的论述，这个理论主张(在此将复杂的故事简化)科学革命会发生在找不到出路的时刻，这经常是当一个领域很不情愿的承认他们现行的理论完全无法解释一些实验现象的时候；在1900年代初期量子力学的发展即为一例；200年前普利斯特理发现氧气亦是如此。
“科学革命的结构”是孔恩所写过的一本最著名的书，里面含有许多与化学相关的教训。
孔恩指出科学活动包括两种型态：一种是所谓「正规的科学」，它是依循着已经存在并被接受的想法或是科学的教条而发展；另一种则是「发现」，它则是思想的根本产生变革的基础，换言之就是一种革命。
正规的科学之焦点是集中在提出一些孔恩称为「迷团」的解答，这包括了各种型态的问题(再度简言之)，其解答在工作开始之前就已知晓，其实解答并不重要，而其中的趣味最主要的或大部份的是来自于如何漂亮的得出解答。数独拼图游戏(Sudoku
puzzles)就是一个熟悉的例子；手性的铕偏移试剂(chiral europium shift
reagents)是另一个从我年轻时代的影子中抓出来的例子。
相对的，发现或者革命则是将焦点集中在一些规模较大的问题上，而这些问题的解答是很重要的，但求得其答案的策略是未知的，甚至于根本不知道解答是否存在。例如“情感的本质”就是这样的问题；又如“全球管理(global
stewardship)的最佳策略”。
科学的族群倾向于认为「发现」是比「正规的科学」更为崇高的活动，我认为孔恩非常正确的指出二者是同等的重要，而「正规的科学」乃是需要以独特的方式去选择一些特定的科学谜团，并勤加耕耘以理清科学的根本极限，那么偶尔的会导致对一些基本教条的重新考虑，也就是说，科学的革命。
机会.那么为什么我认为化学正摇荡在革命的门槛边缘呢？有四个原因，首先，作为一个领域，我以及有趣的也包括在这个领域之外的许多人都认为，我们现在具有一个知识责任来解开一些在科学以及科技上最重要的课题。
第二，在一段极度具有成效的发展之后，对处理至少上述的某些课题时，我们现在已经拥有一些工具使得其研究成为可能。
第三，对这个重要的工作，化学家可提供许多技术的精密协调，我们拥有一个独特而且有用的合成方法去解决科学问题：当我们面对一个问题时，我们会制造一些东西：一个新的分子、材料或体系，来解开它。我们也可以用定量的方式去消化并分解复杂的体系，我们也习惯于处理一些具有活动部份的问题。
第四，我们也相当的确定以现在我们的知识是无法解决这些课题的。在各个不同的领域中，化学可能是最适宜去处理许多的这些课题，因为我们比物理学家更专精于整理细节，而我们也比生物学家精于定量分析。
让我给大家几个例子有关于化学家对于一些课题似乎很有希望能提出解答，我所将列举的当然是非常个人的看法，但是它提供了我坚信的一个观点：没有任何规范限制化学家只能处理分子和材料的问题；以孔恩的语汇来说，我们也可以去面对那些极具有挑战性的问题。让我给大家几个例子有关于化学家对于一些课题似乎很有希望能提出解答，我所将列举的当然是非常个人的看法，但是它提供了我坚信的一个观点：没有任何规范限制化学家只能处理分子和材料的问题；以孔恩的语汇来说，我们也可以去面对那些极具有挑战性的问题。
细胞与生命的本质
我相信要了解细胞终究会是一个化学的问题，而化学家理论上是最有资格去解决它的。细胞是一个袋子：一个内含一些小袋子以及有效组织起来的义大利麵条，填满了果冻般的化学反应物质，还可透过某种方式复制自己。是的，去了解细胞中进行的每一个反应是很重要，但是更重要的问题是去了解为什么生命
— 细胞 — 一个以紧密互相关联的化学反应网路，用一种在动态上稳定的型态存在于时间及空间中，会组成这样一个我们所无法理解的型式。
虽然现在我们没有理论能解释这样的体系，但是去了解相关联的反应体系的动力学，理论上正是那种化学与化工学家最最有资格去做的事。
能量、环境与全球管理
如果我们要开始去了解永续的想法，那么就必须了解整个化学反应的网路
— 从油田或煤矿到精炼到汽车到大气到海洋到矿物质 —
这与去了解生命是极为相似的问题：它需要去预测一个相互作用的化学步骤之网路，在不同的位置受到牵扯的时候的行为。
在此，再一度的，有许多重要但却是局部的问题。例如光合作用到底是怎么一回事，可否将它改进？有什么最好的方法去捕捉二氧化碳？什么是最有成本效益的太阳能电池？
但是更大的问题是在它们如何的相关联，也正是在了解这个网路也就是这个复杂的体系的方面，我们需要革命性的想法。如果我们改变了这个系统的某一个部份，譬如说美国以及中国大陆燃烧了更多的煤，那么其它的部份会发生什么事，例如冰岛的温度，全球光合作用的速度，以及尼日的雨量？现在我们不知道如何解答，我们也不知道需要花多久去了解。
生命的源头
这个问题是科学里最大的几个问题之一，它将生命，以及我们，放置于宇宙中。大部份的化学家和我相信，生命是前生命状态的地球上从一堆化学分子的混合物中自发而生的。
如何发生？我毫无概念，或许是由于一些自发性产生的自我催化体系以及之后相互的结合而造成。基于我所知道的所有化学，这似乎对我而言是极端的不可能。一个核醣核酸(RNA)的世界之想法是一个不错的暗示，但是它的结构实在太复杂，这对一个在高温、还原性的海洋以及高气压的二氧化碳状态下的一个简单分子所形成的稀溶液世界而言，使我不知如何将二者连贯在一起。
我们需要一个非常好的新想法，这个想法当然必须引领着我们从头步向一个会自动进化的体系：一个真正的革命。
水中的分子辨识以及药物的设计
一个化学对社会最重要的贡献就是透过医学，透过设计药物以及合成药物。一个小分子
— 一个药品、配体(ligand)、物质或过渡状态 — 与蛋白质的错合，可被视为是生物上最基础的分子作用。
当我刚开始进入化学的领域时，以一个理性的方式去设计药物，或更谨慎以及实在的称之为配体，是一个大家都了解的目标。现在仍然如此，但是在过去的这些年我们的进展是倒退的。我们比过去了解的更多，也知道为什么这问题这么复杂，但是我们仍然不知道如何的去设计配体。
在这个竞技场中我们所遭受的挫败，照亮了一些大有机会增进我们基础知识的领域。尤其在分子辨识方面，在各种步骤中反应物如何与溶剂尤其是水来作用？我们应该如何的思考熵(entropy)？为什么水如此特殊？
催化剂
几乎所有的化学都是被催化的，石油的精炼，大部份复杂的合成，代谢，石头内二氧化碳的水合，光合作用以及神经传导物质的生成，这些只不过是在一个无止尽的化学步骤的名单上取下的几个少数的例子，在其中催化剂处于枢纽的位置。我很惊讶的发现我们对催化剂所知是如何之少，而设计新的催化剂又是如何之难。这又是另一个需要一些全新的东西的美妙领域。
情感的分子基础
记忆、思想以及知觉终究应有分子的基础。非常确定的，分子与离子只是这个故事的一部份，就好像电晶体与电流只是网际网路的一部份而已。但是要去了解情感，我们最终需要去尝试将思想连结到脑子里的最简单元件
— 像是乙酰胆素(acetyl choline)，钾离子，蛋白质和水 —
从而说出一个故事并能延伸到〝巴哈的平均律〞。很难再找到一个比如何成就了人性更难的问题了，以我们现在的研究方法去做，也将同样的很难去知道要从何处去着手这个问题。
为何如此的缓慢？
在我的学术生涯中，化学一直是乐于去建立一些越来越有用的工具箱 — 更好的分析装置，更好的合成方法，更好的纤维 —
也一直是惊人的精于此术，但是我们倾向于制造扳手而不是车子。譬如说新的有机化学反应以及复杂的有机合成中的合成策略，虽然对我们来说是很美妙的，但是它们对于这个社会的重要性在于它们能成就什么，那就是去合成药物以及其它能解决问题的分子。
质谱是很重要的，并非因为它能产生巨量的数据，而是在于从同位素的比例可以得到这个世界温度变化的历史。电化学不仅仅是离子和电子和分子；它是电池和燃料电池的基础。
我们现在至少拥有一些工具来挑战那些在探究生命的本质以及了解气候与环境的议题中更大、更有野心的问题。但目前化学才刚开始缓慢的侧身而上，为何我们如此缓慢？孔恩对这个问题有好几个评论，让我引述其中之一，这个答案让我较为舒坦，因为我们与其它的领域没什么差别。
孔恩说：“正常科学的目标中并没有包括唤出新的现象；实际上，那些没有办法放入盒子里面的东西往往是看不见的。科学家通常也不会把发明新的理论当成他们的目标，同时他们也经常不能接受别人所提出的新理论。”
我觉得化学如果要去开拓在根本上崭新的领域，现在有五个议题需要去解决。
我们知道什么以及我们不知道什么
我们其实不像我们所自以为知道的那么多，当我们开始去思考那些很具有挑战性的问题时，就会发现现行的理论很简单的就是行不通，例如有关复杂且相互关联的动力学网路；有关蛋白质与配体之间的错合；有关分散的非平衡体系；有关液体及溶液；有关非共价键的作用力；有关熵；等等。在某些情况下我们知道理论为何会失败，但在其它的情况下我们是不知道的。
相互评审
相互评审的体系尤其是在一个财政紧缩的时代容易流于保守，它将过滤掉所有差劲的构想、大部份新而且好的构想以及所有真正很特殊的构想。好的点子在面对这种〝零容忍〞的情况下仍有替代的方法，用孔恩的措辞来说：如果希望化学能欢迎新的构想，相互评审的体系需要能表达这种想法。
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