That air was not elementary was known or suspected before Priestley's time. John Mayow distinguished at least two components in atmospheric air, one which supported combustion and respiration and one which did not [Mayow 1674]. Before Priestley's work, chemists had to distinguish among "airs" (i.e., gases) for several were known, including "fixed air" (carbon dioxide), "mephitic air" (nitrogen), and "inflammable air" (hydrogen ). But Priestley "isolated and studied more new gases than any person before or since" in only a few years [Ihde 1964]. His researches began with the "fixed air" which formed over the fermenting mash at a brewery. While in the service of Lord Shelburne, Priestley studied "nitrous air" (nitric oxide), "dephlogisticated nitrous air" (nitrous oxide), "marine acid air" (hydrogen chloride), "alkaline air" (ammonia), "vitriolic acid air" (sulfur dioxide), "fluoro acid air" (silicon tetrafluoride), and "dephlogisticated air" (oxygen). Because Priestley did so much to demonstrate the multiplicity of "airs," it is fitting to examine an extract from his work as an illustration that air is not a simple substance.
Priestley was as orthodox in chemistry as he was unorthodox in religion in that he remained one of the last adherents of the phlogiston theory of combustion. (See note 5 below.) Ironically, the correct description of combustion involves oxygen, one of Priestley's discoveries. (See next chapter.) T√estley as a careful experimenter and candid observer in his first work on oxygen. At the same time, it shows some of the theoretical and observational limitations which prevented Priestley from recognizing the greater significance of his discovery.
The contents of this section will furnish a very striking illustration of the truth of a remark, which I have more than once made in my philosophical writings, and which can hardly be too often repeated, as it tends greatly to encourage philosophical investigations; viz. that more is owing to what we call chance, that is, philosophically speaking, to the observation of events arising from unknown causes, than to any proper design, or pre-conceived theory in this business. This does not appear in the works of those who write synthetically upon these subjects; but would, I doubt not, appear very strikingly in those who are the most celebrated for their philosophical acumen, did they write analytically and ingenuously.
For my own part, I will frankly acknowledge, that, at the commencement of the experiments recited in this section, I was so far from having formed any hypothesis that led to the discoveries I made in pursuing them, that they would have appeared very improbable to me had I been told of them; and when the decisive facts did at length obtrude themselves upon my notice, it was very slowly, and with great hesitation, that I yielded to the evidence of my senses. And yet, when I re-consider the matter, and compare my last discoveries relating to the constitution of the atmosphere with the first, I see the closest and the easiest connexion in the world between them, so as to wonder that I should not have been led immediately from the one to the other. That this was not the case, I attribute to the force of prejudice, which, unknown to ourselves, biasses not only our judgments, properly so called, but even the perceptions of our senses: for we may take a maxim so strongly for granted, that the plainest evidence of sense will not intirely change, and often hardly modify our persuasions; and the more ingenious a man is, the more effectually he is entangled in his errors; his ingenuity only helping him to deceive himself, by evading the force of truth.
There are, I believe, very few maxims in philosophy that have laid firmer hold upon the mind, than that air, meaning atmospherical air (free from various foreign matters, which were always supposed to be dissolved, and intermixed with it) is a simple elementary substance, indestructible, and unalterable, at least as much so as water is supposed to be. In the course of my inquiries, I was, however, soon satisfied that atmospherical air is not an unalterable thing; for that the phlogiston with which it becomes loaded from bodies burning in it, and animals breathing it, and various other chemical processes, so far alters and depraves it, as to render it altogether unfit for inflammation, respiration, and other purposes to which it is subservient; and I had discovered that agitation in water, the process of vegetation, and probably other natural processes, by taking out the superfluous phlogiston, restore it to its original purity. But I own I had no idea of the possibility of going any farther in this way, and thereby procuring air purer than the best common air. I might, indeed, have naturally imagined that such would be air that should contain less phlogiston than the air of the atmosphere; but I had no idea that such a composition was possible.
It will be seen in my last publication, that, from the experiments which I made on the marine acid air, I was led to conclude that common air consisted of some acid (and I naturally inclined to the acid that I was then operating upon) and phlogiston; because the union of this acid vapour and phlogiston made inflammable air; and inflammable air, by agitation in water, ceases to be inflammable, and becomes respirable. And though I could never make it quite so good as common air, I thought it very probable that vegetation, in more favourable circumstances than any in which I could apply it, or some other natural process, might render it more pure.
Upon this, which no person can say was an improbable supposition, was founded my conjecture, of volcanos having given birth to the atmosphere of this planet, supplying it with a permanent air, first inflammable, then deprived of its inflammability by agitation in water, and farther purified by vegetation.
Several of the known phenomena of the nitrous acid might have led me to think, that this was more proper for the constitution of the atmosphere than the marine acid: but my thoughts had got into a different train, and nothing but a series of observations, which I shall now distinctly relate, compelled me to adopt another hypothesis, and brought me, in a way of which I had then no idea, to the solution of the great problem, which my reader will perceive I have had in view ever since my discovery that the atmospheric air is alterable, and therefore that it is not an elementary substance, but a composition, viz. what this composition is, or what is the thing that we breathe, and how is it to be made from its constituent principles.
At the time of my former publication, I was not possessed of a burning lens of any considerable force; and for want of one, I could not possibly make many of the experiments that I had projected, and which, in theory, appeared very promising. I had, indeed, a mirror of force sufficient for my purpose. But the nature of this instrument is such, that it cannot be applied, with effect, except upon substances that are capable of being suspended or resting on a very slender support. It cannot be directed at all upon any substance in the form of a powder, nor hardly upon any thing that requires to be put into a vessel of quicksilver; which appears to me to be the most accurate method of extracting air from a great variety of substances, as was explained in the Introduction to this volume. But having afterwards procured a lens of twelve inches diameter, and twenty inches focal distance, I proceeded with great alacrity to examine, by the help of it, what kind of air a great variety of substances, natural and factitious, would yield, putting them into the vessels represented fig. a, which I filled with quicksilver, and kept inverted in a bason [sic] of the same. Mr. Warltire, a good chymist, and lecturer in natural philosophy, happening to be at that time in Calne, I explained my views to him, and was furnished by him with many substances, which I could not otherwise have procured.
With this apparatus, after a variety of other experiments, an account of which will be found in its proper place, on the 1st of August, 1774, I endeavoured to extract air from mercurius calcinatus per se; and I presently found that, by means of this lens, air was expelled from it very readily. Having got about three or four times as much as the bulk of my materials, I admitted water to it, and found that it was not imbibed by it. But what surprized me more than I can well express, was, that a candle burned in this air with a remarkably vigorous flame, very much like that enlarged flame with which a candle burns in nitrous air, exposed to iron or liver of sulphur; but as I had go nothing like this remarkable appearance from any kind of air besides this particular modification of nitrous air, and I knew no nitrous acid was used in the preparation of mercurius calcinatus, I was utterly at a loss how to account for it.
In this case, also, though I did not give sufficient attention to the circumstance at that time, the flame of the candle, besides being larger, burned with more splendor and heat than in that species of nitrous air; and a piece of red-hot wood sparkled in it, exactly like paper dipped in a solution of nitre, and it consumed very fast; an experiment which I had never thought of trying with nitrous air.
At the same time that I made the above mentioned experiment, I extracted a quantity of air, with the very same property, from the common red precipitate, which being produced by a solution of mercury in spirit of nitre, made me conclude that this peculiar property, being similar to that of the modification of nitrous air above mentioned, depended upon something being communicated to it by the nitrous acid; and since the mercurius calcinatus is produced by exposing mercury to a certain degree of heat, where common air has access to it, I likewise concluded that this substance had collected something of nitre, in that state of heat, from the atmosphere.
This, however, appearing to me much more extraordinary than it ought to have done, I entertained some suspicion that the mercurius calcinatus, on which I had made my experiments, being bought at a common apothecary's, might, in fact, be nothing more than red precipitate; though, had I been any thing of a practical chymist, I could not have entertained any such suspicion. However, mentioning this suspicion to Mr. Warltire, he furnished me with some that he had kept for a specimen of the preparation, and which, he told me, he could warrant to be genuine. This being treated in the same manner as the former, only by a longer continuance of heat, I extracted much more air from it than from the other.
This experiment might have satisfied any moderate sceptic: but, however, being at Paris in the October following, and knowing that there were several very eminent chymists in that place, I did not omit the opportunity, by means of my friend Mr. Magellan, to get an ounce of mercurius calcinatus prepared by Mr. Cadet, of the genuineness of which there could not possibly be any suspicion; and at the same time, I frequently mentioned my surprize at the kind of air which I had got from this preparation to Mr. Lavoisier, Mr. le Roy, and several other philosophers, who honoured me with their notice in that city; and who, I dare say, cannot fail to recollect the circumstance.
At the same time, I had no suspicion that the air which I had got from the mercurius calcinatus was even wholesome, so far was I from knowing what it was that I had really found; taking it for granted, that it was nothing more than such kind of air as I had brought nitrous air to be by the processes above mentioned; and in this air I have observed that a candle would burn sometime quite naturally, and sometimes with a beautiful enlarged flame, and yet remain perfectly noxious.
At the same time that I had got the air above mentioned from mercurius calcinatus and the red precipitate, I had got the same kind from red lead or minium. In this process, that part of the minium on which the focus of the lens had fallen, turned yellow. One third of the air, in this experiment, was readily absorbed by water, but, in the remainder, a candle burned very strongly, and with a crackling noise.
That fixed air is contained in red lead I had observed before; for I had expelled it by the heat of a candle, and had found it to be very pure. I imagine it requires more heat than I then used to expel any of the other kind of air.
This experiment with red lead confirmed me more in my suspicion, that the mercurius calcinatus must get the property of yielding this kind of air from the atmosphere, the process by which that preparation, and this of red lead is made, being similar. As I never make the least secret of anything I observe, I mentioned this experiment also, as well as those with the mercurius calcinatus, and the red precipitate, to all my philosophical acquaintance at Paris, and elsewhere; having no idea, at that time, to what these remarkable facts would lead.
Presently after my return from abroad, I went to work upon the mercurius calcinatus, which I had procured from Mr. Cadet; and, with a very moderate degree of heat, I got from about one fourth of an ounce of it, an ounce-measure of air, which I observed to be not readily imbibed, either by the substance itself from which it had been expelled (for I suffered them to continue a long time together before I transferred the air to any other place) or by water, in which I suffered this air to stand a considerable time before I made any experiment upon it.
In this air, as I had expected, a candle burned with a vivid flame; but what I observed new at this time (Nov. 19), and which surprized me no less than the fact I had discovered before, was, that, whereas a few moments agitation in water will deprive the modified nitrous air of its property of admitting a candle to burn in it; yet, after more than ten times as much agitation as would be sufficient to produce this alteration in the nitrous air, no sensible change was produced in this. A candle still burned in it with a strong flame; and it did not, in the least, diminish common air, which I have observed that nitrous air, in this state, in some measure, does.
But I was much more surprized, when, after two days, in which this air had continued in contact with water (by which it was diminished about one twentieth of its bulk) I agitated it violently in water about five minutes, and found that a candle still burned in it as well as in common air. The same degree of agitation would have made phlogisticated nitrous air fit for respiration indeed, but it would certainly have extinguished a candle.
These facts fully convinced me, that there must be a very material difference between the constitution of the air from mercurius calcinatus, and that of phlogisticated nitrous air, notwithstanding their resemblance in some particulars. But though I did not doubt that the air from mercurius calcinatus was fit for respiration, after being agitated in water, as every kind of air without exception, on which I had tried the experiment, had been, I still did not suspect that it was respirable in the first instance; so far was I from having any idea of this air being, what it really was, much superior, in this respect, to the air of the atmosphere.
In this ignorance of the real nature of this kind of air, I continued from this time (November) to the 1st of March following; having, in the mean time, been intent upon my experiments on the vitriolic acid air above recited, and the various modifications of air produced by spirit of nitre, an account of which will follow. But in the course of this month, I not only ascertained the nature of this kind of air, though very gradually, but was led by it to the complete discovery of the constitution of the air we breathe.
Till this 1st of March, 1775, I had so little suspicion of the air from mercurius calcinatus, &c. being wholesome, that I had not even thought of applying to it the test of nitrous air; but thinking (as my reader must imagine I frequently must have done) on the candle burning in it after long agitation in water, it occurred to me at last to make the experiment; and putting one measure of nitrous air to two measures of this air, I found, not only that it was diminished, but that it was diminished quite as much as common air, and that the redness of the mixture was likewise equal to that of a similar mixture of nitrous and common air.
After this I had no doubt but that the air from mercurius calcinatus was fit for respiration, and that it had all the other properties of genuine common air. But I did not take notice of what I might have observed, if I had not been so fully possessed by the notion of there being no air better than common air, that the redness was really deeper, and the diminution something greater than common air would have admitted.
Moreover, this advance in the way of truth, in reality, threw me back into error, making me give up the hypothesis I had first formed, viz. that the mercurius calcinatus had extracted spirit of nitre from the air; for I now concluded, that all the constituent parts of the air were equally, and in their proper proportion, imbibed in the preparation of this substance, and also in the process of making red lead. For at the same time that I made the above-mentioned experiment on the air from mercurius calcinatus, I likewise observed that the air which I had extracted from red lead, after the fixed air was washed out of it, was of the same nature, being diminished by nitrous air like common air: but, at the same time, I was puzzled to find that air from the red precipitate was diminished in the same manner, though the process for making this substance is quite different from that of making the two others. But to this circumstance I happened not to give much attention.
I wish my reader be not quite tired with the frequent repetition of the word suprize [sic], and others of similar import; but I must go on in that style a little longer. For the next day I was more surprized than ever I had been before, with finding that, after the above-mentioned mixture of nitrous air and the air from mercurius calcinatus, had stood all night, (in which time the whole diminution must have taken place; and, consequently, had it been common air, it must have been made perfectly noxious, and intirely unfit for respiration or inflammation) a candle burned in it, and even better than in common air.
I cannot, at this distance of time, recollect what it was that I had in view in making this experiment; but I know I had no expectation of the real issue of it. Having acquired a considerable degree of readiness in making experiments of this kind, a very slight and evanescent motive would be sufficient to induce me to do it. If, however, I had not happened for some other purpose, to have had a lighted candle before me, I should probably never have made the trial; and the whole train of my future experiments relating to this kind of air might have been prevented.
Still, however, having no conception of the real cause of this phenomenon, I considered it as something very extraordinary; but as a property that was peculiar to air extracted from these substances, and adventitious; and I always spoke of the air to my acquaintance as being substantially the same thing with common air. I particularly remember my telling Dr. Price, that I was myself perfectly satisfied of its being common air, as it appeared to be so by the test of nitrous air; though, for the satisfaction of others, I wanted a mouse to make the proof quite complete.
On the 8th of this month I procured a mouse, and put it into a glass vessel, containing two ounce-measures of the air from mercurius calcinatus. Had it been common air, a full-grown mouse, as this was, would have lived in it about a quarter of an hour. In this air, however, my mouse lived a full half hour; and though it was taken out seemingly dead, it appeared to have been only exceedingly chilled; for, upon being held to the fire, it presently revived, and appeared not to have received any harm from the experiment.
By this I was confirmed in my conclusion, that the air extracted from mercurius calcinatus, &c. was, at least, as good as common air; but I did not certainly conclude that it was any better; because, though one mouse would live only a quarter of an hour in a given quantity of air, I knew it was not impossible that another mouse might have lived in it half an hour; so little accuracy is there in this method of ascertaining the goodness of air: and indeed I have never had recourse to it for my own satisfaction, since the discovery of that most ready, accurate, and elegant test that nitrous air furnishes. But in this case I had a view to publishing the most generally-satisfactory account of my experiments that the nature of the thing would admit of.
This experiment with the mouse, when I had reflected upon it some time, gave me so much suspicion that the air into which I had put it was better than common air, that I was induced, the day after, to apply the test of nitrous air to a small part of that very quantity of air which the mouse had breathed so long; so that, had it been common air, I was satisfied it must have been very nearly, if not altogether, as noxious as possible, so as not to be affected by nitrous air; when, to my surprize again, I found that though it had been breathed so long, it was still better than common air. For after mixing it with nitrous air, in the usual proportion of two to one, it was diminished in the proportion of 41/2 to 31/2; that is, the nitrous air had made it two ninths less than before, and this in a very short space of time; whereas I had never found that, in the longest time, any common air was reduced more than one fifth of its bulk by any proportion of nitrous air, nor more than one fourth by any phlogistic process whatever. Thinking of this extraordinary fact upon my pillow, the next morning I put another measure of nitrous air to the same mixture, and, to my utter astonishment, found that it was farther diminished to almost one half of its original quantity. I then put a third measure to it; but this did not diminish it any farther: but, however, left it one measure less than it was even after the mouse had been taken out of it.
Being now fully satisfied that this air, even after the mouse had breathed it half an hour, was much better than common air; and having a quantity of it still left, sufficient for the experiment, viz. an ounce-measure and a half, I put the mouse into it; when I observed that it seemed to feel no shock upon being put into it, evident signs of which would have been visible, if the air had not been very wholesome; but that it remained perfectly at its ease another full half hour, when I took it out quite lively and vigorous. Measuring the air the next day, I found it to be reduced from 11/2 to 2/3 of an ounce-measure. And after this, if I remember well (for in my register of the day I only find it noted, that it was considerably diminished by nitrous air) it was nearly as good as common air. It was evident, indeed, from the mouse having been taken out quite vigorous, that the air could not have been rendered very noxious.
For my farther satisfaction I procured another mouse, and putting it into less than two ounce-measures of air extracted from mercurius calcinatus and air from red precipitate (which, having found them to be of the same quality, I had mixed together) it lived three quarters of an hour. But not having had the precaution to set the vessel in a warm place, I suspect that the mouse died of cold. However, as it had lived three times as long as it could probably have lived in the same quantity of common air, and I did not expect much accuracy from this kind of test, I did not think it necessary to make any more experiments with mice.
Being now fully satisfied of the superior goodness of this kind of air, I proceeded to measure that degree of purity, with as much accuracy as I could, by the test of nitrous air; and I began with putting one measure of nitrous air to two measures of this air, as if I had been examining common air; and now I observed that the diminution was evidently greater than common air would have suffered by the same treatment. A second measure of nitrous air reduced it to two thirds of its original quantity, and a third measure to one half. Suspecting that the diminution could not proceed much farther, I then added only half a measure of nitrous air, by which it was diminished still more; but not much, and another half measure made it more than half of its original quantity; so that, in this case, two measures of this air took more than two measures of nitrous air, and yet remained less than half of what it was. Five measures brought it pretty exactly to its original dimensions.
At the same time, air from red precipitate was diminished in the same proportion as that from mercurius calcinatus, five measures of nitrous air being received by two measures of this without any increase of dimensions. Now as common air takes about one half of its bulk of nitrous air, before it begins to receive any addition to its dimensions from more nitrous air, and this air took more than four half-measures before it ceased to be diminished by more nitrous air, and even five half-measures made no addition to its original dimensions, I conclude that it was between four and five times as good as common air. It will be seen that I have since procured air better than this, even between five and six times as good as the best common air that I have ever met with.
Being now fully satisfied with respect to the nature of this new species of air, viz. that, being capable of taking more phlogiston from nitrous air, it therefore originally contains less of this principle; my next inquiry was, by what means it comes to be so pure, or philosophically speaking, to be so much dephlogisticated; and since the red lead yields the same kind of air with mercurius calcinatus, though mixed with fixed air, and is a much cheaper material, I proceeded to examine all the preparations of lead, made by heat in the open air, to see what kind of air they would yield, beginning with the grey calx, and ending with litharge.
The red lead which I used for this purpose yielded a considerable quantity of dephlogisticated air, and very little fixed air; but to what circumstance in the preparation of this lead, or in the keeping of it, this difference is owing, I cannot tell. I have frequently found a very remarkable difference between different specimens of red lead in this respect, as well as in the purity of the air which they contain. This difference, however, may arise in a great measure, from the care that is taken to extract the fixed air from it. In this experiment two measures of nitrous air being put to one measure of this air, reduced it to one third of what it was at first, and nearly three times its bulk of nitrous air made very little addition to its original dimensions; so that this air was exceedingly pure, and better than any that I had procured before.
The preparation called massicot (which is said to be a state between the grey calx and the red lead) also yielded a considerable quantity of air, of which about one half was fixed air, and the remainder was such, that when an equal quantity of nitrous air was put to it, it was something less than at first; so that this air was about twice as pure as common air.
I thought it something remarkable, that in the preparations of lead by heat, those before and after these two, viz. the red lead and massicot, yielded only fixed air. I would also observe, by the way, that a very small quantity of air was extracted from lead ore by the burning lens. The bulk of it was easily absorbed by water. The remainder was not affected by nitrous air and it extinguished a candle.
Priestley admits that he stumbled upon many interesting phenomena by chance rather than by design. We should not be surprised that scientists frequently were surprised by their observations, for their observations and experiments were frequently not guided by hypotheses. (See chapter 3, note 4.) Although Priestley did work within a theoretical framework, the phlogiston theory, his course of experiments was not strongly guided by that framework. He went about characterizing new gases with little idea or expectation about what their properties would be.
Even though hypotheses now have a greater role in the design and interpretation of experiments than was the case in Priestley's day, chance and circumstance are still important. In this volume, we will examine the role of chance in the discovery of radioactivity (chapter 17). A popular account of chance in a wide variety of scientific discoveries may be found in Roberts 1989.
Even though Priestley did not design his experiments with his theoretical assumptions in mind, those assumptions nevertheless colored his expectations. Here he notes the disadvantage of a theoretical framework when it leads to incorrect expectations: those expectations can prevent or hinder understanding of an experiment, and lead to confusion. Ideally, however, such confusion would in turn lead an experimenter to reconsider the theoretical framework or at least not to rely on it. In Priestley's case, he did come to discard certain incorrect ideas, but he still held on to the phlogiston theory.
As noted above, the long-standing belief that air was an elementary substance was on its way out before Priestley's work. That belief in the elementary nature of water, however, was to persist for nearly another decade.
According to the phlogiston theory, combustible bodies contain a subtle fluid called phlogiston. (It is now known that there is no such material as phlogiston.) In the process of combustion, the burning body was believed to discharge its phlogiston into the air. Since the air could hold only so much phlogiston, burning would stop when the air becomes saturated with phlogiston. Similarly, animals were supposed to discharge phlogiston into the air when they breathed. Common atmospheric air was believed to contain little if any phlogiston, so it was believed to be most able to sustain combustion or respiration.
Another class of reactions "explained" by the phlogiston theory was the smelting of ores ("earths") and its reverse process, calcination. Earths were thought to be simple substances. In the process of smelting, an earth is heated in the presence of charcoal; phlogiston was believed to flow from the charcoal to the earth, producing a metal. The production of an earth from a metal can be brought about by the process of calcination, heating the metal in open air; the phlogiston was believed to flow from the metal into the air, converting the metal back into an earth or calx. See White 1932 for a history of the phlogiston theory.
Priestley knew that water could "purify" air, making it more fit for respiration and combustion; perhaps, he speculated, this process could make the air more "pure" than ordinary atmosperic air. He noted on another occasion that a green substance in the water was necessary for this purification of the air. The Dutch physician Jan Ingenhousz published observations which further elucidated the phenomenon: the green matter was plant material, and light was necessary for the "purification" to occur [Ingenhousz 1779]. The process is now known as photosynthesis: the reaction of carbon dioxide and water in green plants in the presence of light to produce oxygen and complex carbon-containing compounds which are incorporated into the plant.
Priestley's speculation bears some similarity to what earth scientists currently believe about the origin of the atmosphere. Oxygen is not abundant among the gases emitted by volcanoes. Oxygen is a product of photosynthesis by plants, primarily in the oceans: as plant life became more abundant, so did oxygen in the atmosphere.
Back to Priestley's idea that air is a compound of phlogiston and an acid. His first thought was that the acid was "marine acid." Next he thought it was "nitrous acid." What Priestley called nitrous acid is now called nitric acid (HNO3); what is now called nitrous acid is HNO2. In any event, the idea was completely mistaken: the atmosphere is primarily a mixture (not a compound) of nitrogen (N2) and oxygen (O2), neither of which is an acid.
Priestley emphasizes the importance of having the right tools. Several of the right tools for investigating gases in the late 18th century are shown in this engraving from Experiments and Observations on Different Kinds of Air. These include a basin containing mercury or water for the collection of gases. A gas could be trapped by allowing it to pass through a tube into an empty container whose open end is submerged in a liquid. (Imagine collecting one's breath by blowing through a straw into a glass turned upside-down in a basin of water.) Many common gases can dissolve in water but not in mercury, so mercury was often employed in collecting gases. A burning lens or burning glass is an optical lens which could concentrate the rays of the sun onto a small spot, providing rather intense heat and light to a small area. A mirror could also concentrate sunlight; however, the object on which the light is to be focused cannot be too large, or it would block the original sunlight from reaching the mirror. View a picture of Priestley's burning lens (at the Edgar Fahs Smith collection, University of Pennsylvania) and a diagram of a huge one Lavoisier used (at Les Amis de Lavoisier).
John Warltire lecturer in natural history at Birmingham, was a longtime associate and collaborator of Priestley's.
Once he obtained the proper equipment, Priestley's plan as to use the burning lens to heat several different materials and to collect over mercury any "airs" which might be given off. One of those materials was mercuric oxide, HgO, then known as mercurius calcinatus per se. Mercurius calcinatus, literally "calcined mercury," was prepared by heating mercury in the presence of air; in modern terms, the mercury reacts with oxygen in the air:
2 Hg + O2 --> 2 HgO .Upon being heated, the mercuric oxide gave off a gas, namely oxygen, and regenerated the mercury.
Once he collected enough of the gas to work with (about three or four times the volume of the mercuric oxide he started with), Priestley begins to characterize the gas, to test its properties. The gas is not appreciably soluble in water, he discovers by bringing water into contact with the gas and observing no decrease in its volume.
Liver of sulphur is a material formed from the fusion of potassium carbonate and sulfur. The resulting solid is a reddish-brown mass consisting of potassium thiosulfate (K2S2O3) and potassium polysulfides.
The observation which catches Priestley's attention is that this gas supports combustion more vigorously than ordinary air. He goes on to mention that he had obtained similarly vigorous combustion (but not quite this vigorous) under other circumstances, but that the present case involves different materials. "Nitrous air" is now known as nitric oxide, NO. Nitric oxide is fairly reactive, and left to stand in the presence of iron, it turns into another gas, nitrous oxide, N2O:
2 NO + Fe --> FeO + N2O .The same sort of transformation of NO to N2O can also be effected by contact with the potassium thiosulfate in liver of sulfur:
6 NO + K2S2O3 --> K2S2O8 + 3 N2O .N2O supports combustion, but not respiration. [Conant 1957, pp. 90-1]
The red precipitate is formed from the reaction of nitric acid solution ("spirit of nitre") with mercury; in modern terms, the reaction is:
Hg + 2 HNO3 --> HgO + 2 NO2 + H2O .Red precipitate is the same substance as mercurius calcinatus. Both are now called mercuric oxide, HgO. They had different names because they were prepared by different means, and not yet known to be the same substance. Certainly Priestley writes as if they were different materials. Mercuric oxide serves as an excellent example of the nomenclature reforms Lavoisier was to make a decade after this work of Priestley's. (See previous chapter.) The term mercuric oxide, which follows Lavoisier's nomenclature, describes the composition of the subject. The older terms, which Priestley uses, suggest that there are two different substances; one name describes the method of perparation (calcination of mercury), while the other alludes to a superficial property (its red color) as well as its preparation (a precipitation reaction).
Priestley knew that the "spirit of nitre" he used to prepare the red precipitate, and the modified "nitrous air" of which the new gas reminded him, were related. (We would say that both are nitrogen-containing compounds; even the names Priestley used suggest some sort of relationship.) So he thought the new gas obtained from the red precipitate may be modified "nitrous air" produced by some residual "spirit of nitre" in his red precipitate. (This is incorrect, for the red precipitate contains no nitrogen). And he thought that the mercurius calcinatus also contained a nitrogenous component.
Priestley shows some concern here for the purity of his materials, or at least for their integrity. He suspected that the mercurius calcinatus he had bought for his original experiment might really be red precipitate (not knowing, of course, that the two materials were actually the same). So he got yet another sample of mercurius calcinatus, one he knew was not prepared using anything related to nitrous air, and obtained the same new gas from it. Purity of materials was an important issue for chemists at the time, and it continues to be. Priestley's subsequent experiments on airs released from calces were plagued by problems of purity. See, for example, notes 19 and 36 below and Conant 1957, p. 103.
The interaction of scientists and their ideas is important to the development of science. We shall see in the next chapter that Lavoisier was able to understand the significance of the gas obtained by heating mercurius calcinatus.
Lavoisier carried out some similar experiments on mercurius calcinatus beginning in November 1774, and reported his results to the French Academy in spring 1775 [Lavoisier 1775]. In reporting these experiments, Lavoisier did not mention either Priestley's work or the communication from Priestley concerning it. [Conant 1957, p. 89]
The terms wholesome and noxious refer to the fitness of the gas to breathe, to its ability or inability to support respiration.
Red lead or minium are both names for a particular lead oxide, Pb3O4. Heating a pure sample of this substance drives off some of the oxygen, leaving a different lead oxide, a yellow solid:
2 Pb3O4 --> 6 PbO + O2 .The fact that Priestley observed a substantial fraction of the gas dissolve in water suggests that he had an impure sample of minium, one contaminated significantly by lead carbonate, PbCO3. Heating this material would produce carbon dioxide (CO2, "fixed air"), which readily dissolves in water.
Notice the formulation of successive hypotheses concerning the source of the new gas. Minium and mercury calcinatus are both products of heating metals in the presence of atmospheric air; red precipitate is the product of a chemical reaction in solution. Heating all of these products yields the same gas. Where does that gas come from? Not the "spirit of nitre," from which red precipitate is prepared. Maybe, reasons Priestley, it comes from common air, which is involved in the preparation of the other two materials. This is plausible, and it turns out to be correct (although certainly not yet proved).
Turning again to the characterization of the new gas, Priestley notices several respects in which the new gas differs from N2O, or "dephlogisticated nitrous air" as he calls it here. These differences in behavior result from the difference in solubility between the N2O and the new gas, oxygen. N2O is quite soluble in water, so agitation in water would have dissolved it, removing from whatever gas remained the ability to support combustion. Oxygen, on the other hand, did not dissolve to an appreciable extent. Priestley concludes that the difference in behavior implies a difference in constitution between N2O and the new gas.
That is, Priestley still did not realize that the new gas was respirable right away, even without "purification" by water.
The "test of nitrous air" was a test for the "wholesomeness" or "purity" of air which Priestley developed when he thought that there was no gas more fit for respiration than common air. The test involved mixing nitrous air (NO) with twice as much by volume of the gas to be tested, in an inverted vessel over water. If the air was fit to breathe, one would observe red fumes over the water; then the fumes would disappear as the water rose in the vessel. The test could even be quantitative. If the test gas was pure atmospheric air, then adding one unit of NO to two units of atmospheric air would result in 1.8 units total of residual gas. [Conant 1957, pp. 74-6]
Priestley tried the nitrous air test on the new gas, and obtained a result similar to what would be observed for common air. This result led Priestley astray, for he did not know the composition of nitrous air and therefore did not understand the basis for the test. "Nitrous air" (NO) reacts quickly with oxygen, producing a reddish gas (NO2) which dissolves readily in water:
2 NO + O2 --> 2 NO2 .Common air is a mixture of roughly 80% nitrogen (N2) and 20% oxygen (O2). When one unit of NO is mixed with 2 units of common air, all of the oxygen present (0.4 units) reacts with most of the NO (0.8 units) producing reddish fumes. Only 1.8 volumes of gas remains of the original two units of common air and one of NO; most of it is nitrogen (1.6 units) and the remainder is excess NO.
When Priestley tried the test by mixing two volumes of the new gas (oxygen) with one of NO, there was more than enough oxygen present to react with all the NO, producing red fumes and leaving behind 1.5 units of gas, all oxygen. In other words, what happens when pure oxygen is tested looks a lot like what happens when common air is tested, and this misled Priestley into thinking his new gas was common air. [Conant 1957]
What happens when pure oxygen is tested looks a lot like what happens when common air is tested, but not exactly the same. If Priestley had been looking closely for differences in the first place, he would have seen slightly more red fumes generated from oxygen and slightly less residual gas. He went back and compared the test results (using new samples, of course) after he realized the new gas was not common air. This is where he writes that he was biased by his preconceptions into not seeing evidence that was before his eyes (near note 3 above).
That is, Priestley now thinks that the new gas is not just a component of atmospheric air, but a sample of atmospheric air itself. To recap the progression of his hypotheses: maybe the gas comes from nitre; no, maybe it is something nitrous from the air; it is not "nitrous air"; no, it seems to be common air itself.
A reader accustomed to modern scientific communications cannot fail to notice Priestley's refreshing candor. Modern journals and monographs try to tightly conserve space (and even so, scientific journals publish a seemingly limitless but ever-increasing number of articles). The contemporary scientific style is terse, concentrating on observations to the extent that the observer practically vanishes. It is rare for a modern scientist to admit surprise--even if he or she would want to do so--let alone to admit surprise at every turn and to describe wrong turns!
By trying to burn a candle in the residual gas, Priestley carries out a test that distinguishes his new gas from common air. If the new gas had been common air, the remaining gas would have put out the candle (for it would contain no oxygen); instead, the residual gas made the candle burn even more brightly than normal (for it was nearly pure oxygen). With the convenience of 200 years of hindsight, I would say this test shows decisively that the new gas was not common air. Yet Priestley clearly did not yet come to that conclusion.
Burning this candle, by the way, appears to be the event Priestley says above (near note 2) happened by chance. It was not exactly accidental, but it was serendipitous in that it was done for no good reason.
Priestley is well aware that individuals are highly variable in their reactions, so much so that he could not be sure that the difference in the times two mice stayed alive was a significant difference, a difference which signified a difference in the quality of the air. The phenomenon of individual variability is one with which life scientists and social scientists must seriously contend. Physical scientists, by contrast, frequently have the luxury of working with enormous samples of identical subjects (for even small samples can contain millions of billions of atoms or molecules). The issue of when observed differences are significant is taken up in more detail in chapter 14.
The effect of the mouse on the atmosphere of pure oxygen would be mainly to replace some of the oxygen with carbon dioxide and water vapor. The air that an animal exhales contains more carbon dioxide and slightly less oxygen than the air it inhales. That is, an animal breathes out nearly all the oxygen it breathes in, but it exchanges some of that oxygen for carbon dioxide. In any event, carbon dioxide is soluble in water, so it is likely that the gas tested after the mouse breathed in it was still mostly oxygen. The nitrous air test performed on the residual gas if the original gas was mostly oxygen, would look like the original test. By contrast, if the original gas had been common air, carrying out the nitrous air test on the residual gas would produce no red fumes and no decrease in the amount of gas, for the original test would have used up all the oxygen present in common air.
That is, only by mixing two units of the new gas with five units of NO does one get two units of residual gas. In this case, the residual gas is mostly excess NO left after nearly all the oxygen reacts. Recall that if the test gas were common air, mixing two units of the test gas with one of nitrous air would have resulted in nearly two units of residual gas, mainly nitrogen.
Since common air is about 20% oxygen, pure oxygen is about five times as good as it is for respiration and combustion. That is, a given volume of pure oxygen contains five times as much oxygen as that same volume of common air.
Up to this point, Priestley has discovered and characterized a new gas, whose main characteristic is that it supports combustion and respiration even better than common air. Note that he has not shown it to be an element. He has not even decisively shown that it is a component of atmospheric air, although he has made a plausible argument for that opinion.
Since the new gas is better able to support combustion, Priestley assumes it has less phlogiston than common air. Remember that in the phlogiston theory, combustion stops when the air can hold no more phlogiston from the burning object (note 5). In his mind the nitrous air test also involves the transfer of phlogiston from nitrous air to the test gas.
There are several distinct oxides of lead, that is several different compounds of lead and oxygen. The grey calx of lead is Pb2O. Litharge and massicot are both yellow lead oxides whose formula is PbO. (They are different substances, however, with different crystal structures.) We have already met red lead, Pb3O4. Two other oxides of lead do not enter into this story: Pb2O3 and PbO2. Note that the ratio of oxygen to lead atoms in this series of compounds ranges from 1:2 to 2:1. Heating lead in the open air, we understand now, will allow the lead to combine with oxygen; more heating or more oxygen would allow the grey calx to be formed first, and then the higher lead oxides. (Unfortunately, this process also produces lead carbonates; the end product of heating in open air is not a chemically pure oxide, but a mixture of oxides and carbonates. See next note) Priestley decided to try heating several of these lead calces to see if he would obtain the same gas which he got from red lead.
This statement is a sign that the samples Priestley used were not very pure. We have already noted (note 19) that his red lead contained carbonates and that heating lead in open air generally produces carbonates as well. As a result, Priestley obtained inconsistent results, for heating a mixture of lead oxides and lead carbonate will produce a mixture of oxygen and carbon dioxide ("fixed air"). The interfering effects of the carbon dioxide prevented Priestley from accumulating the consistent and convincing data that would have been necessary for him to see that the new gas was an integral part of the calcination of metals. Given Priestley's adherence to the phlogiston theory [Priestley 1796], only clear and overwhelming evidence (if that) would have allowed him to come to such a conclusion; indeed, when Lavoisier arrived at it (See next chapter.), Priestley was still unconvinced. [Conant 1957, Giunta 2001]
The tests Priestley describes are certainly indicative of "fixed air" (CO2), which dissolves quite readily in water, does not support combustion, and does not react with "nitrous air".