XIX .
On the mean density of the Earth .
By Dr. CHARLES HUTTON , F. R. S. Read April 5 , 1821 .
A LT HOUGH the determination of the mean density of the whole terraqueous globe of our planet , is admitted to be a problem of the utmost importance to several branches of philosophy , particularly to physical astronomy , and the figure and constitution of the earth ; it would seem , from the discordancy of the declared opinions of some eminent philosophers , that the problem is still in an uncertain state .
Since the first notice of this subject by NEWTON , in his admirable Principia , it has often been incidentally alluded to , without receiving a precise determination ; with the exception of two instances only , in which it has been stated to be , certainly or approximately , determined by experiment ; namely , in the case of the Schehallien experiment , by Dr. MASKELYNE and myself , and by the Honorable HENRY CAVENDISH , by a method invented by Mr. MICHELL .
The former of these experiments was made by Dr. MASKELYNE , in the years 1774 , 1775 , and 1776 , by means of that large mountain in Scotland , in measuring its dimensions , and in comparing its attraction on a plummet , with that of the whole earth on the same ; the calculations on it having been made by myself , and first published in the Philosophical Transactions of the year 1778 ; and since more correctly in the second volume of my Mathematical Tracts .
The other experiment , by Mr. CAVENDISH , was by observing the attraction on small pendulous balls , of two inches diameter , by larger ones of ten inches diameter , as compared with the attraction of the earth on the same .
By some strange mistake , or perversion , for many years , it was customary among certain persons , to withhold the mention of my name , with regard to the great share that I had in the experiment on Schehallien .
But from certain complaints which I have made , some little justice has lately been awarded to me on that head ; though still , it would seem , with reluctance , as the opinion is promptly assumed that the latter small experiment is susceptible of the greater accuracy , and the numbers in its result gratuitously adopted as nearer the truth than that of the former .
As this is an opinion which I have never been able to bring my mind to acknowledge , and as it is a matter of great importance in the present state of physics , I have been desirous to draw the attention of philosophers to a closer consideration of the subject , with a view to a more deliberate and impartial decision of this point .
From the closest and most scrupulous attention I can employ on this question , the preference , in point of accuracy , appears to be decidedly in favour of the large or mountain experiment , over that of the small balls .
It is indeed true , that though the large mass of the mountain must yield an immensely greater force than a small ball , yet it may be said that this advantage must be balanced , either wholly or in great part , on the score of distance , as the plummet is acted on at a great distance from the centre of the mountain , while the balls are approached very near together ; so that the visible effects may thus be nearly equal , by the reciprocal balancing between magnitude and distance .
Hence the visible effect of the mountain , is that of the small angle of eleven or twelve seconds , by which the plummet is drawn aside from the perpendicular ; thereby showing that the attraction of the earth , on the plummet , is to that of the mountain on it , as radius is to the tangent of those seconds ; while , in the other experiment , the small pendulous balls are drawn aside by the large ones the space of between one-seventh and twothirds of an inch ; the distance of each ball from the middle of their connecting rod , being a little more than thirty-six inches .
The first or immediate small results of the two experiments , thus appearing so far to be about equally favourable , it will be necessary to examine the circumstances of each of them separately , that we may be able to judge more particularly of their merits ; and , first , of the Schehallien experiment .
This experiment , it is well known , was conducted by the late Astronomer Royal , Dr. MASKELYNE , than whom a more correct , faithful , and experienced individual probably never existed .
The account of his measures and observations , taken in conducting it , is minutely detailed in the Philosophical Transactions of the year 1775 , or in my edition of the Transactions , vol. xiii , page 702 ; where all the instruments and operations are particularly described , in the most plain and satisfactory manner .
The principal instrument was the ten foot zenith sector ; with which the meridian zenith distances of forty-three stars by three-hundred and thirty-seven observations , were carefully taken , both on the north and south sides of the mountain .
The medium of all these , with s78 other necessary measures , gave a final result of 1.6 seconds , for the sum of the deviations of the plumb line , on both sides of the mountain ; and that , in all probability , within much less than half a second of the truth .
Other instruments used , were the Royal Society 's transit instrument made by Mr. BIRD , and an astronomical clock by SHELTON , which had both been provided on occasion of the observations on the transit of Venus , in 1761 or 1769 .
Besides these and several other instruments , one of RAMSDEN'S best theodolites was used , in measuring the figure and dimensions of the mountain , which was performed in the most correct manner by skilful surveyors ; so as that thence an exact model of it might be made , or all its dimensions accurately taken , for computing the attraction .
By only reading over the accounts of these operations , ( in the places before mentioned ) made by means of such instruments , and in such hands , every person must be convinced of the impossibility that any error could have been committed , capable of causing any sensible inaccuracy in the conclusion of the work .
It remains now to describe the share which I bore in this important business ; which consisted in taking all the measurements as above described , and from those data , calculating what must have been the exact magnitude of the mountain ; what its attraction on the plummet , relatively to that of the globe of the earth on the same ; and what must be the mean density of the earth .
These computations , which employed my daily and assiduous labours during the greater part of two years , are recorded in the Philosophical Transactions of the year 1778 , and also in the second volume 279 of my Mathematical Tracts .
It may there be seen , that after computing , trigonometrically , the bearing and distance of every point in the numerous sections of the mountain , from the two observatories , I conceived it to be divided into nearly one thousand vertical columns , of given bases and altitudes .
I then computed the quantity of the attraction of all these columns , on the plummet , in the direction of the meridian , when placed at the two observatories , on both sides of the hill , where the whole effect had been observed , which attraction was thus found to be expressed by the number 8811i .
I then computed , from the magnitude of the earth , what must be its attraction on the same plummet , and found it expressed by the number 8752272o .
Consequently , the whole attraction of the earth , is to the sum of the two contrary attractions of the mountain , as the number 8752272o to 8811i ; that is , as 9933 to i very nearly ; on supposition that the density of the matter in the hill , is equal to the mean density of that in the earth .
But Dr. MASKELYNE found by his observations , that the sum of the deviations of the plumb line , produced by the two contrary attractions , was 11.6 seconds .
Hence then it is inferred , that the attraction of the earth , is actually to the sum of the attractions of the hill , nearly as radius to the tangent of 11.6 seconds , that is , as 1 to.000oooo5629 , or as 17781 to 1 ; or as 17804 to 1 nearly , after allowing for the centrifugal force arising from the rotation of the earth about its axis .
Having now obtained the two results , namely , that which arises from the actual observations , and that due to the computation on the supposition of an equal density in the two 28o bodies , the two ratios compared , must give the ratio of their densities , and which is therefore that of 17804 to 9933 , or 1434 to 800 nearly , or almost as 9 to 5 ; and so much does the mean density of the earth exceed that of the hill .
Con .
sequently , if we know the density of the latter , we shall thence obtain that of the former .
At the time when this computation was first printed , in the year 1778 , the real density of the hill was unknown .
It was only known that it consisted chiefly of very hard and dense rocks , much heavier than common stone , which is allowed to be 4 times the density of water .
I then , by way of example in applying the density , multiplied 9 by 2 , which produced I or 4for the density of the earth , on the smallest assumption ; till such time as we should come to know more nearly what the real density of those rocks is : and therefore I must feel reason to complain , tha this number ( 41 ) has often been stated , rather unfairly , as my final conclusion for the earth 's mean density ; instead of being only the very lowest limit that might be used , till we could better learn something on that point with more certainty .
But a lithological survey of the mountain being afterwards accurately made , at my earnest request , by that excellent philosopher and geologist , Mr. PLAYFAIR , the result of which was published in the Philosophical Transactions for the year 1811 ; I then applied his mean statement of the rocks to my own calculations , which gave me the number 5 for the density of the earth ; as I published in the fourteenth volume of my edition of the Philosophical Transactions , and in the second volume of my Tracts .
in Mr. PLAYFAIR 's account of the mountain , are given the 28i names and nature of the several rocks that compose it , with tables or lists of their densities or specific gravities .
In one table is a list of thirteen specimens of densities , contained between the numbers s.6109 and 2.6656 , the medium of the whole being 2.639876 .
In another table , of fifteen specimens , the densities are limited between 2.71845 and 3.o642 , the medium of all which is 2.81039 .
And the mean between these two means , gives t.725 for the medium density of the whole mountain , admitting it to be quite solid , or without vacuities , as it appears to be on the exterior surface at least .
But in the calculation in my Tracts I went even a little higher , using the number 2.75 or 2- , thus 9x 21- , which gives i9 or 4.95 for the mean density of the earth .
Or , if we assume the density of the mountain still higher , as 2.8 instead of 2.75 , we then obtain 9x 2.8 = 5F.5 , a little more than 5 for the earth 's density ; which last number 5 , I therefore fix upon , in conclusion , as probably the nearest to the truth ; or at least it is sufficiently large , as it is grounded on several assumptions that are most favourable for the highest result ; namely , 2.777714 , or 2for the density of the mountain ; also .
as rather above the calculated ratio of the densities of the earth and mountain ; and lastly , the assumption of the mountain being quite solid ; though it is probable that there may be cavities in most mountains , as they are generally the production either of volcanoes , or of earthquakes .
For all these reasons , then , it is highly probable , that the earth 's mean density is very near five times the density of water ; but not higher .
If any person should still hesitate to adopt this conclusion , his hesitation must arise from doubts either on the data obtained by the measurements , or on the e8a accuracy of the computations made from them .
But if any such person attentively read over Dr. MASKELYNE'S account of the measurements , in the Philosophical Transactions of 1775 , his doubts must be soon removed , as to the data supplied by the survey of the hill , or by the astronomical observations .
And as to the accuracy of my own computations , made from those data , they are fully and fairly before the public , in the works before mentioned ; and let any person , who doubts , look over and repeat the calculations there stated , and try if he can find any inaccuracy in them .
The only possible ground of doubt in the measured data , must be in the observed deviation in the plumb line , taken by Dr. MASKELYNE ; but when we consider the accuracy of the observer , and of the instruments , and read the account of the use of them , it must be then very difficult to doubt of their accuracy .
On this point it is commonly acknowledged that a good observer , with the best instruments , can observe angles to a small fraction of a second .
Dr. MASKELYNE'S observations give 11.6 seconds for the sum of the deviations of the plumb line , from a medium of between 300 and 400 observations .
Now let us suppose it possible to hav'e committed an error of four tenths of a second in this number , and that the true number should have been is seconds , instead of 11.6 , being an error of the twenty-ninth part of the whole .
This then would cause an error of the 92th part of the result ; which would reduce the density 5 to about 4.8 ; showing that the number 11.6 is not too small , but may be the contrary .
Next , let us assume 11 seconds only , omitting the six-tenths , being almost the twentieth part of the whole , and which therefore would give nearly 5.25 for the earth 's density , being still far below the number 5.48 , as deduced from Mr. CAVENDISH'S experiment .
Hence it appears , that our result cannot be made to agree with that of Mr. CAVENDISH , unless our 1i.6 seconds be diminished to about 1o.5 or 1o.4 , on the supposition of an error of more than a whole second in excess , in the number 1i.6 seconds ; which cannot be admitted , without doing great violence to the observations .
Having thus failed in our endeavour to discover any error , or even suspicion of error , in the conduct or result of the Schehallien experiment , let us now turn our attention to the other experiment , as performed by Mr. CAVENDISH .
And here I must at once disclaim all expectation of meeting any failing with regard to the operator himself , whom I well knew to be a most excellent philosopher and mathematician , as well as a patient , accurate , and acute experimenter .
The failure then , if any , must be expected from the nature of the machine , and of the calculations .
From the perusal of Mr. CAVENDISH'S account of the machine he employed ( in the Philosophical Transactions of 1778 , or vol. xviii .
of my edition ) , and the nature of the arithmetical calculations , they at once appear to be formidable and discouraging in the highest degree .
The machine is small , comparatively with those in the former , or mountain experiment .
It is not easily to be understood , without actually seeing it , though assisted with the view of the drawing of the whole , on account of the intricacy and perplexity of the construction .
In the first place , at each end of a light wooden rod , of near'two yards in length , is attached a small leaden ball of two inches diameter ; the middle of the rod being fixed to and suspended by a long and very slender 884 copper wire ; by any small movement of these balls and the connecting rod , in a horizontal direction , by the torsion or twisting of the wire , a very minute and slow vibratory motion is commenced .
To produce this small motion in the two little balls , and their connecting rod , two other large balls of ten inches diameter , are connected together by certain machinery , at like distance as the former , and capable of being moved to different distances on the horizontal level with the small balls .
By so setting the large balls near the small ones , these are attracted by the former , producing a very small motion in them , and in consequence a very slow vibration .
So minute are these motions , that the extent of the vibrations is but a small fraction of an inch , and the duration of each vibration is not performed but in the time of several minutes , from three or four to near fifteen minutes .
So minute are these motions , that telescopes and other means are necessary to view and to estimate their quantity and durations .
'ro produce these minute motions , very complex machinery are necessarily employed , while the delicate movements are watched for many hours together , during many days , and recorded with regard to the extent and time of each vibration .
Then , from these spaces and times , the density of the earth is to be calculated , by peculiar theorems , as compared with the vibrations of common pendulums that are produced by the attractions of the earth .
All these effects were so minute , and produced by machinery so complex , and the results calculated by theorems derived from intricate mathematical investigations , that it is impossible , at first , for ordinary readers to conceive how any accurate results can be deduced from them ; and even for the more judicious reader to place confidence in them , except chiefly on account of the high character of the experimenter himself .
From the nature of the machinery , I could therefore derive no confidence in the results , nor compare them with the mountain experiment , without repeating the whole of the calculations .
But , after a long life spent in almost daily abstruse investigations , from the tenth year of my age , and now being at eighty-four , and oppressed with distressing illness , I thought I might be excused from such a task .
But , after urging more than one mathematical friend , without being able to interest them sufficiently to engage in so severe an operation , my anxiety to accomplish the business induced me to make an exertion to effect it myself ; especially as the learned experimenter informs us , that he availed himself of the assistance of the then clerk of the Society , who he says made some of the experiments , and who doubtless made most of the arithmetical computations : operations , of both kinds , in which I remember he was much employed by Sir CHARLES BLAGDEN , and other gentlemen , in preparing their papers for the Royal Society .
I have therefore recomputed all the experiments , and have traced the investigations of all the theorems ; and have found that my labour has not Leen in vain ; but , on the contrary , has been rewarded with the following copious list of errata , some of which are large or important .
In the following instances it is to be noted , that the references are made to Mr. CAVENDISH'S paper , as printed in my edition of the Philosophical Transactions , as I am not now possessed of a set of the original edition ; but with which , however , I have had my own set compared and verified .
a86 Some of the errata in Mr. CAVENDISH'S paper .
In page 399 , line io from the bottom , for 8739000 , read 8740000 .
In page 399 , line 6 b , or from the bottom , for 8739000 , read 87400oo .
The same also in line 5 b. In page 399 , line 4 b , for o1683 read 1o685 .
The same also in line i b. In page 403 , lines 1i and 13 , for 8739000 , read 8740000 .
---..- ... line 13 , for 10844 , read lo847 .
-------..--- ... .
for o1683 , read io685 , In page 404 , line 11 , for 185 , read i86.5 .
_.------lines 15 16 , , 25 , for 185 , read i865 .
It is to be noted , that after the experiments have been all made , and the motion of the arm carrying the small balls , and expressed in twentieths of an inch , observed and denoted by the letter B ; also the time of one vibration , expressed in seconds , denoted by the letter N ; and both of these being corrected according to certain rules there given , then the mean density of the earth D , in each experiment , is to be computed by this theorem , viz. D o , or when corrected , D= 1063 B &gt; io68s B And by this theorem erecalculted the following twentynine experiments , as they stand recorded in the original .
287 Table of the results of the experiments .
x-Ei E Motion of The same Time of Ditto The Pents the arm .
corrected .
vibration .
corrected .
Density .
ments.1 3456789 10 11 12 13 14 15 16 17 18 19 20 21 22 23 24 25 26 27 28 29 2oths .
Inc. 14.32 14 .
1 15.87 15-45 15.22 14.5 S. 1 6.i8 5.92 5 ' 9 5.98 3-.03 5 .
9 3.15 6 .
i 3.13 5.72 6.32 6.15 6.07 6.09 6.12 5.97 6.27 6.13 6.34 6 .
' 5.78 5.64 zoths .
Inc. 13.42 13.17 14.69 14.14 13.56 13.28 2.95 2.9 5.71 3.03 5.9 3.00 5.54 M. S. 1455 14 42 14 39 14 54 717S 75 757 By 4 mean .
6 58 659 717376777676777 i6 7273 654 6 57 J 5.50 5.6i 4.88 5-07 5.26 5.55 5.36 5.29 5-58 5.65 5.57 5.53 5.62 5.29 5.44 5.34 5.79 5.10 5.27 5.39 5.42 5.47 5.63 5.34 5.46 5.30 5.75 5.68 5.85 The last column shows the numbers for the required density , resulting from the calculation by the foregoing theorem , 288 i i being all a little above 5 , excepting the third number , which is a little below 5 .
And immediately after , is the following remark , showing the author 's doubt of their accuracy ; viz. " From this table it appears , that though the experiments " agree pretty well together , yet the difference between them , " both in the quantity of motion of the arm , and in the time of vibration , is greater than can proceed merely from the error of observation .
As to the difference in the motion of " the arm , it may very well be accounted for , from the cur"rent of air produced by the difference of temperature ; but " whether this can account for the difierence in the time of ( vibration , is doubtful .
If the current of air was regular , and of the same swiftness in all parts of the vibration of " the ball , I think it could not ; but as there will most likely " be much irregularity in the current , it may very likely be " sufficient to account for the difference .
" It then proceeds : " By a mean of the experiments made with the wire first " used , " ( viz. the first six numbers or experiments ) ' " the density of the earth comes out 5.48 times greater than that " of water ; and by the mean of those made with the latter " wire , it comes out the same ; &amp;c. " Now , though the former list of errata were but small in quantity , yet here is one of considerable magnitude , viz. in the medium of the first six experiments , said to be 5.48 , which is very erroneous , the true medium being only 5.1 ; and it is rather curious that that medium 5.48 has been obtained , by taking the third experiment as 5.88 instead of 4.88 , through mere oversight or carelessness .
If this were the only error , it might perhaps be excused as a single accident ; but the whole will make a very different appearance , when we have shown that many small errors exist in almost all the numbers 289 in^ the last column of the table , as resulting from erroneous calculations , in the use of the general theorem before mentioned , and evinced by a comparison of the numbers in the foregoing table , with those of the following one , derived by our calculation from the same data , and by the same theorem .
The corrected table of the experiment results , ExMhotion ofT vibr Ditto in sDensities pe-i arm corcorrected .
seconds .
corrected .
ments .
: rected .
2 zoths Inch .
Min .
Sec. Seconds .
I1 3.46 14 55 895 5-49 ' 13.2 1 1455 895 5.59 x15.17 14 55 895 4.86 q4 14 ?
.68 1442 882 4.89 5 14.46 i 1439 879 4.93 6 13.63 14 54 894 5-41 7 2.92 65 414i 5 41 8 09 74 21 5*29 9 2.96 73 423 5.57 10 2.95 75 425 5*64 2ji 2.99 75 425 5.57 a3 2.85 6 57 417 5.62 13 2.86 6 57 417 5.61 14 29 75 657 417 5.-4 215 95 6 57 417 543 16 2.97 657 417 5.40 17 2.77 657 417 5.79 18 3.16 ; 658 418 5.1o 0 19 3.08 659 419 i 5.s6 i o0 3.03 71 421 5.38 21 ' 3.05 73 423 5.42 22 3.06 7 ; ' 426 S 5.47 3.99 77 447 5.6 , '24 3.14 76 426 ; 5.34 15l 3-07 77 6 426 X 5.46 6 26 3.17 77 427 53 ? ?
4 27 ; 305 716 5.38 29 2.82 73 423 5.85 i~~ 731h 290 Here the medium of the first six of these experiments is 5.19 ; of the other twenty-three experiments it is 5.43 ; and the mean of both these means is 5.31 , instead of 5.48 , as stated in the former table , being the error arising from the sum of the numerical calculations .
The remaining difference , o.31 , about the 17th part of the whole , must therefore be ascribed to the inaccuracy of making and reading off experiments , with such intricate and inadequate machinery .
I cannot conclude this paper of enquiry , without expressing a hearty wish for the repetition of the large or mountain experiment , in some other favourable situation , and with improved means , if possible .
For this purpose , I shall venture just to mention an idea which has sometimes occurred to my mind , namely , that one of the large pyramids in Egypt might profitably be employed , instead of a mountain , for this experiment .
Such a body offers several advantages for the purpose .
In the first place , the mass is sufficiently large , standing on a base of about the size of the whole space of Lincoln 's Inn Fields , and of a height almost double of that of St. Paul 's steeple ; then the station for the plummtet , or zenith sector , could be taken much nearer the centre bf the mass , than on a mountain , which would give a larger quantity of deviation of the plummet ; then the regular figure and the known composition of the mass would yield great facilities in the calculation of its attraction ; lastly , the deviation of the plummet might be observed on all the four sides .
Should such a project take place , it will be best to take the stations at about one fourth of its altitude above the base , that being the place where the deviation of the plummet would be the greatest .
Finally , so favourable for such an experiment do those circumstances appear , and so anxious are my wishes for its completion and success , that , were it not for my great age and little health , I should be glad to make one in any party to undertake such an expedition .
CHARLES HUTTON .
Bedford Row , 17tb March , 1821 .

