History of science index

Taken from the 2nd Volume of Joseph Priestley's
"Experiments and Observations on Different Kinds of Air"
(This edition of Priestley's work was published in 3 volumes in 1790. I have
tried to copy the original, page for page, as faithfully as possible.)

B O O K  IV.

P A R T 1.



An Account of the Discovery of dephlogisticated Air, 
and its general Properties.

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, at it tends greatly to encourage philo- sophical investigations; viz. that more is owing to what we call chance, that is, philosophically

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speaking, to the observation of events arising from unknown causes, than to any proper design, or preconceived 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 reconsider 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 between them, so as 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, biases not only our judgements, properly so called, but even the perceptions of our senses; for we may take a maxim so strongly for granted, that 
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the plainest evidence of sense will not entirely 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 in 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, according to my first hypothesis, 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, 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
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phlogifton than the air of the atmosphere; but 1 had no idea that such a composition was possible. 
    In my first publication on the subject of air, I mentioned that which I had got from nitre, and the account I then gave of it demonstrates it to have been dephlogisticated air, but I had not pursued that experiment, nor was it of any use to me in the following course. It may be worth while, however, to recite what I then observed, which was as follows. 
    All the kinds of factitious air, I then observed, on which 1 had made the experiment, were highly noxious, except that which is extracted from nitre, or alum; but in this even a candle burned just as in common air. In one quantity which I got from nitre a candle not only burned, but the flame was increased, and something was heard like a hissing, similar to the decrepitation of nitre in an open fire. 
    The air was extracted from these substances by heating them in a gun barrel, which was much corroded and soon spoiled by the experiment. What effect this circumstance had upon the air I did not consider. 
    At the time of my first 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
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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 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 work. 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, Pl. IV. which I filled with quicksilver, and kept inverted in a bason of the same. Mr. Warltire, a good chemist, 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 endeav- oured 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 surprised 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 got nothing like this remarkable appearance from any kind of air besides this particular modific- ation 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 dephlogisticated 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,
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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 
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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 surprise 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 sometimes 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, 
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a candle burned very strongly, and with a crackling noise.
    This experiment with red lead confirmed me more in my suspicion, that the mercurius calcinatus must: have got 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 any thing that 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 some 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 surprised me no 
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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 had observed that nitrous air, in this state, in some measure does.
    But I was much more surprised, 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 dephlogisticated 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 
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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, and the various modifications of air produced by spirit of nitre. 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, as I then thought, to the complete discovery of the constitution of the air we breathe.
    Till this first of March, I775, 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.
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    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.
    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 surprize, and others of similar import; but I must go on in that style a 
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little longer. For the next day I was more surprised 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
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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 but 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,
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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 four and a half to three and a half; 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 pro portion 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
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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 one and a half to two thirds 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 mea- sures of air extracted from mercurius calcinatus and
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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 this 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 
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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 the 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 concluded that it was between four and five times as good a common air. It will be seen that I have since procured air purer than this.