Hasok Chang. Is Water H2O? Evidence, Realism and Pluralism. 2012
Это работа по истории науки. Выполнена замечательно. Для рассказа об устройстве науки, ее истории и методологии автор выбрал очень красивый. но и очень трудный способ: работа с одним примером. Помните, была такая книга - "Аскарида"? Рихард Гольдшмидт. Введение в науку о жизни (аскарида). Вся биология рассмотрена на примере одного организма. И здесь тоже - все проблемы науки (ну, как все...) - на одном примере: установление формулы воды, что такое вода, в самом ли деле вода - Н2О?
Поэтому сначала - глава о научной революции в химии, Лавуазье и Пристли и вот это всё, и как там всё непросто, и насколько вынесенные другими "готовые уроки" из этой истории отличаются от реальности. Банальное "Пристли был неправ, а Лавуазье открыл истину" - это очень далекое от реальности описание. И вот - детали этой истории, научные лагеря, решение вопроса - и почему же мнение о победе Лавуазье и такой-то формуле воды победило и произошла научная революция? Ответ автора надо смотреть детально - там в его позиции важно каждое слово, потому что без подготовки его трудно сказать - неправильно поймут. Я скажу - потому что у меня не авторитетное исследование, а мнение в блоге. Так вот, там была победа по типу "моды" - то есть мнение ученых по вненаучным причинам быстро поменялось. И автор потом через всю книгу проводит нить - а если б не победил Лавуазье? Ведь это была ошибочная победа. А если бы химия развивалась с флогистоном? И мнение автора: теорию флогистона следует оживить, вновь принять, это до сих пор плодотворная точка зрения. (Классификационная проблема: отчего следует считать элементами водород и кислород, отчего не считать элементом воду? Проблема химических элементов - это классификационная проблема (и родилась она из старых алхимических практик "очищения веществ"). Если принять не-лавуазьерову классификацию, облик химии будет в теоретическом смысле совершенно иной - но вот кто б занялся переписыванием современных результатов на совсем другой теоретический язык. То, что в скобках - не от Чанга, это мое дополнение - говорю, чтобы автора не ругали за не его ошибки).
И тут другой ряд рассуждений. Множество людей легко рассуждают о самом известном примере научной ошибки - флогистоне. Явная, мол, чушь. Автор показывает, что это был отличный научный концепт. Что флогистонова химия очень многое сделала - для сегодняшней науки, а если б ее по ненаучным причинам не пришибли, она могла бы сделать больше.
И тут - штрих мастера. Вот в этом месте "могла б больше..." обычно останавливаются, но автор - профи, и он указывает: в современной науке есть мало известные ручейки, где окольным путем, с негодными средствами и трудно, но было сделано то. что легко и понятно было б сделать из флогистоновой химии. То есть прогресс-то поехал дальше, а дырка в познании, которая образовалась из-за победы атомизма и химии Лавуазье - очень медленно, но зарастает. да, это теперь трудно понять, да, это не осознается как продолжение флогистоновой химии - но оно есть.
И потом следующая глава - про атомизм в химии. Только в химии - играми физиков автор не занимается. Атомизм в химии - это закон Авогадро и озарение Дальтона, закон объемов: можно заметить, что вещества вступают в реакцию в определенных неизменных отношениях. И отсюда - идея: ба, да это ж оттого что атомы, это доказательство атомной теории. Вся эта штука открывается в электролизе воды: вот мы ее электролизиуем, и на одном электроде выделяется кислород, на другом водород. Это доказательство. Это доказательство? И автор показывает, что в химии XIX века это не было доказательством, имелось по меньшей мере пять разных теорий, почему имеют место такие-то феномены. показывает трудности ныне принятой точки зрения - отчего ее не принимали (как атомы перемещаются к одному или другому электроду?). И как электрохимия весь XIX век жила без истины - то есть не было господствующей точки зрения. И автор это параллелит к примеру с химической революцией. Вот с Лавуазье поторопились принять единую точку зрения - и сколько всего упустили. А электрохимики не торопились, не образовалось согласованной научной точки зрения, конкурирвоали пять гипотез-теорий - и хорошо получилось.
И как там дальше - три теории соединились (противоречиво и не очень логично) и победили другие две. Получилась нынешняя электрохимия - но там есть огрехи. Автор, опять же, это показывает - кто из ученых что думал, с кем соглашался и почему, а почему не соглашался с другими и какие там неприятности были - во многом сейчас забытые.
Ну и дальше он проходится по химическому атомизму, показывая дырки и - что во многих случаях верное решение принималось по неверным (вненаучным) причинам. А также показывает. что многое полагаемое бесспорным из других наук глядя - совсем не такое при внимательном профессиональном взгляде. Автор говорит: ну что, вот мы вязли модельныйпример банального высказывания, которое используется как истина 2х2, Н2О. И что, вода в самом деле такую формулу имеет? И показывает. что это неточный взгляд - с современной точки зрения вода не Н2О. Там речь о растворенных солях и изотопах, и еще кой о чем. То есть это такой концепт воды - модель воды во многих умах имеет такую формулу. А реальное вещество не такое. И мы уже знаем, какое оно - но истина "формула воды" все живет в рассуждениях тех, кто этим профессионально не занят. Можно искусственно создать вещество с такой формулой, но называть ли его водой - дело соглашения. Известные химические и физические свойства существенно зависят от присутствия различных ионов, а также от связей между соседними молекулами, которые противоречат формуле одной молекулы H2О. Если бы у нас была простая куча молекул H2O, ее нельзя было бы распознать как воду.
И дальше автор раскрывает свою научную позицию - он придумал "активный реализм", то есть плюрализм. Хорошо, когда нет единой истины, и в науке это тоже хорошо. Отличает от релятивизма. Тот пассивно сомневается во всем, а тут совсем другое - активное принятие и разработка сразу многих гипотез, возможность видеть недостатки и противоречия каждого взгляда.
Касаясь моего субъективного мнения: замечательно изложена фактура химии XVIII-XIX вв., подробная и ясная история химической революции и принятия атомизма. А вот философсие рассуждения автора насчет эпистемологии - не везде так хороши. Но он имеет право - после такого эмпирического исследования отчего же высказать точку зрения. с которой он на эти дела смотрит.
Это всё безумно наскоро, потому что книга скрупулезная и с деталями, ее не пересказать общими словами - я только намечаю линии, по которым у автора развернуты рассуждения. Там все в каждом случае очень непросто - разнообразие позиций химиков, их взаимоотношения, причины, по которым теория принимается или нет, недостатки ныне считающихся "прекрасными" объяснений. В целом книга свою задачу решает. На примере банальной истины научного знания показывает, что эта истина, строго говоря, неверна, мнения о том, как она получена - ложные, а среди противников этой научной истины были те, кто в то время при тех знаниях были, по сути, правы и истинно научны. А победили не они, и они во многом забыты, хотя кое-что (немногое, надо сказать) удалось открыть и другим путем - и кто знает, что бы удалось открыть, если б путь науки был все время научным.
Однако тут уж я себя поправлю: другой науки сейчас нет. Все суждения о недостатках науки производятся при наличии единственного уникального объекта - науки. Сравнить ее с какой-то другой наукой, лучшей, - нельзя: нету такой.
Автор формулирует то, что считает новым взглядом на доказательность в научном исследовании. Его позиция такая: любое научное знание условно. Знание не имеет отношения к истине. Там сложно и с оговорками, но если в простоте - старая теория операционализации знания. то есть знание есть структура действий-операций, и далее результат. Вот это знание. А категорию истины надо из науки убрать, она вредит - потому что многие соблазняются думать, что открыли истину и только монизм разводят со своими несовершенными взглядами. Автор упоминает многих современных эмпириков-плюралистов, это одна из самых распространенных позиций в современной философии науки - истины нет и она непознаваема, наше знание относится скорее к умениям, верны могут быть и противоположные точки зрения - то есть не верны, а заслуживают развития и сбора выпадающих плодов.
У меня эти выводы автора никакого сочувствия не вызывают, что не мешает оценивать книгу как совершенно выдающуюся.
Кстати, книга сделана в соответствии с убеждениями автора. Это не равномерное изложение его точки зрения. В каждой из частей он придерживается такого плана: сначала дает общее (как он говорит - популярное) изложение всего материала, облегченное и без многих деталей, но в целом верное. Потом дает в следующем разделе углубленное изложение, частично по внешности противоречащее облегченному - там много деталей. В третьем разделе раскрывает скрытые подробности и загадочные обстоятельства, которые совсем не всегда согласуются со всеми общими суждениями в других разделах. То есть каждый вопрос у него в книге раскрыт в логике"понятно для всех" - "понятно для профи" - "никому не понятно (пока)".
Книгу я пересказал безумно бедно, можно интересными деталями наполнить еще несколько страниц. Но я все же надеюсь, что кусочки цитат под катом помогут представить разнообразие материала.
1. Water and the Chemical Revolution
1 1.1.1 Joseph Priestley
1.1.3 The Trouble with Lavoisier
1.1.4 Could Water Be an Element?
1.2 Why Phlogiston Should Have Lived
1.2.1 Phlogiston vs. Oxygen
1.2.2 What Really Happened in the Chemical Revolution?
1.2.3 Weights, Composition, and Chemical Practice
1.2.4 What Good Is Phlogiston?
1.3 Choice, Rationality, and Alternatives
1.3.2 Social Explanations of the Chemical Revolution
1.3.4 Between Principlism and Compositionism
1.3.5 Counterfactual History
2 Electrolysis: Piles of Confusion and Poles of Attraction
2.1 Electrolysis and Its Discontents
2.1.1 The Distance Problem
2.1.2 Electrolysis as Synthesis
2.1.3 Lavoisierian Rescue-Hypotheses
2.1.4 “No Winner ” Is Not “No Win”
2.2 Electrochemistry Undeterred
2.2.1 How the Synthesis View Was Eliminated
2.2.2 How the Lavoisierian Rescue-Hypotheses Fared
2.2.3 The Character of Compound-Water Electrochemistry
2.3 In the Depths of Electrolytic Solutions
2.3.1 The Value of Studying Messy Science
2.3.2 Was Priestley Deluded? A View from the Laboratory
2.3.3 The Intricacies of Ion-Transport
2.3.4 Disputes on How the Battery Works
2.3.5 Ritter and Romanticism
3 HO or H2O? How Chemists Learned to Count Atoms
3.1 How Do We Count What We Can’t See?
3.1.1 Unobservability and Circularity
3.1.2 The Avogadro–Cannizzaro Myth
3.1.3 Operationalism and Pragmatism in Atomic Chemistry
3.1.4 From Underdetermination to Pluralism
3.2 Variety and Convergence in Atomic Chemistry
3.2.1 Operationalizing the Concept of the Chemical Atom
3.2.2 Competing Systems of Atomic Chemistry
3.2.3 The H2O Consensus
3.2.4 Beyond Consensus
3.3 From Chemical Complexity to Philosophical Subtlety
4 Active Realism and the Reality of H2O
4.1 Is Water Really H2O?
4.1.1 Hypothesis-Testing Within Systems of Practice
4.1.3 H2O: A Pluralistic Truth
4.1.4 Knowledge, Progress, and Active Realism
4.2 Active Scientific Realism
4.2.1 Maximizing Our Learning from Reality
4.2.2 The Optimistic Rendition of the Pessimistic Induction
4.2.3 How the Argument from Success Fails
4.2.4 The Immaturity of Maturity-Talk
4.3 Out of the Standard Realist Fly-Bottle
4.3.1 Truth and Its Multiple Meanings
4.3.2 The Certainty Trap
4.3.4 Reference (Farewell to Twin Earth)
5 Pluralism in Science: A Call to Action
5.1 Can Science Be Pluralistic?
5.1.1 Plurality: From Acceptance to Celebration
5.1.2 Monism and Pluralism
5.1.3 Why Pluralism Is Not Relativism
5.1.4 Is Pluralism Paralyzing?
5.1.5 Can We Afford It All?
5.2 Benef i ts of Plurality, and How to Attain Them
5.2.1 What Is Pluralism?
5.2.2 Benef i ts of Toleration
5.2.3 Benef i ts of Interaction
5.2.4 Tasks for History and Philosophy of Science
5.3 Further Notes on the Practice of Pluralism
5.3.1 Pluralism vs. The Pluralist Stance
5.3.2 Between Metaphysics and Epistemology
5.3.3 Can Monists Help, Too?
5.3.4 Complementary Science Continued
Anyone with even the slightest acquaintance with modern science knows that water is H 2 O. Yet it was a very diff i cult thing for scientists to learn. In this book I intend to show how contingent the series of decisions were that led people from the traditional assumption that water was an element to the consensus that it was a compound with the chemical formula H 2 O, which was not reached till the late nineteenth century. Through this story of the changing conceptions of water, I also wish to advance the debate on some major philosophical issues, including realism and pluralism. I have deliberately chosen as the subject of my study one of the most familiar substances in human life and one of the most basic scientif i c facts about that substance. My aim is to make us all aware of the challenges involved in building scientif i c knowledge, no matter how simple or taken for granted. Without such awareness, we can reach neither a true appreciation of the achievements of science nor a properly critical attitude regarding the claims of science.
Over half of the book consists of three chapters containing a philosophical history of water from the middle of the eighteenth century to the late nineteenth century.
I begin with a re-telling of the Chemical Revolution, in which water came to be recognized as a compound for the fi rst time in Western science; I will attempt, and fail, to remove a lingering suspicion that there never was such a conclusive reason for rejecting the infamous phlogiston theory. Next I examine the early history of electrochemistry, in which electricity decomposed water into hydrogen and oxygen as expected, but a serious puzzle was raised about why the two gases came out from distant places while they were presumed to originate from the same water molecule in each case. This is followed by a slice of the early history of chemical atomism, in which chemists took more than half a century to agree on changing John Dalton’s original formula for water from HO to H 2 O. In these studies I intend to make some original historiographical contributions, as well as craft new philosophical ideas fit for the purpose of framing the historical accounts.
A careful consideration of this question will lead me to formulate a fully contextual and practice-based view of evidence in scientif i c inquiry. This inevitably leads into the realism question: if scientif i c knowledge is contingent, can we still preserve the notion of scientif i c truth and its pursuit? Contingency also implies choice: past scientists could reasonably have made choices that would have led to systems of science that are different from what we have today. Rather than try to avoid this implication, I embrace it and develop it into a full-blown doctrine of pluralism in science.
My questioning of the simple and unique truth of the statement “Water is H 2 O” will raise eyebrows and disturb commonplace assumptions, and that is fully intended. Independently of the details of my various arguments, it will be benef i cial for people to realize that it is not crazy to subject the most fundamental truths of modern science to critical scrutiny, and to contemplate the possibility of scientif i c systems which deny or do without them. After all, many of the great and rational thinkers whose political, philosophical and scientif i c writings we still study with reverence did not have any idea that water was H 2 O: Newton, Voltaire, Hume, Franklin, Goethe and Kant, just to mention a few out of a myriad. In any case, very modern science no longer subscribes to the notion that water is simply H 2 O .
1 Not only does water contain rarer isotopes such as deuterium, but its familiar chemical and physical properties depend essentially on the presence of various ions, and on the continual connections and re-connections between neighboring molecules which belie the single-molecule formula of H 2 O. If we had a simple heap of H 2 O molecules, it would not be recognizable as water. Of course, the “H 2 O” view still contains an important element of truth about the constitution of water, and continues to have heuristic utility. But it would be wrong to take it as an eternal and unqualif i ed truth;
rather, it was merely one important resting-point in the continuing progressive saga of science. This illustrates a general point: there is no benef i t to be gained from a dogmatic adherence to a simple-minded scientif i c truth that science itself has already modified.
The following is a very brief synopsis of the fi ve main chapters of the book. Chapter 1 , opening our philosophical history of water, is about the Chemical Revolution of the late eighteenth century. This is a very familiar topic in history and philosophy of science, but my re-examination of it will show that there never was suff i -ciently strong evidence at the time to warrant the triumph of Antoine-Laurent Lavoisier’s oxygen theory (with water as a compound of hydrogen and oxygen) over the phlogiston theory (with water as an element). Phlogiston-based chemistry was actually a highly cogent system of knowledge, grounded in very concrete labora-tory operations such as the calcination and reduction of metals. The concept of phlogiston provided some important unifying explanations, and played an impor-tant heuristic role in many empirical discoveries, including that of oxygen itself.
Lavoisier’s chemistry had many diff i culties, both as recognized by his contem-poraries and from a modern (whiggish) point of view. The very name of “oxygen” (acid-generator) embodies a mistaken theory of acidity, and Lavoisier’s theory of combustion rested crucially on the concept of caloric, an imponderable fl uid just like phlogiston.
All in all, I argue, there were no conclusive grounds of empirical evidence, simplicity or progressiveness that supported the complete elimination of the phlogiston theory. Rather, there was a genuine methodological incommensurability between the two systems of chemistry. Joseph Priestley was not irrational or unreasonable in his resistance to Lavoisierian chemistry, nor was he alone. So I conclude that phlogiston was killed prematurely; that is a shocking claim, and its implications must be considered seriously. I argue that the concept of phlogiston should have been kept on; it was not, so we might contemplate reviving it. But a look back at the subsequent history of chemistry reveals that phlogiston was in effect brought back, under different names. Lavoisier’s chemistry never explained why chemical reactions happened, and phlogiston was later seen to have held the conceptual space that chemical potential energy would fi ll. On the other hand, phlogiston was even at the time commonly identif i ed with electricity, and could easily have been kept and developed into the concept of free electrons. Eminent chemists such as William Odling, Justus Liebig and G.N. Lewis have recognized and expressed these phlogistic connections.
If Lavoisier was right about water, it should also have been possible to decompose water into hydrogen and oxygen. Chapter 2 begins by noting the great excitement following the invention of Alessandro Volta’s “pile” (battery), which allowed the
electrolysis of water in the year 1800. What more could one ask, as proof of the compound nature of water? But there was a problem, which was already recognized in the very fi rst paper on the subject, by William Nicholson: if electrolysis broke down each molecule of water into hydrogen and oxygen, how could it be that the two gases emerged separately, at positive and negative electrodes separated by a macroscopic distance from each other? If this problem was not solved, the electrolysis of water threatened to become a piece of evidence against Lavoisier’s theory. Indeed, Johann Wilhelm Ritter advanced an anti-Lavoisierian interpretation, according to which electrolysis was synthesis : at one electrode, the combination of water with negative electricity forms hydrogen; at the other electrode, positive electricity and water make oxygen; water is an element, and hydrogen and oxygen are compounds.
Ritter’s view was not so much refuted as repelled by the mainstream of chemistry, by this time heavily Lavoisierian. There was never a convincing solution to the distance problem until the end of the nineteenth century, when Svante Arrhenius’s theory of free ionic dissociation was proposed and accepted. Meanwhile chemists and physicists consoled themselves with hypothetical mechanisms, such as an invisible transfer of oxygen or hydrogen through the water over to the other side, or a chain of partner-swapping water molecules linking the two electrodes. Who advanced and advocated which views, on what basis? Why was Ritter’s view rejected, and was there suff i cient evidence supporting that rejection? There is not a great deal of modern literature on this episode. From an examination of some primary sources and older secondary sources, I weave together an account of the development of various competing views. I also note how electrochemistry forged ahead as a productive research science without a clear agreement on the fundamental mechanism of electrolysis (and of the battery).
For those accepting that water was made up of hydrogen and oxygen, the advent of chemical atomic theory raised a further question: how many atoms of each element combined to make water? This is the subject of Chap. 3 . John Dalton, from his original 1808 publication onward, candidly acknowledged that he had no way of answering such questions with certainty. There is a fundamental circularity between atomic weights and molecular formulas. In the case of water, what was known from experiments was that hydrogen and oxygen always combined in a 1:8 ratio by bulk weight (in approximate modern numbers). From that we can deduce that the ratio of atomic weights is 1:16, if we know that water is H 2 O; or we can deduce that the molecular formula of water is H 2 O, if we know that the atomic weight ratio is 1:16.
But we need to know one in order to know the other—and to begin with, we know neither. Dalton applied his “rules of greatest simplicity” to break the circularity:
since water was the only chemical compound of hydrogen and oxygen that he knew, he assumed that it was the simplest possible atomic combination: HO. Amedeo Avogadro almost immediately proposed a system familiar to the modern eye: two volumes of H 2 and one volume of O 2 make two volumes of H 2 O. Interestingly, Avogadro’s ideas were rejected by Dalton and most other chemists as ad hoc, speculative and implausible, and not generally adopted until half a century later.
Retracing the history of early chemical atomism, I discern at least fi ve different systems of atomic–molecular chemistry in operation in the fi rst half-century. Each
system had its own distinct aims, and its own list of successes and failures, too.
It was only as a result of some complicated developments and interactions of these systems that the consensus on the H 2 O formula slowly emerged. It was not simply a matter of reviving and publicizing Avogadro’s hypothesis in a clearer and more convincing form. Many clues had to be fi tted together, and some of the decisive clues arose from very subtle developments in organic chemistry in the 1840s and the 1850s. When the consensus on molecular formulas and atomic weights (including H 2 O for water) did come, it was not taken by everyone in a realist manner; many leading chemists still doubted the existence of physical atoms, and had reservations about taking the models of structural chemistry literally. And the synthesis of systems leading to this consensus also left some important questions unanswered, which were taken up by the newly emerging fi eld of physical chemistry.
Regarding each of the episodes treated in the fi rst three chapters, I arrive at the judgment that there was no system that deserved a monopolistic dominance, and that not having one dominant system in each situation did not hamper, or would not have hampered, the progress of science. There can be, and have been, successful systems of science which do not aff i rm the truth of the statement that water is H 2 O.
What does this judgment imply about the traditional conception of the pursuit of truth in science? Addressing this question in Chap. 4 , I advance a novel doctrine called active scientif i c realism, which aff i rms that science should strive to maximize our contact with reality in order to learn as much as we can. “Reality” is taken to mean whatever is not subject to one’s own will; reality offers resistance to our ill-conceived schemes, as the pragmatists put it. Nearly all sides in the scientif i c realism debate should be able to subscribe to active realism. But there is a more controversial side to it, too. Active realism recommends that we should pursue all systems of knowledge that can provide us an informative contact with reality; if there are mutually incom-mensurable paradigms, we should retain all of them at once. But will that not interfere with the pursuit of the one truth about nature? I maintain that we need to come away from such an inoperable notion of truth. When we come to consider what “truth” means in practice, the concept splinters into several different ones, including one that is internal to a given system and nearly synonymous with “success”. Realism should be a commitment to promote realistic ways of learning from reality, not a vain and hubristic attempt to prove that we are in possession of the unique truth about nature.
My discussion of evidence and realism leads to a general pluralism about science, which I explicate and advocate fully in Chap. 5 . When we take a fully contextual view of evidence, we will come to see that any serious scientif i c topic is bound to admit more than one rationally justif i ed treatment. To the extent that scientists have a tendency to agree on one theory (or system) at a given time, we need to be aware of the possibility that there might be worthwhile alternatives that are rejected without suff i cient reasons. This tendency is amply exhibited in the episodes discussed in Chaps. 1 and 2 , and there are many other apt cases in the history of science. The judgment that a system of knowledge was rejected without suff i cient epistemic warrant is a weighty one to make. First of all, it involves a claim that it would have been better to let it survive. Secondly, judgment comes with a demand for action: if I think, for instance, that phlogiston chemistry was killed off prematurely,what am I going to do about it? If there is lost potential there, it should be recovered and developed. This is pluralism in practice — not the armchair pluralism of declaring “Let a hundred fl owers bloom”, but an active pluralism of actually cultivating the 99 neglected fl owers.
But why is it better to be pluralistic? Why keep multiple systems of knowledge alive? The immediate reason for this is the sense that we are not likely to arrive at the one perfect theory or viewpoint that will satisfy all our needs. Call it pessimism, but I do not think it is unwarranted pessimism. I would rather think of it as reasonable humility about human capabilities. If we are not likely to fi nd the one perfect system, it makes sense to keep multiple ones, which will each have different strengths. Different benef i ts, practical and intellectual, will spring from different sys-tems of knowledge. It is also important to note that the co-existence of multiple systems can facilitate productive interactions between them through integration, co-optation and competition. These benef i ts of interaction are just as important as the more widely recognized benef i ts of toleration; both are essential planks in the program of pluralism that I advocate. It is important to distinguish pluralism from relativism. Relativism involves an idle permissiveness and renunciation of judgment.
Pluralism does not renounce judgment, yet maintains that it is better to foster a multitude of worthwhile systems, rather than only one. Pluralism as I conceive it actively engages in the work of proliferation; it is about knowledge-building, not just knowledge-evaluation. In that sense, pluralism emerges as the underlying spirit behind the project of complementary science.
This book has an unusual structure, which deserves some explanation at the outset. Each chapter has three main sections. Section 1 gives an engaging surface-level introduction and summary, intended to be accessible to non-specialists; it is at the level of depth and detail that I may be drawn to give in a serious sociable conversa-tion with interested friends. Section 2 contains a full exposition of my position without constraints; it says what I want to say the way I want to say it, in a linear, focused and systematic way, assuming a fair amount of background. Then Section 3 follows up with esoteric details and anticipated objections that would interest specialists on particular topics; it is a mix of in-depth discussion, self-defence, apologies, qualif i cations, and projections for future work; some of it will be shallow and sketchy, merely registering an awareness of certain issues and questions and encouraging future work by myself and others.
For readers who fi rst want to get a sense of what this book is all about, or those who do not think they can invest much time reading it, or those who just want the big story without esoteric details, I recommend the surface approach: read this Introduction, and then Section 1 of all the chapters. If that intrigues you suff i ciently, or if you are already determined to fi nd out in full what it is that I have learned and think you would enjoy learning, too, then you can take the full-content approach by reading Sections 1 and 2 of all the chapters. If you are a philosopher who can’t stand historical details, then you can take the surface approach in Chapters 1 , 2 , and 3 , and follow that with a full reading of Chapters 4 and 5 . But I make a gentle request: be open to the possibility that you may get intrigued about the history through reading
The evidential assessment made in the last section leaves us with a very uncertain verdict. It seems clear that each of the oxygenist and the phlogistonist systems had its own merits and diff i culties, and that there were different standards according to which one or the other was better supported by empirical evidence. In a way, this is only an indication that evidential support is not a straightforward matter of logical or probabilistic connections between theory and observation, but a complex rela-tionship mediated by epistemic values, which can be divergent and contextual. My own judgment is that both systems were partially successful in their attempts to attain worthwhile goals, and that there was no reason to clearly favour one over the other (I will say more about the implications of that judgment in Sect. 1.2.4 ). But if there was no clear justif i cation for the choice of oxygen over phlogiston, then why did chemists make that choice? Why did the Chemical Revolution happen? In Sect. 1.1 I only touched brief l y on this question. One reason I did not enter into a full discussion of it is that I think philosophers and historians have wasted a lot of time and energy by tackling an illusory question. There is great futility in the enter-prise of explaining why the vast majority of chemists quickly went over to Lavoisier’s side—because actually that is not quite what happened. I would like to set out a different and more accurate story of the Chemical Revolution, before I launch into further discussions of its causes, its rationality, and its consequences.
There is an extensive literature on the Chemical Revolution, which I will not be able to survey with any comprehensiveness here; instead I refer the reader to John McEvoy’s ( 2010 ) up-to-date and thorough critical review of this literature. My own aim here is to advance a particular revisionist thesis: the Chemical Revolution did not consist in a swift and nearly universal conversion of the chemical community to Lavoisier’s theory. I have made that argument more fully elsewhere (Chang 2010 ) , so I will present a shorter summary.
To summarize: the clear evidential advantage of the oxygenist system on the basis of weight considerations only holds if one accepts compositionism; phlogis-tonists disregarded weight-based arguments because they were principlists. The Chemical Revolution makes much more sense when we see it as a ripple riding on a large wave, which was the very gradual establishment of compositionism. It is important to see beyond the clash between phlogiston and oxygen. If we should want to conceive of the Chemical Revolution as the event that gave rise to “modern chemistry”, we must follow Robert Siegfried and Betty Jo Dobbs ( 1968 ) in identifying it as a compositionist revolution, whose endpoint was not Lavoisier, but Dalton.
All in all, I think it is quite clear that killing phlogiston off had two adverse effects: one was to discard certain valuable scientif i c problems and solutions; the other was to close off certain theoretical and experimental avenues for future scien-tif i c work. Perhaps it’s all fi ne from where we sit, since I think the frustrated poten-tial of the phlogistonist system was quite fully realized eventually, by some very circuitous routes. But it seems to me quite clear that the premature death of phlogiston retarded scientif i c progress in quite tangible ways. If it had been left to develop, I think the concept of phlogiston would have split into two. On the one hand, by the early nineteenth century someone might well have hit upon energy conservation, puzzling over this imponderable entity which seemed to have an elusive sort of reality which could be passed from one ponderable substance to another.
In that parallel universe, we would be talking about the conservation of phlogiston, and how phlogiston turned out to have all sorts of different forms, but all intercon-vertible with each other. This would be no more awkward than what we have in our actual universe, in which we still talk about the role of “oxygen” (acid-generator, Sauerstoff ) in supporting combustion, and the “oxidation” number of ions. On the other hand, the phlogiston concept could have led to a study of electrons without passing through such a categorical and over-simplif i ed atomic theory as Dalton’s.
Chemists might have skipped right over from phlogiston to elementary particles, or at least found an alternative path of development that did not pass through the false simplicity of the atom–molecule–bulk matter hierarchy. Keeping the phlogiston theory would have led chemists to pay more attention to the “fourth state of matter”, starting with fl ames, and served as a reminder that the durability of compositionist chemical building-blocks may only be an appearance. Keeping phlogiston alive could have challenged the easy Daltonian assumption that chemical atoms were physically unbreakable units.
The survival of phlogiston into the nineteenth century would have sustained a vigorous alternative tradition in chemistry and physics, which would have allowed scientists to recognize with more ease the wonderful fl uidity of matter, and to come to grips sooner with the nature of ions, solutions, metals, plasmas, cathode rays, and perhaps even radioactivity.
My own sense about the rationality of the Chemical Revolution is as follows.
The Chemical Revolution, as it actually happened , was a fairly rational affair, in the sense that there was reasoned debate about the choice between the competing systems for the most part. The evidential situation was not clear-cut, and the response was accordingly diverse, which is also quite rational. The main irrationality I see in the picture is not in the refusal of some chemists to go along with Lavoisier, but in the readiness of too many others to do so, which will be discussed in Sect. 1.3.2 below.
It was perhaps irrational to retain terms like “oxygen” after the rationale for their naming had disappeared. Irrationality increased in the later retrospective glorif i ca-tions of Lavoisier, though in one sense those were rational, too: they served the (political) purposes of those who made them!
The results of my counterfactual investigations were reported in Sect. 1.2.4 . The initial counterfactual returns were encouraging, and I became fairly convinced that a robust survival of phlogiston would have accelerated developments in chemistry and physics. However, as my historical research progressed, I was also pleasantly sur-prised to learn that the work of reviving phlogiston had actually been done already by a number of other scholars. Not only have there been relatively maverick attempts to employ phlogiston again for various scientif i c purposes, reaching from Davy in the early nineteenth century to Allchin in the late twentieth. Even more important is the recognition that some important aspects of the phlogiston concept were actually brought back, under different names, in order to help remedy the shortcomings of Lavoisierian–compositionist chemistry as it weathered the nineteenth century. When Odling and others saw phlogiston as the predecessor of chemical potential energy, and when Lewis saw phlogiston as the predecessor of electrons, what they were doing may have been whiggish but it was certainly not pointless. And their insights provide a suff i cient answer as to why I am not going to try to bring phlogiston back to modern chemistry—it is already here!
Abstract However one might assess the arguments about the nature of water in the Chemical Revolution (Chap. 1), it may seem that the electrolysis of water (f i rst performed in 1800) must have produced decisive evidence that it was a compound substance. But electrolysis came with a serious puzzle: if the action of electricity was breaking up each particle of water into a particle of oxygen and a particle of hydrogen, how did the oxygen and hydrogen gases emerge at electrodes that were separated from each other by macroscopic distances? The distance problem turned the electrolysis of water into a serious anomaly, rather than positive evidence, for Lavoisierian chemistry. Ritter and his followers argued that electrolysis was in fact a pair of syntheses: water was an element after all, and its combination with positive and negative electricity formed oxygen and hydrogen. This view was dismissed by the majority of post-Lavoisierian chemists, but never conclusively refuted at the time. Those who opposed Ritter proposed a plethora of different solutions to the distance problem, none of them completely convincing. The modern ionic theory only emerged in the last years of the nineteenth century, so there was nearly a whole century of electrochemistry taking place without a consensus on some very basic questions. Nonetheless, electrochemistry made signif i cant progress. Its experimental practices were stabilized and standardized without recourse to agreed-upon fundamental theory. In the theoretical realm there was pluralistic progress, with several competing systems each making its distinctive contributions, in productive interaction with each other.
-- Given this situation, it seems to me that the nineteenth-century scientists were wise when they decided not to decide—or rather, not to declare a clear winner amongst a group of imperfect contenders. Leaving the ultimate truth undecided, electrochemists got on with their work, experimental and theoretical, as we will see in some detail in Sect. 2.2.2 . That seems to me like the right and mature thing to have done, rather than giving in to the temptation of a clear choice—as in the case of the Lavoisierian bandwagon that made the Chemical Revolution. The legacy of Lavoisierian dogmatism is the only signif i cant blemish on the pleasing pluralism of nineteenth-century electrochemistry: just one among the several serious theoretical alternatives was suppressed, namely Ritter’s synthesis view, for its attempted anti-Lavoisierian resurrection of elementary water. The dogmatic nature of this suppres-sion also meant that the electrolysis could not function as independent evidence for the compound nature of water until much later. (More positively, this stroke of dogmatism did create a useful common ground for all those who believed in com-pound water; see Chap. 5 on how such benef i ts can still be preserved in a more pluralistic regime of science.)
In this part of the chapter I will take a deeper and broader look at the debate on the electrolysis of water. First, I will consider how well the various competing theories accounted for the phenomena. Did Ritter’s synthesis view deserve to be eliminated?
And how good were the various Lavoisierian rescue-hypotheses? After that consid-eration, I will use this debate on electrolysis as a lens through which we can gain a fresh and informative view of the development of electrochemistry in the earlier parts of the nineteenth century. Except for a few recognizably brilliant moments, such as Davy’s discovery of the alkali metals and Faraday’s elucidation of electro-chemical equivalents, electrochemistry for most of the nineteenth century may seem to have been mired in disputes between competing theories, without a productive agreement until after Arrhenius. I would like to correct that impression, and bring out fruitful patterns of development hidden in the messy state of plurality.
Understandably, not many chemists and physicists were willing to follow Ritter’s imaginative leaps and daring experiments to see which parts of his fantastical-sounding ideas and observations could be verif i ed and built upon. Although he was very popular with scientists and philosophers sympathetic to Romantic Naturphilosophie , Ritter’s standing in science declined as unfavorable reactions to Naturphilosophie set in among men of science. Even phlogistonists were on the whole quite sober-minded people who did not like Ritter’s wildly brilliant style of science. It is telling that Priestley did not ally himself with Ritter. Ritter’s view on the electrolysis of water was thrown out by mainstream science as part of a compre-hensive rejection, and layers of it: the rejection of his views on electricity in general, the rejection of any theories of chemistry incorporating elementary water (including the phlogiston theory), and the rejection of Naturphilosophie . I will not enter here into the question of whether Ritter’s general outlook should have been maintained in science. What is clear is that the idea of elementary water was logically independent of Ritter’s other views, and it was perhaps unfortunate that the unfortunate Ritter was its leading advocate at the turn of the nineteenth century.
In summary, what can we say about the electrolysis of water in relation to the com-plex theoretical fi eld in nineteenth-century electrochemistry? There are two major points to note. First, electrolysis did not provide any conclusive additional argument for the compound nature of water; rather, the bulk of work in electrochemistry beyond the fi rst few years of the nineteenth century was partly def i ned by its exclu-sion of elementary water as postulated in the phlogiston theory and in Ritter’s theory of electrolysis. Second, within the tradition of what I have called compound-water electrochemistry, there was a frank recognition of many unsolved problems and deep underlying theoretical uncertainty. As a result, electrochemistry developed in a pluralistic manner despite having ruled out Ritter’s synthesis view. Without reach-ing a grand theoretical consensus, electrochemistry based its theoretical debates on a reasonably stable and expanding body of experimental work. Disputes on the mechanism of electrolysis, which continued throughout the nineteenth century, did not disturb the assumption of compound water, which retained the axiomatic status that was assigned to it in the early years.
Having learned to be cautious about sweeping explanations involving the rejection of romanticist science, let us return to the question about the reasons for the rejection of Ritter’s ideas. I think Ritter’s failure to be accepted by the communities of chemists and physicists had more to do with style and strategy of communication rather than the substance of his work, just as much as Lavoisier’s success owed much to his vigorous and effective campaigning. It does not even seem that Ritter’s work was strongly ruled by a desire to be accepted by the scientif i c communities.
As factors hindering the scientif i c acceptance of Ritter’s work, I note the following.
(1) His style was profuse and diffuse, and not easily accessible to those who did not invest a great deal of time and attention. (2) He was not strategic in placing his pub-lications in high-prof i le outlets. (3) He made no efforts to downplay certain thoughts and results, such as his work on water-divination, that were likely to put off the audiences he was addressing. (4) Placing himself against the solidifying Lavoisierian orthodoxy reduced his chances of being accepted in the German chemical community.
There may have been other reasons, too. What seems certain, however, is that the rejection of Ritter’s electrochemical theory was idiosyncratic and contingent, rather than principled and inevitable.
Abstract Water served as an emblematic locus for debates on the atomic constitution of matter. Today it is taken as common sense that water is H 2 O, but this was a highly disputed hypothesis for the fi rst half-century of atomic chemistry. In Dalton’s origi-nal formulation of the atomic theory published in 1808 water was presented as HO, and consensus on the H 2 O formula (f i rst proposed by Avogadro) was not reached until after the mid-century establishment of organic structural theory based on the concept of valency. The main epistemic diff i culty was unobservability: molecular formulas could be ascertained only on the basis of the knowledge of atomic weights, and vice versa. There were multiple self-consistent sets of molecular formulas and atomic weights, which were employed in at least fi ve different systems of atomic chemistry that fl ourished in the nineteenth century, each with its distinctive set of aims and methods and in productive mutual interaction. At the heart of the distinc-tive systems of atomic chemistry were different ways of operationalizing the con-cept of the atom (weighing, counting, and sorting atoms). It was operationalization that enabled atomic theories to become more than mere hypotheses that may or may not be consistent with observed phenomena. If we examine the crucial phase of development in which the consensus on H 2 O was achieved, the key was not the revival of Avogadro’s ideas by Cannizzaro, but the establishment of good atom-counting methods in substitution reactions. This, too, was a triumph of operational-ization. We also need to keep in mind that the H2O consensus was not a straightforward unif i cation of all systems of atomic chemistry; rather, it was a reconfiguration of the field which resulted in a new pluralistic phase of development.
Dalton’s main contribution was to marry the familiar old (even ancient) idea of atoms and the eighteenth-century chemistry of compositions, 4 creating the essential nexus of nineteenth-century atomic chemistry. He realized that some striking regu-larities in the proportions by which various chemical substances combined with each other could be explained nicely if one assumed that chemical combination was the grouping together of atoms possessed of def i nite weights. For example, examin-ing the fi ve oxygen–nitrogen compounds known to him, he discerned compounds that would be written in modern notation as NO, N 2 O, NO 2 , NO 3 , and N 2 O 3 , as shown in Fig. 3.1 (diagrams 41–45).
5 Dalton published his atomic ideas in a book titled A New System of Chemical Philosophy , the fi rst part of which appeared in 1808. It is gratifying to know that the ideas of this unknown country schoolteacher received proper attention from the scientif i c community. Although many chemists were reluctant to believe in Daltonian atoms in a fully literal sense, it soon became common practice to conceptualize chemical reactions in terms of the grouping and re-grouping of some atomic units of elementary substances. Dalton remained in the provinces and kept to a modest way of life, but his work in chemistry and physics was widely acclaimed. He became a Fellow of the Royal Society of London (though he almost never attended its meetings), had an audience with the King, and served as the President of the Manchester Literary and Philosophical Society.
When he died he was given a state funeral. Not bad for a scientist who never even went to secondary school!
The real story as I see it, which is told in fulsome detail by Brooke ( 1981 ) and Nicholas Fisher ( 1982 ) , is that Avogadro’s microphysical hypotheses were noticed, discussed, and rejected by most, for fair enough reasons. They were too hypothetical and blatantly ad hoc , not grounded in any experiments providing independent empirical evidence. In addition, Dalton had specif i c physical arguments against them, and so did the promulgators of electrochemical dualism, including Berzelius.
For the latter, the story was simple: two atoms of the same kind have the same elec-tric charge, so they would repel each other. As for Dalton, in connection with his rules of simplicity I have noted above his view that all atoms were full of self-repellent caloric, and chemical combination could happen only between different types of atoms which exerted an attractive force of chemical aff i nity on each other, enough to overcome the self-repulsion of caloric. Avogadro does not seem to have given a convincing account of why two atoms of the same kind should stick together, and if they do, why the lumping would stop at two atoms. Jean-Baptiste Dumas (1800–1884) made a serious attempt to develop Avogadro’s ideas, but he gave up after his study of vapor densities revealed apparent contradictions or at least arbitrariness; for example, the elementary molecule of mercury, phosphorus and sulphur had to be regarded as Hg, P 4 and S 6 , not binary like hydrogen, oxygen and nitrogen (see Nye 1976 , 248).