19th-century theories of boiling

It is of some interest to examine the historical development of theories of boiling through the 19th century. Developments in the early 19th century laid the foundation for the familiar thermodynamic theory that presumes the sharpness of the boiling temperature as a function of external pressure; this theoretical framework went very nicely with the practical use of the steam-point, as will be apparent in the discussion to follow. On the other hand, there were also some ideas in the 19th century which went in other directions. Some of these ideas were later incorporated (or reinvented) in the modern engineering theory of boiling; others disappeared. Therefore the 19th-century theoretical history will both help us understand the modern theories better, and point to their limitations.

In charting the 19th-century developments, let us start with a very basic question. We have seen that De Luc's extensive investigations in the late 18th century did not lead to any conclusive ideas about the definition of boiling. The 19th-century investigators retreated to the basic common notion that for anything to deserve the name of "boiling" to take place, vapor should form within the body of the liquid water and move out through the liquid. But why should this happen at anything like a fixed temperature? The crucial factor is the relation between the pressure and the temperature of water vapor. Suppose we let a body of water evaporate into an enclosed space as much as possible. In the familiar setup, a small amount of water rests on a column of mercury in a barometer-like inverted glass tube, and evaporates into the vacuum above the mercury until it cannot evaporate any more. Then the space is said to be "saturated" with vapor; similarly, if such a maximum evaporation would occur into an enclosed space containing air, the air is said to be saturated. Perhaps more confusingly, it is also said that the vapor itself is saturated, under those circumstances.

It was observed already in the mid-18th century that the density of saturated vapor is such that the pressure exerted by it seemed to have a definite value determined by temperature, and temperature only. If one allows more space after saturation is obtained (for instance by lifting the inverted test tube a bit higher), then just enough additional vapor is produced to maintain the same pressure as before; if one reduces the space, enough vapor turns back into water so that the vapor pressure again remains the same. But if the temperature is raised, more vapor per available space is produced, resulting in a higher vapor pressure. It was in fact Lord Charles Cavendish (1704-1783), Henry's father, who first designed the simple mercury-based equipment to show and measure vapor pressures, and the son fully endorsed the father's results and assigned much theoretical significance to them as well (see Cavendish [n.d.] 1921, 355, and also Jungnickel and McCormmach 1999, 127). Cavendish's discovery of the exclusive dependence of vapor pressure on temperature was later confirmed by numerous illustrious observers including James Watt (1736-1819), John Dalton (1766-1844), and Victor Regnault (1810-1878). The tableshows some of the vapor-pressure data obtained by various observers.

A comparative table of vapor-pressure measurements for water (All of the vapor pressure data in this table indicate the height of a column of mercury balanced by the vapor, in English inches.)


Charles Cavendish (c.1757)a

John Dalton (1802)b

Jean-Baptiste Biot (1816)c

Victor Regnault (1847)d


Vapor pressure e

Vapor pressure

Vapor pressure

Vapor pressure

35°F (1.67°C)

0.20 in. Hg














50 (10°C)






























86 (30°C)





104 (40°C)





122 (50°C)





140 (60°C)





158 (70°C)





176 (80°C)





194 (90°C)





212 (100°C)





302 (150°C)





392 (200°C)





446 (230°C)





a These data are taken from Cavendish [n.d.] 1921, 355, editor's footnote.

b Dalton 1802, 559-563. The last point (for 302°F, or 150°C) was obtained by extrapolation.

c Biot 1816, 1:531. The French data (Biot's and Regnault's) were in centigrade temperatures and millimeters of mercury. I have converted the pressure data into English inches at the rate of 25.4mm per inch.

d Regnault 1847, 624-626. The entries for Regnault in the 35°-75°F range are approximate conversions (except at 50°F), since his data were taken at each centigrade, not Fahrenheit, degree.

As seen in the table, the pressure of saturated vapor ("vapor pressure" from now on, for convenience) is equal to the normal atmospheric pressure when the temperature is 100°C. That observation provided the basic theoretical idea for a causal understanding of boiling: boiling takes place when the water produces vapor with sufficient pressure to overcome the resistance of the external atmosphere. (This idea was also harmonious with Antoine Lavoisier's view that a liquid was only prevented from flying off into a gaseous state by the force of the surrounding atmosphere.) This view gave a natural explanation for the pressure-dependence of the boiling point. It also provided perfect justification for the use of steam temperature to define the boiling point, since the key relation underlying the fixity of that point is the one between the temperature and pressure of saturated steam.

The above view, which I will call the pressure-balance theory of boiling, was a powerful and attractive theoretical framework. Still, there was a lot of "mopping up" or "anomaly-busting" left to do (to borrow liberally from Thomas Kuhn's description of "normal science"). The first great anomaly for the pressure-balance theory of boiling was the fact that the boiling temperature was plainly not fixed even when the external pressure was fixed. The typical and reasonable thing to do was to postulate, and then try to identify the existence of interfering factors preventing the "normal" operation of the pressure-balance mechanism. An alternate viewpoint was that the matching of the vapor pressure with the external pressure was a necessary, but not sufficient condition for boiling, so other facilitating factors had to be present in order for boiling to occur. The two points of view were in fact quite compatible with each other, and they were used interchangeably sometimes even by a single author: saying that factor X was necessary to enable boiling came to the same thing in practice as saying that the absence of X prevented boiling. There were various competing ideas about the operation of these facilitating or preventative factors. Let us see if any of these auxiliary ideas were truly successful in defending the pressure-balance theory of boiling, thereby providing a theoretical justification for the use of the steam point.

Gay-Lussac (1818, 130) theorized that boiling would be retarded by the adhesion of water to the vessel in which it is heated, and also by the cohesion of water within itself. The "adhesion of the fluid to the vessel may be considered as analogous to its viscidity. . . . The cohesion or viscosity of a fluid must have a considerable effect for its boiling point, for the vapor which is formed in the interior of a fluid has two forces to overcome; the pressure upon its surface, and the cohesion of the particles." Therefore "the interior portions may acquire a greater degree of heat than the real boiling point," and the extra degree of heat acquired will also be greater if the vessel has stronger surface adhesion for water. Gay-Lussac inferred that the reason water boiled "with more difficulty" in a glass vessel than in a metallic one must be because there were stronger adhesive forces between glass and water than between metal and water. Boiling was now seen as a thoroughly sticky phenomenon. The stickiness is easier to visualize if we think of the boiling of a thick sauce, and allow that water also has some degree of viscosity within itself and adhesiveness to certain solid surfaces.

Twenty-five years later Marcet (1842, 388-390) tested out the adhesion hypothesis more rigorously. First he predicted that throwing in bits of metal into a glass vessel of boiling water would lower the boiling temperature, but not as far down as 100°C, which is where water boils when the vessel is entirely made of metal. This prediction was borne out in his tests, since the lowest boiling temperature he could ever obtain with the insertion of metal pieces was 100.2°C, contrary to Gay-Lussac's earlier claim that it went down to 100°C exactly. More significantly, Marcet predicted that if the inside of the vessel could be coated with a material that has even less adhesion to water than metals do, the boiling temperature would go down below 100°C. Again as predicted, Marcet achieved boiling at 99.85°C in a glass vessel scattered with drops of sulphur. When the bottom and sides of the vessel were covered with a thin layer of gomme laque, boiling took place at 99.7°C. Although 0.3° is not a huge amount, Marcet felt that he had detected a definite error in previous thermometry, which had fixed the boiling point at the temperature of water boiling in a metallic vessel:

"It is apparent that previous investigators have been mistaken in assuming that under given atmospheric pressure, water boiling in a metallic vessel had the lowest possible temperatures, because in some cases the temperature could be lowered for a further 0.3 degrees. It is, however, on the basis of that fact, generally assumed to be exactly true, that physicists made a choice of the temperature of water boiling in a metallic vessel as one of the fixed points of the thermometric scale." (Marcet 1842, 391)

Finally, it seemed, theoretical understanding had reached a point where it could lead to a refinement in existing practices, going beyond their retrospective justification.

Marcet's beautiful confirmations seemed to show beyond any reasonable doubt the correctness of the pressure-balance theory modified by the adhesion hypothesis. However, two decades later Dufour (1861, 254-255) voiced strong dissent on the role of adhesion. Since he observed extreme superheating of water drops removed from solid surfaces by suspension in other liquids, he argued that simple adhesion to solid surfaces could not be the main cause of superheating. Instead Dufour stressed the importance of the ill-understood molecular actions at the point of contact between water and other substances:

"For example, if water is completely isolated from solids, it always exceeds 100°C before turning into vapor. It seems to me beyond doubt that heat alone, acting on water without the joint action of alien molecules, can only produce its change of state well beyond what is considered the temperature of normal ebullition."

Dufour's notion was that the production of vapor would only take place when a sort of equilibrium that maintains the liquid state was broken. Boiling was made possible at the point of pressure-balance, but some further factor was required for the breaking of equilibrium, unstable as it may be. Heat alone could serve as the further facilitating factor, but only at a much higher degree than the normal boiling point. Dufour also made the rather subtle point that the vapor pressure itself could not be a cause of vapor-production, since the vapor pressure was only a property of "future vapor," which did not yet exist before boiling actually set in. Dufour's critique was cogent, but he did not get very far in advancing an alternative. He was very frank in admitting that there was insufficient understanding of the molecular forces involved (see the last pages of Dufour 1861, esp. 264). Therefore the principal effect of his work was to demolish the adhesion hypothesis without putting in a firm positive alternative.

There were two main attempts to fill this theoretical vacuum. One was a revival of Cavendish's and De Luc's ideas about the importance of open surfaces in enabling a liquid to boil. According to Cavendish's "first principle of boiling," the conversion of water at the boiling point into steam was only assured if the water was in contact with air or vapor. And De Luc had noted that air bubbles in the interior of water would serve as sites of vapor-production. For De Luc this phenomenon was an annoying deviation from true boiling, but it came to be regarded as the definitive state of boiling in the new theoretical framework.

One crucial step in this development was taken by Marcel Emile Verdet, whose work is discussed briefly in the discussion of superheating. Following the basic pressure-balance theory, he defined the "normal" point of boiling as the temperature at which the vapor pressure was equal to the external pressure, agreeing with Dufour that at that temperature boiling was made "possible, but not necessary." Accepting Dufour's view that contact with a solid surface was a key factor promoting ebullition, Verdet also made an interesting attempt to understand the action of solid surfaces along the Cavendish-De Luc line. He theorized, somewhat tentatively, that boiling was not provoked by all solid surfaces, but only by "unwettable" surfaces that also possessed microscopic roughness. On those surfaces, capillary repulsion around the points of irregularity would create small pockets of empty space, which could serve as sites of evaporation. There would be no air or steam in those spaces initially, but it seemed sensible that a vacuum should be able to serve the same role as gaseous spaces in enabling evaporation. If such an explanation were tenable, then not only Dufour's observations but all the observations that seemed to support the adhesion hypothesis could be accounted for. (For the exposition of Verdet's view, I follow Gernez 1875, 351-353.)

Verdet's idea was taken up more forcefully by Desiré-Jean-Baptiste Gernez (1834-1910), physical chemist in Paris, who was one of Louis Pasteur's "loyal collaborators" and contributed to various undertakings ranging from crystallography to parasitic etiology. (The information about Gernez is taken from M. Prévost, et al., eds., Dictionnaire de Biographie Française, vol. 15, and also from comments in G. Geison's entry on Pasteur in the Dictionary of Scientific Biography, 10:360, 373-374.) In papers published in 1866 and 1875, Gernez reported that common boiling could always be induced in superheated water by the insertion of a trapped pocket of air into the liquid by means of a small glass instrument. A tiny amount of air was sufficient for this purpose, since boiling tended to be self-perpetuating once it began. Gernez (1875, 338) thought that at least half a century had been wasted due to the neglect of De Luc's work: "the explanation of the phenomenon of boiling that De Luc proposed was so clear and conformable to reality, that it is astonishing that it was not universally adopted." (In Gernez's view, the general rejection of De Luc's ideas had probably been prompted by De Luc's "unfortunate zeal" in opposing Lavoisier's chemistry.) In Gernez's view a full understanding of boiling could be achieved by a consistent and thorough application of De Luc's idea, a process initiated by Donny, Dufour, and Verdet among others. Donny (1846, 189) had given a new theoretical definition of boiling as evaporation from interior surfaces: "boiling is nothing but a kind of extremely rapid evaporation that takes place at interior surfaces of a liquid that surrounds bubbles of a gas."

Gernez (1875, 376) took up Donny's definition, adding two refinements. First, he stated that such boiling started at a definite temperature, which could be called "the point of normal ebullition." He added that the gaseous surfaces within the liquid could be introduced by hand, or produced spontaneously by the disengagement of dissolved gases. Here one should also allow a possible role of Verdet's empty spaces created by capillary forces, and of internal gases produced by chemical reactions or electrolysis (the latter effect was demonstrated by Dufour (1861, 246-249). Gernez's mopping-up bolstered the pressure-balance theory of boiling quite sufficiently; the presence of internal gases was the crucial enabling condition for boiling, and together with the balance of pressure it constituted a sufficient condition as well. The theoretical foundation of boiling now seemed quite secure.

There were, however, more twists to come in the theoretical debate on boiling. While Verdet and Gernez were busily demonstrating the role of gases, a contrary view was being developed by Charles Tomlinson (1808-1897) in London . Tomlinson believed that the crucial enabling factor in boiling was not gases, but small solid particles. Tomlinson's argument was based on some interesting experiments that he had carried out with superheated liquids. Building on previous observations that inserting solid objects into a superheated liquid could induce boiling, Tomlinson (1868-69, 243) showed that metallic objects lost their vapor-liberating power if they were chemically cleaned to remove all specks of dust. In order to argue conclusively against the role of air, he lowered a small cage made out of fine iron-wire gauze into a superheated liquid, and showed that no boiling was induced as long as the metal was clean. The cage was full of air trapped inside, so Tomlinson inferred that there would have been visible production of vapor if air had really been the crucial factor. He declared: "It really does seem to me that too much importance has been attached to the presence of air and gases in water and other liquids as a necessary condition of their boiling." (ibid., 246) Defying Dufour's warning against theorizing about boiling on the basis of the properties of "future vapor," Tomlinson started his discussion with the following "definition": "A liquid at or near the boiling-point is a supersaturated solution of its own vapour, constituted exactly like soda-water, Seltzer-water, champagne, and solutions of some soluble gases." (ibid., 242) This conception allowed Tomlinson to make use of insights from his previous studies of supersaturated solutions.

Tomlinson's theory and experiments attracted a good deal of attention, and a controversy ensued. It is not clear to me whether and how this argument was resolved. As late as 1904, the second edition of Thomas Preston's well-informed textbook on heat reported: "The influence of dissolved air in facilitating ebullition is beyond question; but whether the action is directly due to the air itself or to particles of dust suspended in it, or to other impurities, does not seem to have been sufficiently determined." (Preston 1904, 362) Much of the direct empirical evidence cited by both sides was in fact ambiguous: ordinary air typically contained small solid particles; on the other hand, introducing solid particles into the interior of a liquid was likely to bring some air into it as well (as De Luc had noticed when he tried to insert thermometers into his air-free water). Some experiments were less ambiguous, but still not decisive. For example, Gernez acknowledged in his attack on Tomlinson that the latter's experiment with the wire-mesh cage would clearly be negative evidence regarding the role of air; however, he claimed that Tomlinson's result could not be trusted because it had not been replicated by anyone else. Like Dufour earlier, Gernez (1875, 354-357, 393) also scored a theoretical point by denigrating as unintelligible Tomlinson's concept of a liquid near boiling as a supersaturated solution of its own vapor, though he was happy to regard a superheated liquid as a supersaturated solution of air.

The Tomlinson-Gernez debate on the theory of boiling is fascinating to follow, but its details were not so important for understanding the fixity of the steam point. Saturated vapor does obey the pressure-temperature relation, whatever the real cause of its production may be. Likewise, the exact method by which the vapor is produced is irrelevant as well. The pressure-temperature relation is all the same, whether the vapor is produced by steady common boiling, or by bumpy and unstable superheated boiling, or by an explosion, or by evaporation from the external surface alone. After a century of refinement, then, it became clear that boiling itself was irrelevant to the definition or determination of the "boiling point."

Before we close the discussion of 19th-century theories, it will be instructive to make a brief examination of the ideas of the Scottish meteorologist John Aitken broader ideas. His work on the supersaturation of steam came from a general theoretical viewpoint about the "conditions under which water changes from one of its forms to another." There are four such changes of state that take place commonly: melting (solid to liquid), freezing (liquid to solid), evaporation (liquid to gas), and condensation (gas to liquid). Aitken's general viewpoint about changes of state led him to expect that steam must be capable of supersaturation, before he made any observations of the phenomenon. In his own words:

"I knew that water could be cooled below the freezing-point without freezing. I was almost certain ice could be heated above the freezing-point without melting. I had shown that water could be heated above the boiling-point. . . . Arrived at this point, the presumption was very strong that water vapour could be cooled below the boiling-point . . . without condensing. It was on looking for some experimental illustration of the cooling of vapour in air below the temperature corresponding to the pressure that I thought that the dust in the air formed 'free surfaces' on which the vapour condensed and prevented it getting supersaturated." (Aitken 1880-81, 341-342)

Changes of state are caused by changes of temperature, but "something more than mere temperature is required to bring about these changes. Before the change can take place, a 'free surface' must be present." Aitken declared:

"When there is no 'free surface' in the water, we have at present no knowledge whatever as to the temperature at which these changes will take place. . . . Indeed, we are not certain that it is possible for these changes to take place at all, save in the presence of a 'free surface.' " (ibid., 339)

By a "free surface" he meant, somewhat tautologically, "a surface at which the water is free to change its condition." In an earlier paper, Aitken (1878, 252) had stated that a free surface was formed between any liquid and any gas/vapor (or vacuum), which would seem to indicate that he thought the point of contact between any two different states of matter (solid, liquid, or gaseous) constituted a free surface enabling changes between the two states involved. I am not aware whether Aitken ever developed of his concept of "free surface" in a precise way. As it turned out, the exact mechanism by which dust particles facilitated the condensation of vapor was not a trivial issue, and its elucidation required much theoretical investigation, especially on the effect of surface curvature on vapor pressure (for further details, see Galison 1997, 98-99, and Preston 1904, 406-412). It is unclear whether different kinds of "free surfaces" would have shared anything essential in the way they facilitated changes of state.

When applied to the case of boiling, Aitken's free-surface theory fitted very well with the De Luc-Donny-Dufour line of thought about the role of dissolved air in boiling (see the discussion of superheating), which he was quite familiar with. But his ideas did not necessarily go with the pressure-balance theory of boiling, and in fact Aitken actively rejected it: "The pressure itself has nothing to do with whether the water will pass into vapour or not" (1878, 242). Instead, he thought that what mattered for boiling was "the closeness with which the vapour molecules are packed into the space above the water." He re-defined the "boiling point" as follows: "the temperature at which evaporation takes place into an atmosphere of its own vapour at the standard atmospheric pressure of 29.905 inches of mercury." This definition is unusual, but may well be quite compatible with Cavendish's operational procedure adopted by the Royal Society Committee for fixing the steam point. Aitken recognized that his definition of the boiling point did not require any "boiling" in the sense of vapor rising from within the body of the liquid:

"Where, then, it may be asked, is the difference between boiling and evaporation? None, according to this view. Boiling is evaporation in presence of only its own vapour; and what is usually called evaporation is boiling in presence of a gas. The mechanical bubbling up of the vapour through the liquid is an accident of the boiling. . . . [W]e may have no free surface in the body of the liquid, and no bubbles rising through it, and yet the liquid may be boiling." (Aitken 1878, 242)

Aitken was clearly working at the frontiers of knowledge. But the fruit of his labors, as far as the theory of boiling was concerned, was only an even more serious disorientation than produced by De Luc's pioneering work on the subject a century earlier.

At the end of his major paper on dust and fogs, Aitken expressed his sense that he had only opened this whole subject:

"Much, very much, still remains to be done. Like a traveller who has landed in an unknown country, I am conscious my faltering steps have extended but little beyond the starting point. All around extends the unknown, and the distance is closed in by many an Alpine peak, whose slopes will require more vigorous steps than mine to surmount. It is with reluctance I am compelled for the present to abandon the investigation." (Aitken 1880-81, 368)

Well over a century after Aitken's humble pronouncement, we tend to be completely unaware that boiling, evaporation and other such mundane phenomena ever constituted "many an Alpine peak" for science. Aitken lamented that he had only been able to take a few faltering steps, but the vast majority of us who have received today's scientific education are entirely ignorant of even the existence of Aitken's unexplored country. (There are, of course, some specialists who know that the boiling and freezing of water are very complicated phenomena and investigate them through sophisticated modern methods. For an accessible introduction to the specialist work, see Ball 1999, part 2.)

Already in Aitken's own days, science had gone far enough down the road of specialization that even elementary knowledge became neglected if it did not bear explicitly on the subjects of specialist investigation. In an earlier paper Aitken blasted some respectable authors for making inaccurate statements about the boiling and melting temperatures. After citing patently incorrect statements from such canonical texts as James Clerk Maxwell's Theory of Heat and John Tyndall's Heat A Mode of Motion, Aitken gave a diagnosis that speaks very much to the spirit of my own work:

"Now, I do not wish to place too much stress on statements like these given by such authorities, but would look on them simply as the current coin of scientific literature which have been put in circulation with the stamp of authority, and have been received and reissued by these writers without questioning their value." (Aitken 1878, 252)

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