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Title: Astronomical Discovery
Author: Turner, Herbert Hall
Language: English
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ASTRONOMICAL DISCOVERY
[Illustration: ASTRONOMERS ROYAL.]
ASTRONOMICAL
DISCOVERY
BY
HERBERT HALL TURNER, D.Sc., F.R.S.
SAVILIAN PROFESSOR OF ASTRONOMY IN THE
UNIVERSITY OF OXFORD
_WITH PLATES_
LONDON
EDWARD ARNOLD
41 & 43 MADDOX STREET, W.
1904
(All rights reserved)
TO
EDWARD EMERSON BARNARD
ASTRONOMICAL DISCOVERER
THESE PAGES ARE INSCRIBED IN MEMORY OF
NEVER-TO-BE-FORGOTTEN DAYS SPENT WITH HIM AT THE
YERKES OBSERVATORY OF
THE UNIVERSITY OF CHICAGO
PREFACE
The aim of the following pages is to illustrate, by the study of a few
examples chosen almost at random, the variety in character of astronomical
discoveries. An attempt has indeed been made to arrange the half-dozen
examples, once selected, into a rough sequence according to the amount of
"chance" associated with the discovery, though from this point of view
Chapter IV. should come first; but I do not lay much stress upon it. There
is undoubtedly an element of "luck" in most discoveries. "The biggest
strokes are all luck," writes a brother astronomer who had done me the
honour to glance at a few pages, "but a man must not drop his catches.
Have you ever read Montaigne's essay 'Of Glory'? It is worth reading.
Change war and glory to discovery and it is exactly the same theme. If you
are looking for a motto you will find a score in it." Indeed even in cases
such as those in Chapters V. and VI., where a discovery is made by turning
over a heap of rubbish--declared such by experts and abandoned
accordingly--we instinctively feel that the finding of something valuable
was especially "fortunate." We should scarcely recommend such waste
material as the best hunting ground for gems.
The chapters correspond approximately to a series of six lectures
delivered at the University of Chicago in August 1904, at the hospitable
invitation of President Harper. They afforded me the opportunity of seeing
something of this wonderful University, only a dozen years old and yet so
amazingly vigorous; and especially of its observatory (the Yerkes
observatory, situated eighty miles away on Lake Geneva), which is only
eight years old and yet has taken its place in the foremost rank. For
these opportunities I venture here to put on record my grateful thanks.
In a portion of the first chapter it will be obvious that I am indebted to
Miss Clerke's "History of Astronomy in the Nineteenth Century"; in the
second to Professor R. A. Sampson's Memoir on the Adams MSS.; in the third
to Rigaud's "Life of Bradley." There are other debts which I hope are duly
acknowledged in the text. My grateful thanks are due to Mr. F. A. Bellamy
for the care with which he has read the proofs; and I am indebted for
permission to publish illustrations to the Royal Astronomical Society, the
Astronomer Royal, the editors of _The Observatory_, the Cambridge
University Press, the Harvard College Observatory, the Yerkes Observatory,
and the living representatives of two portraits.
H. H. TURNER.
UNIVERSITY OBSERVATORY, OXFORD,
_November 9, 1904_.
CONTENTS
PAGE
CHAPTER I
URANUS AND EROS 1
CHAPTER II
THE DISCOVERY OF NEPTUNE 38
CHAPTER III
BRADLEY'S DISCOVERIES OF THE ABERRATION OF LIGHT AND OF THE
NUTATION OF THE EARTH'S AXIS 86
CHAPTER IV
ACCIDENTAL DISCOVERIES 121
CHAPTER V
SCHWABE AND THE SUN-SPOT PERIOD 155
CHAPTER VI
THE VARIATION OF LATITUDE 177
INDEX 221
LIST OF PLATES
PLATE
I. PORTRAIT OF J. C. ADAMS _To face page_ 22
II. PORTRAIT OF A. GRAHAM " " 22
III. PORTRAIT OF U. J. LE VERRIER " " 60
IV. PORTRAIT OF J. G. GALLE " " 60
V. CORNER OF THE BERLIN MAP BY THE USE OF WHICH
GALLE FOUND NEPTUNE " " 82
VI. ASTRONOMERS ROYAL _Frontispiece_
VII. GREAT COMET OF NOV. 7, 1882 _To face page_ 122
VIII. THE OXFORD NEW STAR " " 142
IX. NEBULOSITY ROUND NOVA PERSEI " " 146
X. SUN-SPOTS AT GREENWICH, FEB. 18 AND 19, 1894 " " 158
XI. SUN-SPOTS AT GREENWICH, FEB. 20 AND 21, 1894 " " 162
XII. NUMBER OF SUN-SPOTS COMPARED WITH DAILY RANGE
OF MAGNETIC DECLINATION AND DAILY RANGE OF
MAGNETIC HORIZONTAL FORCE " " 164
XIII. GREENWICH MAGNETIC CURVES, 1859-60 " " 166
XIV. GREENWICH MAGNETIC CURVES, 1841-1860 " " 166
XV. SUN-SPOTS AND TURNS OF VANE " " 170
ERRATA
Page 133, line 27, _for_ "200 stars" _read_ "200 stars per hour."
" 145, See note on page 220.
" 146, bottom of page. This nebulosity was first discovered by Dr.
Max Wolf of Heidelberg. See _Astr. Nachr._ 3736.
" 181, line 17, _for_ "observation" _read_ "aberration."
ASTRONOMICAL DISCOVERY
CHAPTER I
URANUS AND EROS
[Sidenote: Popular view of discovery.]
Discovery is expected from an astronomer. The lay mind scarcely thinks of
a naturalist nowadays discovering new animals, or of a chemist as finding
new elements save on rare occasions; but it does think of the astronomer
as making discoveries. The popular imagination pictures him spending the
whole night in watching the skies from a high tower through a long
telescope, occasionally rewarded by the finding of something new, without
much mental effort. I propose to compare with this romantic picture some
of the actual facts, some of the ways in which discoveries are really
made; and if we find that the image and the reality differ, I hope that
the romance will nevertheless not be thereby destroyed, but may adapt
itself to conditions more closely resembling the facts.
[Sidenote: Keats' lines.]
The popular conception finds expression in the lines of Keats:--
Then felt I like some watcher of the skies
When a new planet swims into his ken.
Keats was born in 1795, published his first volume of poems in 1817, and
died in 1821. At the time when he wrote the discovery of planets was
comparatively novel in human experience. Uranus had been found by William
Herschel in 1781, and in the years 1800 to 1807 followed the first four
minor planets, a number destined to remain without additions for nearly
forty years. It would be absurd to read any exact allusion into the words
quoted, when we remember the whole circumstances under which they were
written; but perhaps I may be forgiven if I compare them especially with
the actual discovery of the planet Uranus, for the reason that this was by
far the largest of the five--far larger than any other planet known except
Jupiter and Saturn, while the others were far smaller--and that Keats is
using throughout the poem metaphors drawn from the first glimpses of "vast
expanses" of land or water. Perhaps I may reproduce the whole sonnet. His
friend C. C. Clarke had put before him Chapman's "paraphrase" of Homer,
and they sat up till daylight to read it, "Keats shouting with delight as
some passage of especial energy struck his imagination. At ten o'clock the
next morning Mr. Clarke found the sonnet on his breakfast-table."
SONNET XI
_On first looking into Chapman's "Homer"_
Much have I travell'd in the realms of gold,
And many goodly states and kingdoms seen;
Round many western islands have I been
Which bards in fealty to Apollo hold.
Oft of one wide expanse had I been told
That deep-brow'd Homer ruled as his demesne;
Yet did I never breathe its pure serene
Till I heard Chapman speak out loud and bold:
Then felt I like some watcher of the skies
When a new planet swims into his ken;
Or like stout Cortez when with eagle eyes
He star'd at the Pacific--and all his men
Look'd at each other with a wild surmise--
Silent, upon a peak in Darien.
[Sidenote: Comparison with discovery of Uranus.]
Let us then, as our first example of the way in which astronomical
discoveries are made, turn to the discovery of the planet Uranus, and see
how it corresponds with the popular conception as voiced by Keats. In one
respect his words are true to the life or the letter. If ever there was a
"watcher of the skies," William Herschel was entitled to the name. It was
his custom to watch them the whole night through, from the earliest
possible moment to daybreak; and the fruits of his labours were many and
various almost beyond belief. But did the planet "swim into his ken"? Let
us turn to the original announcement of his discovery as given in the
Philosophical Transactions for 1781.
PHILOSOPHICAL TRANSACTIONS, 1781
XXXII.--ACCOUNT OF A COMET
BY MR. HERSCHEL, F.R.S.
(Communicated by Dr. Watson, jun., of Bath, F.R.S.)
_Read April 26, 1781_
[Sidenote: Original announcement.]
"On Tuesday the 13th of March, between ten and eleven in the evening,
while I was examining the small stars in the neighbourhood of H
Geminorum, I perceived one that appeared visibly larger than the
rest; being struck with its uncommon magnitude, I compared it to H
Geminorum and the small star in the quartile between Auriga and
Gemini, and finding it to be so much larger than either of them,
suspected it to be a comet.
"I was then engaged in a series of observations on the parallax of
the fixed stars, which I hope soon to have the honour of laying
before the Royal Society; and those observations requiring very high
powers, I had ready at hand the several magnifiers of 227, 460, 932,
1536, 2010, &c., all which I have successfully used upon that
occasion. The power I had on when I first saw the comet was 227. From
experience I knew that the diameters of the fixed stars are not
proportionally magnified with higher powers as the planets are;
therefore I now put on the powers of 460 and 932, and found the
diameter of the comet increased in proportion to the power, as it
ought to be, on a supposition of its not being a fixed star, while
the diameters of the stars to which I compared it were not increased
in the same ratio. Moreover, the comet being magnified much beyond
what its light would admit of, appeared hazy and ill-defined with
these great powers, while the stars preserved that lustre and
distinctness which from many thousand observations I knew they would
retain. The sequel has shown that my surmises were well founded, this
proving to be the Comet we have lately observed.
"I have reduced all my observations upon this comet to the following
tables. The first contains the measures of the gradual increase of
the comet's diameter. The micrometers I used, when every circumstance
is favourable, will measure extremely small angles, such as do not
exceed a few seconds, true to 6, 8, or 10 thirds at most; and in the
worst situations true to 20 or 30 thirds; I have therefore given the
measures of the comet's diameter in seconds and thirds. And the parts
of my micrometer being thus reduced, I have also given all the rest
of the measures in the same manner; though in large distances, such
as one, two, or three minutes, so great an exactness, for several
reasons, is not pretended to."
[Sidenote: Called first a comet.]
[Sidenote: Other observers would not have found it at all.]
At first sight this seems to be the wrong reference, for it speaks of a
new comet, not a new planet. But it is indeed of Uranus that Herschel is
speaking; and so little did he realise the full magnitude of his
discovery at once, that he announced it as that of a comet; and a comet
the object was called for some months. Attempts were made to calculate its
orbit as a comet, and broke down; and it was only after much work of this
kind had been done that the real nature of the object began to be
suspected. But far more striking than this misconception is the display of
skill necessary to detect any peculiarity in the object at all. Among a
number of stars one seemed somewhat exceptional in size, but the
difference was only just sufficient to awaken suspicion in a keen-eyed
Herschel. Would any other observer have noticed the difference at all?
Certainly several good observers had looked at the object before, and
looked at it with the care necessary to record its position, without
noting any peculiarity. Their observations were recovered subsequently and
used to fix the orbit of the new planet more accurately. I shall remind
you in the next chapter that Uranus had been observed in this way no less
than seventeen times by first-rate observers without exciting their
attention to anything remarkable. The first occasion was in 1690, nearly a
century before Herschel's grand discovery, and these chance observations,
which lay so long unnoticed as in some way erroneous, subsequently proved
to be of the utmost value in fixing the orbit of the new planet. But there
is even more striking testimony than this to the exceptional nature of
Herschel's achievement. It is a common experience in astronomy that an
observer may fail to notice in a general scrutiny some phenomenon which he
can see perfectly well when his attention is directed to it: when a man
has made a discovery and others are told what to look for, they often see
it so easily that they are filled with amazement and chagrin that they
never saw it before. Not so in the case of Uranus. At least two great
astronomers, Lalande and Messier, have left on record their astonishment
that Herschel could differentiate it from an ordinary star at all; for
even when instructed where to look and what to look for, they had the
greatest difficulty in finding it. I give a translation of Messier's
words, which Herschel records in the paper already quoted announcing the
discovery:--
"Nothing was more difficult than to recognise it; and I cannot
conceive how you have been able to return several times to this star
or comet; for absolutely it has been necessary to observe it for
several consecutive days to perceive that it was in motion."
[Sidenote: No "swimming into ken."]
We cannot, therefore, fit the facts to Keats' version of them. The planet
did not majestically reveal itself to a merely passive observer: rather
did it, assuming the disguise of an ordinary star, evade detection to the
utmost of its power; so that the keenest eye, the most alert attention,
the most determined following up of a mere hint, were all needed to
unmask it. But is the romance necessarily gone? If another Keats could
arise and know the facts, could he not coin a newer and a truer phrase for
us which would still sound as sweetly in our ears?
[Sidenote: Though this may happen at times.]
[Sidenote: Name of new planet.]
I must guard against a possible misconception. I do not mean to convey
that astronomical discoveries are not occasionally made somewhat in the
manner so beautifully pictured by Keats. Three years ago a persistent
"watcher of the skies," Dr. Anderson of Edinburgh, suddenly caught sight
of a brilliant new star in Perseus; though here "flashed into his ken"
would perhaps be a more suitable phrase than "swam." And comets have been
detected by a mere glance at the heavens without sensible effort or care
on the part of the discoverer. But these may be fairly called exceptions;
in the vast majority of cases hard work and a keen eye are necessary to
make the discovery. The relative importance of these two factors of course
varies in different cases; for the detection of Uranus perhaps the keen
eye may be put in the first place, though we must not forget the diligent
watching which gave it opportunity. Other cases of planetary discovery may
be attributed more completely to diligence alone, as we shall presently
see. But before leaving Uranus for them I should like to recall the
circumstances attending the naming of the planet. Herschel proposed to
call it _Georgium Sidus_ in honour of his patron, King George III., and
as the best way of making his wishes known, wrote the following letter to
the President of the Royal Society, which is printed at the beginning of
the Philosophical Transactions for 1783.
_A Letter from_ WILLIAM HERSCHEL, Esq., F.R.S.,
_to_ Sir JOSEPH BANKS, Bart., P.R.S.
"Sir,--By the observations of the most eminent astronomers in Europe
it appears that the new star, which I had the honour of pointing out
to them in March 1781, is a Primary Planet of our Solar System. A
body so nearly related to us by its similar condition and situation
in the unbounded expanse of the starry heavens, must often be the
subject of conversation, not only of astronomers, but of every lover
of science in general. This consideration then makes it necessary to
give it a name whereby it may be distinguished from the rest of the
planets and fixed stars.
[Sidenote: _Georgium Sidus._]
"In the fabulous ages of ancient times, the appellations of Mercury,
Venus, Mars, Jupiter, and Saturn were given to the planets as being
the names of their principal heroes and divinities. In the present
more philosophical era, it would hardly be allowable to have recourse
to the same method, and call on Juno, Pallas, Apollo, or Minerva for
a name to our new heavenly body. The first consideration in any
particular event, or remarkable incident, seems to be its chronology:
if in any future age it should be asked, _when_ this last found
planet was discovered? It would be a very satisfactory answer to say,
'In the reign of King George the Third.' As a philosopher then, the
name GEORGIUM SIDUS presents itself to me, as an appellation which
will conveniently convey the information of the time and country
where and when it was brought to view. But as a subject of the best
of kings, who is the liberal protector of every art and science; as a
native of the country from whence this illustrious family was called
to the British throne; as a member of that Society which flourishes
by the distinguished liberality of its royal patron; and, last of
all, as a person now more immediately under the protection of this
excellent monarch, and owing everything to his unlimited bounty;--I
cannot but wish to take this opportunity of expressing my sense of
gratitude by giving the name _Georgium Sidus_,
_Georgium Sidus
----jam nunc assuesce vocari,_
_Virg. Georg._
to a star which (with respect to us) first began to shine under his
auspicious reign.
"By addressing this letter to you, Sir, as President of the Royal
Society, I take the most effectual method of communicating that name
to the literati of Europe, which I hope they will receive with
pleasure.--I have the honour to be, with the greatest respect, Sir,
your most humble and most obedient servant,
W. HERSCHEL."
[Sidenote: Herschel.]
This letter reminds us how long it was since a new name had been required
for a new planet,--to find a similar occasion Herschel had to go to the
almost prehistoric past, when the names of heroes and divinities were
given to the planets. It is, perhaps, not unnatural that he should have
considered an entirely new departure appropriate for a discovery separated
by so great a length of time from the others; but his views were not
generally accepted, especially on the Continent. Lalande courteously
proposed the name of Herschel for the new planet, in honour of the
discoverer, and this name was used in France; but Bode, on the other hand,
was in favour of retaining the old practice simply, and calling the new
planet Uranus. All three names seem to have been used for many years. Only
the other day I was interested to see an old pack of cards, used for
playing a parlour game of Astronomy, in which the name Herschel is used.
The owner told me that they had belonged to his grandfather; and the date
of publication was 1829, and the place London, so that this name was in
common use in England nearly half a century after the actual discovery;
though in the "English Nautical Almanac" the name "the Georgian"
(apparently preferred to Herschel's _Georgium Sidus_) was being used
officially after 1791, and did not disappear from that work until 1851
(published in 1847.)
[Sidenote: Uranus finally adopted.]
It would appear to have been the discovery of Neptune, with which we shall
deal in the next chapter, which led to this official change; for in the
volume for 1851 is included Adams' account of his discovery with the
title--
"ON THE PERTURBATIONS OF URANUS,"
and there was thus a definite reason for avoiding two names for the same
planet in the same work. But Le Verrier's paper on the same topic at the
same date still uses the name "Herschel" for the planet.
[Sidenote: Bode's law.]
The discovery of Neptune, as we shall see, was totally different in
character from that of Uranus. The latter may be described as the finding
of something by an observer who was looking for anything; Neptune was the
finding of something definitely sought for, and definitely pointed out by
a most successful and brilliant piece of methodical work. But before that
time several planets had been found, as the practical result of a definite
search, although the guiding principle was such as cannot command our
admiration to quite the same extent as in the case of Neptune. To explain
it I must say something of the relative sizes of the orbits in which
planets move round the sun. These orbits are, as we know, ellipses; but
they are very nearly circles, and, excluding refinements, we may consider
them as circles, with the sun at the centre of each, so that we may talk
of the distance of any planet from the sun as a constant quantity without
serious error. Now if we arrange the planetary distances in order, we
shall notice a remarkable connection between the terms of the series. Here
is a table showing this connection.
TABLE OF THE DISTANCES OF THE PLANETS FROM THE SUN, SHOWING "BODE'S LAW."
+----------------------------------------------------+
| Name of | Distance from | "Bode's Law" |
| Planet. | Sun, taking | (originally formulated |
| | that of Earth | by Titius, but brought |
| | as 10. | into notice by Bode). |
|----------------------------------------------------|
| Mercury | 4 | 4 + 0= 4 |
| Venus | 7 | 4 + 3= 7 |
| The Earth | 10 | 4 + 6= 10 |
| Mars | 15 | 4 + 12= 16 |
| ( ) | ( ) | 4 + 24= 28 |
| Jupiter | 52 | 4 + 48= 52 |
| Saturn | 95 | 4 + 96= 100 |
| Uranus | 192 | 4 + 192= 196 |
+----------------------------------------------------+
[Sidenote: Gap in the series suggesting unknown planet.]
[Sidenote: Search for it.]
[Sidenote: Accidental discovery.]
If we write down a series of 4's, and then add the numbers 3, 6, 12, and
so on, each formed by doubling the last, we get numbers representing very
nearly the planetary distances, which are shown approximately in the
second column. But three points call for notice. Firstly, the number
before 3 should be 1-1/2, and not zero, to agree with the rest. Secondly,
there is a gap, or rather was a gap, after the discovery of Uranus,
between Mars and Jupiter; and thirdly, we see that when Uranus was
discovered, and its distance from the sun determined, this distance was
found to fall in satisfactorily with this law, which was first stated by
Titius of Wittenberg. This third fact naturally attracted attention. No
explanation of the so-called "law" was known at the time; nor is any
known even yet, though we may be said to have some glimmerings of a
possible cause; and in the absence of such explanation it must be regarded
as merely a curious coincidence. But the chances that we are in the
presence of a mere coincidence diminish very quickly with each new term
added to the series, and when it was found that Herschel's new planet
fitted in so well at the end of the arrangement, the question arose
whether the gap above noticed was real, or whether there was perhaps
another planet which had hitherto escaped notice, revolving in an orbit
represented by this blank term. This question had indeed been asked even
before the discovery of Uranus, by Bode, a young astronomer of Berlin; and
for fifteen years he kept steadily in view this idea of finding a planet
to fill the vacant interval. The search would be a very arduous one,
involving a careful scrutiny, not perhaps of the whole heavens, but of a
considerable portion of it along the Zodiac; too great for one would-be
discoverer single-handed; but in September 1800 Bode succeeded in
organising a band of six German astronomers (including himself) for the
purpose of conducting this search. They divided the Zodiac into
twenty-four zones, and were assigning the zones to the different
observers, when they were startled by the news that the missing planet had
been accidentally found by Piazzi in the constellation Taurus. The
discovery was made somewhat dramatically on the first evening of the
nineteenth century (January 1, 1801). Piazzi was not looking for a planet
at all, but examining an error made by another astronomer; and in the
course of this work he recorded the position of a star of the eighth
magnitude. Returning to it on the next night, it seemed to him that it had
slightly moved westwards, and on the following night this suspicion was
confirmed. Remark that in this case no peculiar appearance in the star
suggested that it might be a comet or planet, as in the case of the
discovery of Uranus. We are not unfair in ascribing the discovery to pure
accident, although we must not forget that a careless observer might
easily have missed it. Piazzi was anything but careless, and watched the
new object assiduously till February 11th, when he became dangerously ill;
but he had written, on January 23rd, to Oriani of Milan, and to Bode at
Berlin on the following day. These letters, however, did not reach the
recipients (in those days of leisurely postal service) until April 5th and
March 20th respectively; and we can imagine the mixed feelings with which
Bode heard that the discovery which he had contemplated for fifteen years,
and for which he was just about to organise a diligent search, was thus
curiously snatched from him.
[Sidenote: Hegel's forecast.]
More curious still must have seemed the intelligence to a young
philosopher of Jena named Hegel, who has since become famous, but who had
just imperilled his future reputation by publishing a dissertation
proving conclusively that the number of the planets could not be greater
than seven, and pouring scorn on the projected search of the half-dozen
enthusiasts who were proposing to find a new planet merely to fill up a
gap in a numerical series.
[Sidenote: The planet lost again.]
The sensation caused by the news of the discovery was intensified by
anxiety lest the new planet should already have been lost; for it had
meanwhile travelled too close to the sun for further observation, and the
only material available for calculating its orbit, and so predicting its
place in the heavens at future dates, was afforded by the few observations
made by Piazzi. Was it possible to calculate the orbit from such slender
material? It would take too long to explain fully the enormous difficulty
of this problem, but some notion of it may be obtained, by those
unacquainted with mathematics, from a rough analogy. If we are given a
portion of a circle, we can, with the help of a pair of compasses,
complete the circle: we can find the centre from which the arc is struck,
either by geometrical methods, or by a few experimental trials, and then
fill in the rest of the circumference. If the arc given is large we can do
this with certainty and accuracy; but if the arc is small it is difficult
to make quite sure of the centre, and our drawing may not be quite
accurate. Now the arc which had been described by the tiny planet during
Piazzi's observations was only three degrees; and if any one will kindly
take out his watch and look at the minute marks round the dial, three
degrees is just _half_ a single minute space. If the rest of the dial were
obliterated, and only this small arc left, would he feel much confidence
in restoring the obliterated portion? This problem gives some idea of the
difficulties to be encountered, but only even then a very imperfect one.
[Sidenote: Gauss shows how to find it.]
Briefly, the solution demanded a new mathematical method in astronomy. But
difficulties are sometimes the opportunities of great men, and this
particular difficulty attracted to astronomy the great mathematician
Gauss, who set himself to make the best of the observation available, and
produced his classical work, the _Theoria Motus_, which is the standard
work for such calculations to the present day. May we look for a few
moments at what he himself says in the preface to his great work? I
venture to reproduce the following rough translation (the book being
written in Latin, according to the scientific usage of the time):--
EXTRACT FROM THE PREFACE TO THE
_Theoria Motus_.
[Sidenote: The _Theoria Motus_.]
"Some ideas had occurred to me on this subject in September 1801, at
a time when I was occupied on something quite different; ideas which
seemed to contribute to the solution of the great problem of which I
have spoken. In such cases it often happens that, lest we be too much
Distracted From the Attractive Investigation On Which We Are
Engaged, We Allow Associations Of Ideas Which, If More Closely
Examined, Might Prove Extraordinarily Fruitful, To Perish From
Neglect. Perchance These Same Idea-lets of Mine Would Have Met With
This Fate, If They Had Not Most Fortunately Lighted Upon a Time Than
Which None Could Have Been Chosen More Favourable For Their
Preservation and Development. For About The Same Time a Rumour Began
To Be Spread Abroad Concerning a New Planet Which Had Been Detected
On January 1st of That Year at the Observatory Of Palermo; and
Shortly Afterwards the Actual Observations Which Had Been Made
Between January 1st And February 11th by the Renowned Philosopher
Piazzi Were Published. Nowhere in All The Annals of Astronomy Do We
Find Such an Important Occasion; and Scarcely Is It Possible To
Imagine a More Important Opportunity for Pointing Out, As
Emphatically As Possible, the Importance Of That Problem, As at the
Moment When Every Hope of Re-discovering, Among the Innumerable
Little Stars of Heaven, That Mite of a Planet Which Had Been Lost To
Sight for Nearly a Year, Depended Entirely on an Approximate
Knowledge Of Its Orbit, Which Must Be Deduced From Those Scanty
Observations. Could I Ever Have Had A Better Opportunity for Trying
Whether Those Idea-lets Of Mine Were of Any Practical Value Than If I
Then Were To Use Them for the Determination Of The Orbit of Ceres, a
Planet Which, in the Course of those forty-one days, had described
around the earth an arc of no more than three degrees? and, after a
year had passed, required to be tracked out in a region of the sky
far removed from its original position? The first application of this
method was made in the month of October 1801, and the first clear
night, when the planet was looked for by the help of the ephemeris I
had made, revealed the truant to the observer. Three new planets
found since then have supplied fresh opportunities for examining and
proving the efficacy and universality of this method.
"Now a good many astronomers, immediately after the rediscovery of
Ceres, desired me to publish the methods which had been used in my
calculations. There were, however, not a few objections which
prevented me from gratifying at that moment these friendly
solicitations, viz. other business, the desire of treating the matter
more fully, and more especially the expectation that, by continuing
to devote myself to this research, I should bring the different
portions of the solution of the problem to a more perfect pitch of
universality, simplicity, and elegance. As my hopes have been
justified, I do not think there is any reason for repenting of my
delay. For the methods which I had repeatedly applied from the
beginning admitted of so many and such important variations, that
scarcely a vestige of resemblance remains between the method by which
formerly I had arrived at the orbit of Ceres and the practice which
I deal with in this work. Although indeed it would be alien to my
intention to write a complete history about all these researches
which I have gradually brought to even greater perfection, yet on
many occasions, especially whenever I was confronted by some
particularly serious problem, I thought that the first methods which
I employed ought not to be entirely suppressed. Nay, rather, in
addition to the solutions of the principal problems, I have in this
work followed out many questions which presented themselves to me, in
the course of a long study of the motions of the heavenly bodies in
conic sections, as being particularly worthy of attention, whether on
account of the neatness of the analysis, or more especially by reason
of their practical utility. Yet I have always given the greater care
to subjects which I have made my own, merely noticing by the way
well-known facts where connection of thought seemed to demand it."
[Sidenote: Rediscovery of Ceres.]
[Sidenote: Another planet found.]
These words do not explain in any way the methods introduced by Gauss, but
they give us some notion of the flavour of the work. Aided by these
brilliant researches, the little planet was found on the last day of the
year by Von Zach at Gotha, and on the next night, independently, by Olbers
at Bremen. But, before this success, there had been an arduous search,
which led to a curious consequence. Olbers had made himself so familiar
with all the small stars along the track which was being searched for the
missing body, that he was at once struck by the appearance of a stranger
near the spot where he had just identified Ceres. At first he thought this
must be some star which had blazed up to brightness; but he soon found
that it also was moving, and, to the great bewilderment of the
astronomical world, it proved to be another planet revolving round the sun
at a distance nearly the same as the former. This was an extraordinary and
totally unforeseen occurrence. The world had been prepared for _one_
planet; but here were _two_!
[Sidenote: Hypothesis of many fragments.]
The thought occurred to Olbers that they were perhaps fragments of a
single body which had been blown to pieces by some explosion, and that
there might be more of the pieces; and he therefore suggested as a guide
for finding others that, since by the known laws of gravitation, bodies
which circle round the sun return periodically to their starting-point,
therefore all these fragments would in due course return to the point in
the heavens where the original planet had exploded. Hence the search might
be most profitably conducted in the neighbourhood of the spot where the
two first fragments (which had been named Ceres and Pallas) had already
been found. We now have good reason to believe that this view is a
mistaken one, but nevertheless it was apparently confirmed by the
discovery of two more bodies of the same kind, which were called Juno and
Vesta; the second of these being found by Olbers himself after three
years' patient work in 1807. Hence, although the idea of searching for a
more or less definitely imagined planet was not new, although Bode had
conceived it as early as 1785, and organised a search on this plan, three
planets were actually found before the first success attending a definite
search. Ceres, as already remarked, was found by a pure accident; and the
same may be said of Pallas and Juno, though it may fairly be added that
Pallas was actually contrary to expectation.
MINOR PLANETS, 1801 TO 1850.
+---------------------------------------+
|Number| Name. | Discoverer. | Date.|
|---------------------------------------|
| 1 | Ceres | Piazzi | 1801 |
| 2 | Pallas | Olbers | 1802 |
| 3 | Juno | Harding | 1804 |
| 4 | Vesta | Olbers | 1807 |
|------|-----------|-------------|------|
| 5 | Astraea | Hencke | 1845 |
| 6 | Hebe | Hencke | 1847 |
| 7 | Iris | Hind | 1847 |
| 8 | Flora | Hind | 1847 |
| 9 | Metis | Graham | 1848 |
| 10 | Hygeia | De Gasparis | 1849 |
| 11 | Parthenope| De Gasparis | 1850 |
| 12 | Victoria | Hind | 1850 |
| 13 | Egeria | De Gasparis | 1850 |
+---------------------------------------+
[Sidenote: Hencke's long search.]
Here now is a table showing how other bodies were gradually added to this
first list of four, but you will see that no addition was made for a long
time. Not that the search was immediately abandoned; but being rewarded by
no success for some years, it was gradually dropped, and the belief gained
ground that the number of the planets was at last complete. The
discoverers of Uranus and of these first four minor planets all died
before any further addition was made; and it was not until the end of 1845
that Astraea was found by an ex-postmaster of the Prussian town of
Driessen, by name Hencke, who, in spite of the general disbelief in the
existence of any more planets, set himself diligently to search for them,
and toiled for fifteen long years before at length reaping his reward.
Others then resumed the search; Hind, the observer of an English amateur
astronomer near London, found Iris a few weeks after Hencke had been
rewarded by a second discovery in 1847, and in the following year Mr.
Graham at Markree in Ireland (who is still living, and has only just
retired from active work at the Cambridge Observatory) found Metis; and
from that time new discoveries have been added year by year, until the
number of planets now known exceeds 500, and is steadily increasing.
[Illustration:
_By permission of Messrs. Macmillan & Co._
I.--J. C. ADAMS.]
[Illustration:
II.--A. GRAHAM.
DISCOVERER OF THE NINTH MINOR PLANET (METIS).]
[Sidenote: The photographic method.]
You will see the great variety characterising these discoveries; some of
them are the result of deliberate search, others have come accidentally,
and some even contrary to expectation. Of the great majority of the
earlier ones it may be said that enormous diligence was required for each
discovery; to identify a planet it is necessary to have either a good map
of the stars or to know them thoroughly, so that the map practically
exists in the brain. We need only remember Hencke's fifteen years of
search before success to recognise what vast stores of patience and
diligence were required in carrying out the search. But of late years
photography has effected a great revolution in this respect. It is no
longer necessary to do more than set what Sir Robert Ball has called a
"star-trap," or rather planet-trap. If a photograph be taken of a region
of the heavens, by the methods familiar to astronomers, so that each star
makes a round dot on the photographic plate, any sufficiently bright
object moving relatively to the stars will make a small line or trail, and
thus betray its planetary character. In this way most of the recent
discoveries have been made, and although diligence is still required in
taking the photographs, and again in identifying the objects thus found
(which are now very often the images of already known members of the
system), the tedious scrutiny with the eye has become a thing of the past.
TABLE SHOWING THE NUMBER OF MINOR PLANETS DISCOVERED IN EACH DECADE
SINCE 1850.
1801 to 1850--altogether 13 discoveries.
1851 to 1860-- " 49 "
1861 to 1870-- " 49 "
1871 to 1880-- " 108 "
1881 to 1890-- " 83 "
1891 to 1900-- " 180 announcements
In 1901 " 36 "
" 1902 " 50 "
" 1903 " 41 "
---
Total 609
[_N.B._--Many of the more recent announcements turned out to refer to
old discoveries.]
[Sidenote: Scarcity of names.]
The known number of these bodies has accordingly increased so rapidly as
to become almost an embarrassment; and in one respect the embarrassment is
definite, for it has become quite difficult to find _names_ for the new
discoveries. We remember with amusement at the present time that for the
early discoveries there was sometimes a controversy (of the same kind as
in the case of Uranus) about the exact name which a planet should have.
Thus when it was proposed to call No. 12 (discovered in 1850, in London,
by Mr. Hind) "Victoria," there was an outcry by foreign astronomers that
by a subterfuge the name of a reigning monarch was again being proposed
for a planet, and considerable opposition was manifested, especially in
America. But it became clear, as other discoveries were added, that the
list of goddesses, or even humbler mythological people, would not be large
enough to go round if we were so severely critical, and must sooner or
later be supplemented from sources hitherto considered unsuitable; so,
ultimately, the opposition to the name Victoria was withdrawn. Later still
the restriction to feminine names has been broken through; one planet has
been named Endymion, and another, of which we shall presently speak more
particularly, has been called Eros. But before passing to him you may
care to look at some of the names selected for others:--
No. Name.
248 Lameia
250 Bettina
261 Prymno
264 Libussa
296 Phaëtusa
340 Eduarda
341 California
350 Ornamenta
357 Ninina
385 Ilmatar
389 Industria
391 Ingeborg
433 Eros
443 Photographica
457 Alleghenia
462 Eriphyla
475 Ocllo
484 Pittsburghia
503 Evelyn
[Sidenote: Bettina.]
[Sidenote: The provisional letters.]
In connection with No. 250 there is an interesting little history. In the
_Observatory_ for 1885, page 63, appeared the following
advertisement:--"Herr Palisa being desirous to raise funds for his
intended expedition to observe the Total Solar Eclipse of August 1886,
will sell the right of naming the minor planet No. 244 for £50." The
bright idea seems to have struck Herr Palisa, who had already discovered
many planets and begun to find difficulties in assigning suitable names,
that he might turn his difficulty into a source of profit in a good cause.
The offer was not responded to immediately, nor until Herr Palisa had
discovered two more planets, Nos. 248 and 250. He found names for two,
leaving, however, the last discovered always open for a patron, and on
page 142 of the same magazine for 1886 the following note informs us how
his patience was ultimately rewarded:--"Minor planet No. 250 has been
named 'Bettina' by Baron Albert de Rothschild." I have not heard, however,
that this precedent has been followed in other cases, and the ingenuity of
discoverers was so much overtaxed towards the end of last century that the
naming of their planets fell into arrears. Recently a Commission, which
has been established to look after these small bodies generally, issued a
notice that unless the naming was accomplished before a certain date it
would be ruthlessly taken out of the hands of the negligent discoverers.
Perhaps we may notice, before passing on, the provisional system which was
adopted to fill up the interval required for finding a suitable name, and
required also for making sure that the planet was in fact a new one, and
not merely an old one rediscovered. There was a system of _numbering_ in
existence as well as of _naming_, but it was unadvisable to attach even a
number to a planet until it was quite certain that the discovery was new,
for otherwise there might be gaps created in what should be a continuous
series by spurious discoveries being struck out. Accordingly it was
decided to attach at first to the object merely a _letter of the
alphabet_, with the year of discovery, as a provisional name. The alphabet
was, however, run through so quickly, and confusion was so likely to ensue
if it was merely repeated, that on recommencing it the letter A was
prefixed, and the symbols adopted were therefore AA, AB, AC, &c.; after
completing the alphabet again, the letter B was prefixed, and so on; and
astronomers began to fear that they had before them a monotonous prospect
of continually adding new planets, varied by no incident more exciting
than starting the alphabet over again after every score.
[Sidenote: Eros.]
Fortunately, however, on running through it for the fifth time, an object
of particular interest was discovered. Most of these bodies revolve at a
distance from the sun intermediate between that of Mars and that of
Jupiter, but the little planet which took the symbol DQ, and afterwards
the name of Eros, was found to have a mean distance actually less than
that of Mars, and this gave it an extraordinary importance with respect to
the great problem of determining the sun's distance. To explain this
importance we must make a small digression.
[Sidenote: Transit of Venus.]
About the middle of the last century our knowledge of the sun's distance
was very rough, as may be seen from the table on p. 32; but there were in
prospect two transits of Venus, in 1874 and 1882, and it was hoped that
these would give opportunities of a special kind for the measurement of
this important quantity, which lies at the root of all our knowledge of
the exact masses and dimensions of not only the sun, but of the planets as
well.
[Illustration: FIG. 1.]
[Sidenote: The "Black Drop."]
The method may be briefly summarised thus: An observer in one part of the
earth would see Venus cross the disc of the sun along a different path
from that seen by another observer, as will be clear from the diagram. If
the size of the earth, the distance of the sun, and the _relative_
distance of Venus be known, it can be calculated what this difference in
path will be. Now the relative distance of Venus _is_ known with great
accuracy, from observing the time of her revolution round the sun; the
size of the earth we can measure by a survey; there remains, therefore,
only one unknown quantity, the sun's distance. And since from a knowledge
of this we could calculate the difference in path, it is easy to invert
the problem, and calculate the sun's distance from the knowledge of the
observed difference in path. Accordingly, observers were to be scattered,
not merely to two, but to many stations over the face of the earth, to
observe the exact path taken by Venus in transit over the sun's disc as
seen from their station; and especially to observe the exact times of
beginning and ending of the transit; and, by comparison of their results,
it was hoped to determine this very important quantity, the sun's
distance. It was known from previous experience that there were certain
difficulties in observing very exactly the beginning and end of the
transit. There was an appearance called the "Black Drop," which had caused
trouble on previous occasions; an appearance as though the round black
spot which can be seen when Venus has advanced some distance over the
sun's disc was reluctant to make the entry and clung to the edge or "limb"
of the sun as it is called, somewhat as a drop of ink clings to a pen
which is slowly withdrawn from an inkpot. Similarly, at the end of the
transit or egress, instead of approaching the limb steadily the planet
seems at the last moment to burst out towards it, rendering the estimation
of the exact moment when the transit is over extremely doubtful.
[Sidenote: Failure.]
These difficulties, as already stated, were known to exist; but there is a
long interval between transits of Venus, or rather between every pair of
such transits. After those of 1874 and 1882 there will be no more until
2004 and 2012, so that we shall never see another; similarly, before that
pair of the last century, there had not been any such occasion since 1761
and 1769, and no one was alive who remembered at first hand the trouble
which was known to exist. It was proposed to obviate the anticipated
difficulties by careful practice beforehand; models were prepared to
resemble as nearly as possible the expected appearances, and the times
recorded by different observers were compared with the true time, which
could, in this case of a model, be determined. In this way it was hoped
that the habit of each observer, his "personal equation" as it is called,
could be determined beforehand, and allowed for as a correction when he
came to observe the actual transit. The result, however, was a great
disappointment. The actual appearances were found to be totally different
in character from those shown by the model; chiefly, perhaps, because it
had been impossible to imitate with a model the effect of the atmosphere
which surrounds the planet Venus. Observers trained beforehand, using
similar instruments, and standing within a few feet of each other, were
expected, after making due allowance for personal equation, to give the
same instant for contact; but their observations when made were found to
differ by nearly a minute of time, and after an exhaustive review of the
whole material it was felt that all hope of determining accurately the
sun's distance by this method must be given up. The following table will
show how much was learned from the transits of Venus, and how much
remained to be settled. They left the result in doubt over a range of
about two million miles.
SUN'S DISTANCE, IN MILLIONS OF MILES, AS FOUND BY DIFFERENT OBSERVERS
=Before the Transits of Venus= estimates varied between =96= million
miles (Gilliss and Gould, 1856) and =91= million (Winneche, 1863), a
range of 5 million miles.
=The Transits of 1874 and 1882= gave results lying between =93-1/4=
million (Airy, from British observations of 1874), =92-1/2= million
(Stone, from British observations of 1882), and =91-1/2= million
(Puiseux, from French observations), a range of 1-3/4 millions.
=Gill's Heliometer results= all lie very near =93= millions. The
observations of Mars in 1877 give about 100,000 miles over this
figure: but the observations of Victoria, Iris, and Sappho, which are
more trustworthy, all agree in giving about 100,000 miles _less_ than
the 93 millions.
It became necessary, therefore, to look to other methods; and before the
second transit of 1882 was observed, an energetic astronomer, Dr. David
Gill, had already put into operation the method which may be now regarded
as the standard one.
[Sidenote: Modern method for sun's distance.]
[Sidenote: Photography.]
[Sidenote: Dr. Gill's expedition to Ascension.]
We have said that the _relative_ distance of Venus from the sun is
accurately known from observations of the exact time of revolution. It is
easy to see that these times of revolution can be measured accurately by
mere accumulation. We may make an error of a few seconds in noting the
time of return; but if the whole interval comprises 10 revolutions, this
error is divided by 10, if 100 revolutions by 100, and so on; and by this
time a great number of revolutions of all the planets (except those just
discovered) have been recorded. Hence we know their relative distances
with great precision; and if we can find the distance in miles of any one
of them, we can find that of the sun itself, or of any other planet, by a
simple rule-of-three sum. By making use of this principle many of the
difficulties attending the direct determination of the sun's distance can
be avoided; for instance, since the sun's light overpowers that of the
stars, it is not easy to directly observe the place of the sun among the
stars; but this is not so for the planets. We can photograph a planet and
the stars surrounding it on the same plate, and then by careful
measurement determine its exact position among the stars; and since this
position differs slightly according to the situation of the observer on
the earth's surface, by comparing two photographs taken at stations a
known distance apart we can find the distance of the planet from the
earth; and hence, as above remarked, the distance of the sun and all the
other members of the solar system. Or, instead of taking photographs from
two different stations, we can take from the same station two photographs
at times separated by a known interval. For in that interval the station
will have been carried by the earth's rotation some thousands of miles
away from its former position, and becomes virtually a second station
separated from the first by a distance which is known accurately when we
know the elapsed time. Again, instead of taking photographs, and from them
measuring the position of the planet among the stars, we may make the
measurements on the planet and stars in the sky itself; and since in 1878,
when Dr. Gill set out on his enterprise of determining the sun's distance,
photography was in its infancy as applied to astronomy, he naturally made
his observations on the sky with an instrument known as a heliometer. He
made them in the little island of Ascension, which is suitably situated
for the purpose; because, being near the earth's equator, it is carried by
the earth's rotation a longer distance in a given time than places nearer
the poles, and in these observations for "parallax," as they are called,
it is important to have the displacement of the station as large as
possible. For a similar reason the object selected among the planets must
be as near the earth as possible; and hence the planet Mars, which at
favourable times comes nearer to us than any other superior planet[1] then
known, was selected for observation with the heliometer.
And now it will be seen why the discovery of the little planet Eros was
important, for Mars was no longer the known planet capable of coming
nearest to us; it had been replaced by this new arrival.
[Sidenote: Victoria, Iris, and Sappho.]
[Sidenote: Eros.]
Further, a small planet which is in appearance just like an ordinary star
has, irrespective of this great proximity, some distinct advantages over a
planet like Mars, which appears as a round disc, and is, moreover, of a
somewhat reddish colour. When the distance of an object of this kind from
a point of line such as a star is measured with the heliometer it is found
that a certain bias, somewhat difficult to allow for with certainty, is
introduced into the measures; and our confidence in the final results
suffers accordingly. After his observations of Mars in 1878, Dr. David
Gill was sufficiently impressed with this source of error to make three
new determinations of the sun's distance, using three of the minor planets
instead of Mars, in spite of the fact that they were sensibly farther
away; and his choice was justified by finding that the results from these
three different sets of observations agreed well among themselves, and
differed slightly from that given by the observations of Mars. Hence it
seems conclusively proved that one of these bodies is a better selection
than Mars in any case, and the discovery of Eros, which offered the
advantage of greater proximity in addition, was hailed as a new
opportunity of a most welcome kind. It was seen by a little calculation
that in the winter of 1900-1901 the planet would come very near the
earth; not the nearest possible (for it was also realised that a still
better opportunity had occurred in 1894, though it was lost because the
planet had not yet been discovered), but still the nearest approach which
would occur for some thirty years; and extensive, though somewhat hasty,
preparations were made to use it to the fullest advantage. Photography had
now become established as an accurate method of making measurements of the
kind required; and all the photographic telescopes which could be spared
were pressed into the service, and diligently photographed the planet and
surrounding stars every fine night during the favourable period. The work
of measuring and reducing these photographs involves an enormous amount of
labour, and is even yet far from completed, but we know enough to expect a
result of the greatest value. More than this we have not time to say here
about this great problem, but it will have been made clear that just when
astronomers were beginning to wonder whether it was worth while continuing
the monotonous discovery of new minor planets by the handful, the 433rd
discovery also turned out to be one of the greatest importance.
To canons for the advantageous prosecution of research, if we care to make
them, we may therefore add this--that there is no line of research,
however apparently unimportant or monotonous, which we can afford to
neglect. Just when we are on the point of relinquishing it under the
impression that the mine is exhausted, we may be about to find a nugget
worth all our previous and future labour. This rule will not, perhaps,
help us very much in choosing what to work at; indeed, it is no rule at
all, for it leaves us the whole field of choice unlimited. But this
negative result will recur again and again as we examine the lessons
taught by discoveries: there seem to be no rules at all. Whenever we seem
to be able to deduce one from an experience, some other experience will
flatly contradict it. Thus we might think that the discovery of Eros
taught us to proceed patiently with a monotonous duty, and not turn aside
to more novel and attractive work; yet it is often by leaving what is in
hand and apparently has first claim on our attention that we shall do
best, and we shall learn in the next chapter how a failure thus to turn
flexibly aside was repented.
CHAPTER II
THE DISCOVERY OF NEPTUNE
[Sidenote: Search for definite objects.]
In the last chapter we saw that the circumstances under which planets were
discovered varied considerably. Sometimes the discoveries were not
previously expected, occurring during a general examination of the
heavens, or a search for other objects; and, on one occasion at least, the
discovery may be said to have been even contrary to expectation, though,
as the existence of a number of minor planets began to be realised, there
have also been many cases where the discovery has been made as the result
of a definite and deliberate search. But the search cannot be said to have
been inspired by any very clear or certain principle: for the law of Bode,
successful though it has been in indicating the possible existence of new
planets, cannot, as yet, be said to be founded upon a formulated law of
nature. We now come, however, to a discovery made in direct interpretation
of Newton's great law of gravitation--the discovery of Neptune from its
observed disturbance of Uranus. I will first briefly recall the main facts
relating to the actual discovery.
[Sidenote: Disturbance of Uranus.]
After Uranus had been discovered and observed sufficiently long for its
orbit to be calculated, it was found that the subsequent position of the
planet did not always agree with this orbit; and, more serious than this,
some early observations were found which could not be reconciled with the
later ones at all. It is a wonderful testimony to the care and sagacity of
Sir William Herschel, as was remarked in the last chapter, that Uranus was
found to have been observed, under the mistaken impression that it was an
ordinary star, by Flamsteed, Lemonnier, Bradley, and Mayer, all observers
of considerable ability. Flamsteed's five observations dated as far back
as 1690, 1712, and 1715; observations by others were in 1748, 1750, 1753,
1756, and so on up to 1771, and the body of testimony was so considerable
that there was no room for doubt as to the irreconcilability of the
observations with the orbit, such as might have been the case had there
been only one or two, possibly affected with some errors.
[Sidenote: Suspicion of perturbing planet.]
It is difficult to mention an exact date for the conversion into certainty
of the suspicion that no single orbit could be found to satisfy all the
observations; but we may certainly regard this fact as established in
1821, when Alexis Bouvard published some tables of the planet, and showed
fully in the introduction that when every correction for the disturbing
action of other planets had been applied, it was still impossible to
reconcile the old observations with the orbit calculated from the new
ones. The idea accordingly grew up that there might be some other body or
bodies attracting the planet and causing these discrepancies. Here again
it is not easy to say exactly when this notion arose, but it was certainly
existent in 1834, as the following letter to the Astronomer Royal will
show. I take it from his well-known "Account of some Circumstances
historically connected with the Discovery of the Planet exterior to
Uranus," which he gave to the Royal Astronomical Society at its first
meeting after that famous discovery (Monthly Notices of the R.A.S., vol.
iii., and Memoirs, vol. xvi.).
NO. 1.--_The_ REV. T. J. HUSSEY _to_ G. B. AIRY.
[_Extract._]
"'HAYES, KENT, _17th November 1834_.
"'With M. Alexis Bouvard I had some conversation upon a subject I had
often meditated, which will probably interest you, and your opinion
may determine mine. Having taken great pains last year with some
observations of _Uranus_, I was led to examine closely Bouvard's
tables of that planet. The apparently inexplicable discrepancies
between the ancient and modern observations suggested to me the
possibility of some disturbing body beyond _Uranus_, not taken into
account because unknown. My first idea was to ascertain some
approximate place of this supposed body empirically, and then with
my large reflector set to work to examine all the minute stars
thereabouts: but I found myself totally inadequate to the former part
of the task. If I could have done it formerly, it was beyond me now,
even supposing I had the time, which was not the case. I therefore
relinquished the matter altogether; but subsequently, in conversation
with Bouvard, I inquired if the above might not be the case: his
answer was, that, as might have been expected, it had occurred to
him, and some correspondence had taken place between Hansen and
himself respecting it. Hansen's opinion was, that one disturbing body
would not satisfy the phenomena; but that he conjectured there were
two planets beyond _Uranus_. Upon my speaking of obtaining the places
empirically, and then sweeping closely for the bodies, he fully
acquiesced in the propriety of it, intimating that the previous
calculations would be more laborious than difficult; that if he had
leisure he would undertake them and transmit the results to me, as
the basis of a very close and accurate sweep. I have not heard from
him since on the subject, and have been too ill to write. What is
your opinion on the subject? If you consider the idea as possible,
can you give me the limits, roughly, between which this body or those
bodies may probably be found during the ensuing winter? As we might
expect an eccentricity [inclination?] approaching rather to that of
the old planets than of the new, the breadth of the zone to be
examined will be comparatively inconsiderable. I may be wrong, but I
am disposed to think that, such is the perfection of my equatoreal's
object-glass, I could distinguish, almost at once, the difference of
light of a small planet and a star. My plan of proceeding, however,
would be very different: I should accurately map the whole space
within the required limits, down to the minutest star I could
discern; the interval of a single week would then enable me to
ascertain any change. If the whole of this matter do not appear to
you a chimæra, which, until my conversation with Bouvard, I was
afraid it might, I shall be very glad of any sort of hint respecting
it.'
"My answer was in the following terms:--
[Sidenote: Airy's scepticism.]
NO. 2.--G. B. AIRY _to the_ REV. T. J. HUSSEY.
[_Extract._]
"'OBSERVATORY, CAMBRIDGE, _1834, Nov. 23_.
"'I have often thought of the irregularity of _Uranus_, and since the
receipt of your letter have looked more carefully to it. It is a
puzzling subject, but I give it as my opinion, without hesitation,
that it is not yet in such a state as to give the smallest hope of
making out the nature of any external action on the planet ... if it
were certain that there were any extraneous action, I doubt much the
possibility of determining the place of a planet which produced it. I
am sure it could not be done till the nature of the irregularity was
well determined from several successive revolutions.'"
[Sidenote: Le Verrier's papers.]
[Sidenote: Planet to be detected by disc.]
[Sidenote: Galle's discovery of the planet.]
Although only a sentence or two have been selected from Airy's reply (he
was not yet Astronomer Royal), they are sufficient to show that the
problem of finding the place of such a possible disturbing body was
regarded at that time as one of extreme difficulty; and no one appears
seriously to have contemplated embarking upon its solution. It was not
until many years later that the solution was attempted. Of the first
attempt we shall speak presently, putting it aside for the moment because
it had no actual bearing on the discovery of the planet, for reasons which
form an extraordinary episode of this history. The attempt which led to
success dates from November 1845. The great French astronomer Le Verrier,
on November 10, 1845, read to the French Academy a paper on the Orbit of
Uranus, considering specially the disturbances produced by Jupiter and
Saturn, and showing clearly that with no possible orbit could the
observations be satisfied. On June 1, 1846, followed a second paper by the
same author, in which he considers all the possible explanations of the
discordance, and concludes that none is admissible except that of a
disturbing planet exterior to Uranus. And assuming, in accordance with
Bode's Law, that the distance of this new planet from the sun would be
about double that of Uranus (and it is important to note this
assumption), he proceeds to investigate the orbit of such a planet, and to
calculate the place where it must be looked for in the heavens. This was
followed by a third paper on August 31st, giving a rather completer
discussion, and arriving at the conclusion that the planet should be
recognisable from its disc. This again is an important point. We remember
that in the discovery of Uranus it needed considerable skill on the part
of Sir William Herschel to detect the disc, to see in fact any difference
between it and surrounding stars; and that other observers, even when
their attention had been called to the planet, found it difficult to see
this difference. It might be expected, therefore, that with a planet twice
as far away (as had been assumed for the new planet) the disc would be
practically unrecognisable, and as we shall presently see, this assumption
was made in some searches for the planet which had been commenced even
before the publication of this third paper. Le Verrier's courageous
announcement, which he deduced from a consideration of the mass of the
planet, that the disc should be recognisable, led immediately to the
discovery of the suspected body. He wrote to a German astronomer, Dr.
Galle (still, I am glad to say, alive and well, though now a very old
man), telling him the spot in the heavens to search, and stating that he
might expect to detect the planet by its appearance in this way; and the
same night Dr. Galle, by comparing a star map with the heavens, found the
planet.
[Sidenote: Adams' work publicly announced.]
To two points to which I have specially called attention in this brief
summary--namely, the preliminary assumption that the planet would be,
according to Bode's Law, twice as far away as Uranus; secondly, the
confident assertion that it would have a visible disc--I will ask you to
add, thirdly, that it was found by the aid of a star map, for this map
played an important part in the further history to which we shall now
proceed. It may naturally be supposed that the announcement of the finding
of a planet in this way, the calculation of its place from a belief in the
universal action of the great Law of Gravitation, the direction to an
eminent observer to look in that place for a particular thing, and his
immediate success,--this extraordinary combination of circumstances caused
a profound sensation throughout not only the astronomical, but the whole
world; and this sensation was greatly enhanced by the rumour which had
begun to gather strength that, but for some unfortunate circumstances, the
discovery might have been made even earlier and as a consequence of
totally independent calculations made by a young Cambridge mathematician,
J. C. Adams. Some of you are doubtless already familiar with the story in
its abridged form, for it has been scattered broadcast through literature.
In England it generally takes the form of emphasising the wickedness or
laziness of the Astronomer Royal who, when told where to look for a
planet, neglected his obvious duty, so that in consequence another
astronomer who made the calculation much later and gave a more virtuous
observer the same directions where to look, obtained for France the glory
of a discovery which ought to have been retained in England. There is no
doubt that Airy's conduct received a large amount of what he called
"savage abuse." When the facts are clearly stated I think it will be
evident that many of the harsh things said of him were scarcely just,
though at the same time it is also difficult to understand his conduct at
two or three points of the history, even as explained by himself.
[Sidenote: Facts undoubted.]
There is fortunately no doubt whatever about any of the _facts_. Airy
himself gave a very clear and straightforward account of them at the time,
for which more credit is due to him than he commonly receives; and since
the death of the chief actors in this sensational drama they have been
naturally again ransacked, with the satisfactory result that there is
practically no doubt about any of the facts. As to the proper
interpretations of them there certainly may be wide differences of
opinion, nor does this circumstance detract from their interest. It is
almost impossible to make a perfectly colourless recital of them, nor is
it perhaps necessary to do so. I will therefore ask you to remember in
what I now say that there is almost necessarily an element of personal
bias, and that another writer would probably give a different colouring.
Having said this, I hope I may speak quite freely as the matter appears in
my personal estimation.
[Sidenote: Airy's "Account."]
[Sidenote: "A movement of the age."]
Airy's account was, as above stated, given to the Royal Astronomical
Society at their first meeting (after the startling announcement of the
discovery of the new planet), on November 13, 1846, and I have already
quoted an extract from it. He opens with a tribute to the sensational
character of the discovery, and then states that although clearly due to
two individuals (namely, Le Verrier and Galle), it might also be regarded
as to some extent the consequence of a movement of the age. His actual
words are these: "The principal steps in the theoretical investigations
have been made by one individual, and the published discovery of the
planet was necessarily made by one individual. To these persons the public
attention has been principally directed; and well do they deserve the
honours which they have received, and which they will continue to receive.
Yet we should do wrong if we considered that these two persons alone are
to be regarded as the authors of the discovery of this planet. I am
confident that it will be found that the discovery is a consequence of
what may properly be called a movement of the age; that it has been urged
by the feeling of the scientific world in general, and has been nearly
perfected by the collateral, but independent labours, of various persons
possessing the talents or powers best suited to the different parts of
the researches."
[Sidenote: Airy under-estimated Adams' work.]
I have quoted these words as the first point at which it is difficult to
understand Airy's conduct in excluding from them all specific mention of
Adams, knowing as he did the special claims which entitled him to such
mention; claims indeed which he proceeded immediately to make clear. It
seems almost certain that Airy entirely under-estimated the value of
Adams' work throughout. But this will become clearer as we proceed. The
"account" takes the form of the publication of a series of letters with
occasional comments. Airy was a most methodical person, and filed all his
correspondence with great regularity. It was jestingly said of him once
that if he wiped his pen on a piece of blotting-paper, he would date the
blotting-paper and file it for reference. The letters reproduced in this
"account" are still in the Observatory at Greenwich, pinned together just
as Airy left them; and in preparing his "account" it was necessary to do
little else than to have them copied out and interpolate comments. From
two of them I have already quoted to show how difficult the enterprise of
finding an exterior planet from its action on Uranus was considered in
1834. To these may be added the following sentence from No. 4, dated 1837.
"If it be the effect of any unseen body," writes Airy to Bouvard, "it will
be nearly impossible ever to find out its place." But the first letter
which need concern us is No. 6, and it is only necessary to explain that
Professor Challis was the Professor of Astronomy at Cambridge, and in
charge of the Cambridge Observatory, in which offices he had succeeded
Airy himself on his leaving Cambridge for Greenwich some eight years
earlier.
No. 6.--PROFESSOR CHALLIS _to_ G. B. AIRY.
[_Extract._]
"'CAMBRIDGE OBSERVATORY, _Feb. 13, 1844_.
[Sidenote: Challis mentions Adams to Airy, and suggests Adams' visit
to Greenwich.]
"'A young friend of mine, Mr. Adams of St. John's College, is working
at the theory of _Uranus_, and is desirous of obtaining errors of the
tabular geocentric longitudes of this planet, when near opposition,
in the years 1818-1826, with the factors for reducing them to errors
of heliocentric longitude. Are your reductions of the planetary
observations so far advanced that you could furnish these data? and
is the request one which you have any objection to comply with? If
Mr. Adams may be favoured in this respect, he is further desirous of
knowing, whether in the calculation of the tabular errors any
alterations have been made in Bouvard's _Tables of Uranus_ besides
that of _Jupiter's_ mass.'
"My answer to him was as follows:--
No. 7.--G. B. AIRY _to_ PROFESSOR CHALLIS.
[_Extract._]
"'ROYAL OBSERVATORY, GREENWICH, _1844, Feb. 15_.
"'I send all the results of the observations of _Uranus_ made with
both instruments (that is, the heliocentric errors of _Uranus_ in
longitude and latitude from 1754 to 1830, for all those days on which
there were observations, both of right ascension and of polar
distance). No alteration is made in Bouvard's _Tables of Uranus_
except in increasing the two equations which depend on _Jupiter_ by
1/50 part. As constants have been added (in the printed tables) to
make the equations positive, and as 1/50 part of the numbers in the
tables has been added, 1/50 part of the constants has been subtracted
from the final results.'
"Professor Challis in acknowledging the receipt of these, used the
following expressions:--
No. 8.--PROFESSOR CHALLIS _to_ G. B. AIRY.
[_Extract._]
"'CAMBRIDGE OBSERVATORY, _Feb. 16, 1844_.
"'I am exceedingly obliged by your sending so complete a series of
tabular errors of _Uranus_.... The list you have sent will give Mr.
Adams the means of carrying on in the most effective manner the
inquiry in which he is engaged.'
"The next letter shows that Mr. Adams has derived results from these
errors.
No. 9.--PROFESSOR CHALLIS _to_ G. B. AIRY.
"'CAMBRIDGE OBSERVATORY, _Sept. 22, 1845_.
"'My friend Mr. Adams (who will probably deliver this note to you)
has completed his calculations respecting the perturbation of the
orbit of _Uranus_ by a supposed ulterior planet, and has arrived at
results which he would be glad to communicate to you personally, if
you could spare him a few moments of your valuable time. His
calculations are founded on the observations you were so good as to
furnish him with some time ago; and from his character as a
mathematician, and his practice in calculation, I should consider the
deductions from his premises to be made in a trustworthy manner. If
he should not have the good fortune to see you at Greenwich, he hopes
to be allowed to write to you on this subject.'
"On the day on which this letter was dated, I was present at a
meeting of the French Institute. I acknowledged it by the following
letter:--
NO. 10.--G. B. AIRY _to_ PROFESSOR CHALLIS.
"'ROYAL OBSERVATORY, GREENWICH, _1845, Sept. 29_.
"'I was, I suppose, on my way from France, when Mr. Adams called
here; at all events, I had not reached home, and therefore, to my
regret, I have not seen him. Would you mention to Mr. Adams that I am
very much interested with the subject of his investigations, and that
I should be delighted to hear of them by letter from him?'
"On one of the last days of October 1845, Mr. Adams called at the
Royal Observatory, Greenwich, in my absence and left the following
important paper:--
No. 11.--J. C. ADAMS, Esq., _to_ G. B. AIRY.
[Sidenote: Adams' announcement of the new planet.]
"'According to my calculations, the observed irregularities in the
motion of _Uranus_ may be accounted for by supposing the existence of
an exterior planet, the mass and orbit of which are as follows:--
Mean distance (assumed nearly in accordance
with Bode's Law) 38.4
Mean sidereal motion in 365.25 days 1°30'.9
Mean longitude, 1st October 1845 323 34
Longitude of perihelion 315 55
Eccentricity 0.1610.
Mass (that of the sun being unity) 0.0001656.
For the modern observations I have used the method of normal places,
taking the mean of the tabular errors, as given by observations near
three consecutive oppositions, to correspond with the mean of the
times; and the Greenwich observations have been used down to 1830:
since which, the Cambridge and Greenwich observations, and those
given in the _Astronomische Nachrichten_, have been made use of. The
following are the remaining errors of mean longitude:--
_Observation--Theory._
"
1780 +0.27
1783 -0.23
1786 -0.96
1789 +1.82
1792 -0.91
1795 +0.09
1798 -0.99
1801 -0.04
1804 +1.76
1807 -0.21
1810 +0.56
1813 -0.94
1816 -0.31
1819 -2.00
1822 +0.30
1825 +1.92
1828 +2.25
1831 -1.06
1834 -1.44
1837 -1.62
1840 +1.73
The error for 1780 is concluded from that for 1781 given by
observation, compared with those of four or five following years, and
also with Lemonnier's observations in 1769 and 1771.
"'For the ancient observations, the following are the remaining
errors:--
_Observation--Theory._
"
1690 +44.4
1712 + 6.7
1715 - 6.8
1750 - 1.6
1753 + 5.7
1756 - 4.0
1763 - 5.1
1769 + 0.6
1771 +11.8
The errors are small, except for Flamsteed's observation of 1690.
This being an isolated observation, very distant from the rest, I
thought it best not to use it in forming the equations of condition.
It is not improbable, however, that this error might be destroyed by
a small change in the assumed mean motion of the planet.'
"I acknowledged the receipt of this paper in the following terms:--
NO. 12.--G. B. AIRY _to_ J. C. ADAMS, Esq.
"'ROYAL OBSERVATORY, GREENWICH, _1845, Nov. 5_.
[Sidenote: Airy's inquiry about the "radius vector."]
"'I am very much obliged by the paper of results which you left here
a few days since, showing the perturbations on the place of _Uranus_
produced by a planet with certain assumed elements. The latter
numbers are all extremely satisfactory: I am not enough acquainted
with Flamsteed's observations about 1690 to say whether they bear
such an error, but I think it extremely probable.
"'But I should be very glad to know whether this assumed perturbation
will explain the error of the radius vector of _Uranus_. This error
is now very considerable, as you will be able to ascertain by
comparing the normal equations, given in the Greenwich observations
for each year, for the times _before_ opposition with the times
_after_ opposition.'
"I have before stated that I considered the establishment of this
error of the radius vector of _Uranus_ to be a very important
determination. I therefore considered that the trial, whether the
error of radius vector would be explained by the same theory which
explained the error of longitude, would be truly an _experimentum
crucis_. And I waited with much anxiety for Mr. Adams' answer to my
query. Had it been in the affirmative, I should at once have exerted
all the influence which I might possess, either directly, or
indirectly through my friend Professor Challis, to procure the
publication of Mr. Adams' theory.
"From some cause with which I am unacquainted, probably an accidental
one, I received no immediate answer to this inquiry. I regret this
deeply, for many reasons."
[Sidenote: Adams' silence.]
Here we may leave Airy's "account" for a few moments to consider the
reason why he received no answer. Adams was a very shy and retiring young
man, and very sensitive; though capable of a great resolution, and of
enormous perseverance in carrying it out. We know (what is not indicated
in the above account), how steadily he had kept in view the idea of
solving this great problem. It was characteristic of him that as early as
1841 he had formed a resolution to undertake it, although at the time he
was not able to enter upon its accomplishment. The following memorandum,
which is still in existence, having been found among his papers after his
death, records these facts:
"1841, July 3. Formed a design, in the beginning of this week, of
investigating, as soon as possible after taking my degree, the
irregularities in the motion of Uranus, which were as yet unaccounted
for: in order to find whether they may be attributed to the action of
an undiscovered planet beyond it, and if possible thence to determine
the elements of its orbit, &c., approximately, which would probably
lead to its discovery."
Accordingly, "as soon as possible after taking his degree" he embarked
upon the enterprise, and the first solution was made in the long vacation
of 1843, assuming the orbit of the unknown planet to be a circle with a
radius equal to twice the mean distance of Uranus from the sun (an
assumption which, as we have seen, was also made by Le Verrier). Having
satisfied himself that there was a good general agreement between his
results and the observations, Adams began a more complete solution; indeed
from first to last he made no less than six separate solutions, the one
which he announced to Airy in the above letter being the fourth. Hence he
had already done an enormous amount of work on the problem, and was in his
own mind so justly convinced of the correctness and value of his results
that he was liable to forget that others had not had the same opportunity
of judging of their completeness; and he was grievously disappointed when
his announcement was not received with full confidence.
[Sidenote: His disappointment at Greenwich, and at Airy's question.]
But perhaps it should first be stated that by a series of mischances Adams
had been already much disappointed at the failure of his attempts to see
the Astronomer Royal on his visits to Greenwich. This does not seem to
have been exactly Airy's fault; he was, as may well be supposed, an
extremely busy man, and was much occupied at the time on a question of
great practical importance, at the direct request of the Government,
namely, the settling of the proper gauge for railways throughout the
country. The first time Adams called to see him, he was actually in London
sitting on the Committee which dealt with this question, and Adams was
asked to call later; when the visit was repeated, Airy was unfortunately
at dinner (and it may be added that his hours for dinner were somewhat
peculiar), and the butler, acting somewhat in the manner of his kind,
protected his master's dinner by sending away one whom he doubtless
regarded as a troublesome visitor. There is, as I have said, little doubt
about any of the facts, and it seems well established that Airy himself
did not learn of Adams' visits until afterwards, and it would scarcely be
just to blame him for a servant's oversight. But Adams had left the paper
above reproduced, and Airy with his business-like habits ultimately
proceeded to deal with it; he wrote the answer given above asking Adams a
definite question, filed a copy of it with the original letter, and then
dismissed the matter from his thoughts until the reply from Adams, which
he confidently expected should again bring it under notice.
This further disappointment was, however, too much for Adams; he regarded
the question put by Airy as having so obvious an answer that it was
intended as an evasion, though this was far from being the case. Airy was
thoroughly in earnest about his question, though it must be admitted that
a more careful study of the problem would have shown him that it was
unnecessary. Later, when he learnt of Le Verrier's researches, he put the
same question to him, and received a polite but very clear answer, showing
that the suggested test was not an _experimentum crucis_ as he supposed.
But Adams did not feel equal to making this reply; he shrank into his
shell and solaced himself only by commencing afresh another solution of
the problem which had so engrossed his life at that time.
[Sidenote: The merits of Airy's question.]
[Sidenote: The range of possibilities.]
I have heard severe or contemptuous things said about this question by
those who most blame Airy. Some of them have no hesitation in accusing him
of intellectual incompetence: they say that it was the question of a
stupid man. I think that in the first place they forget the difference
between a deliberate error of judgement and a mere consequence of
insufficient attention. But there is even more than this to be said in
defence of the question. The "error of radius vector" came before Airy in
an entirely independent way, and as an entirely independent phenomenon,
from the "error of longitude," and there was nothing unnatural in
regarding it as requiring independent explanation. It is true that, _as
the event proved_, a mere readjustment of the orbit of Uranus got rid of
this error of radius vector (this was substantially Le Verrier's answer to
Airy's question); but we must not judge of what was possible before the
event in the light of what we now know. The original possibilities were
far wider, though we have forgotten their former extent now that they have
been narrowed down by the discovery. If a sentry during war time hears a
noise in a certain direction, he may be compelled to make the assumption
that it is the movement of an enemy; and if he fires in that direction and
kills him, and thus saves his own army from destruction, he is deservedly
applauded for the success which attends his action. But it does not
follow that the assumption on which he acted was the only possible one.
Or, to take a more peaceful illustration, in playing whist it sometimes
becomes apparent that the game can only be won if the cards lie in a
certain way; and a good player will thereupon assume that this is the
fact, and play accordingly. Adams and Le Verrier played to win the game on
the particular assumption that the disturbance of Uranus was due to an
external planet revolving at a distance from the sun about twice that of
Uranus; _and won it_; and we applaud them for doing so. But it is easy to
imagine a rearrangement of the cards with which they would have lost it;
and Airy's question simply meant that he was alive to these wider
possibilities, and did not see the need for attempting to win the game in
that particular way.
One such alternative possibility has already been mentioned. "Hansen's
opinion was, that one disturbing body would not satisfy the phenomena; but
he conjectured that there were two planets beyond _Uranus_." Another
conceivable alternative is that there was some change in the law of
gravitation at the distance of Uranus, which, it must be remembered, is
twice as great as that of any planet previously known. Or some wandering
body might have passed close enough to Uranus to change its orbit somewhat
suddenly. We now know, for instance, that the swarm of meteorites which
gives rise to the well-known "November meteors" must have passed very
close to Uranus in A.D. 126, assuming that neither the planet nor the
swarm have been disturbed in any unknown manner in the meantime. It is to
this encounter that we owe the introduction of this swarm to our solar
system: wandering through space, they met Uranus, and were swept by his
attraction into an orbit round the sun. Was there no reaction upon Uranus
himself? The probabilities are that the total mass of the swarm was so
small as to affect the huge planet inappreciably; but who was to say that
some other swarm of larger mass, or other body, might not have approached
near Uranus at some date between 1690 and 1845, and been responsible at
any rate in part for the observed errors? These are two or three
suppositions from our familiar experience; and there are, of course,
limitless possibilities beyond. Which is the true scientific attitude, to
be alive to them all, or to concentrate attention upon one?
But we are perhaps wandering too far from the main theme. It is easy to do
so in reviewing this extraordinary piece of history, for at almost every
point new possibilities are suggested.
[Illustration:
III--U. J. LE VERRIER.
(_From a print in the possession of the Royal Astronomical Society._)]
[Illustration:
IV--J. G. GALLE.
WHO FIRST SAW THE PLANET NEPTUNE]
[Sidenote: Airy receives Le Verrier's memoir.]
We must return, however, to Airy's "account." We reached the point where
he had written to Adams (on November 5, 1845), asking his question about
the radius vector, and received no reply; and there the matter remained,
so far as he was concerned, until the following June, when Le Verrier's
memoir reached him; and we will let him give his own version of the
result.
"This memoir reached me about the 23rd or 24th of June. I cannot
sufficiently express the feeling of delight and satisfaction which I
received from it. The place which it assigned to the disturbing
planet was the same, to one degree, as that given by Mr. Adams'
calculations, which I had perused seven months earlier. To this time
I had considered that there was still room for doubt of the accuracy
of Mr. Adams' investigations; for I think that the results of
algebraic and numerical computations, so long and so complicated as
those of an inverse problem of perturbations, are liable to many
risks of error in the details of the process: I know that there are
important numerical errors in the _Mécanique Céleste_ of Laplace; in
the _Théorie de la Lune_ of Plana; above all, in Bouvard's first
tables of _Jupiter_ and _Saturn_; and to express it in a word, I have
always considered the correctness of a distant mathematical result to
be a subject rather of moral than of mathematical evidence. But now I
felt no doubt of the accuracy of both calculations, as applied to the
perturbation in longitude. I was, however, still desirous, as before,
of learning whether the perturbation in radius vector was fully
explained. I therefore addressed to M. Le Verrier the following
letter:--
No. 13.--G. B. AIRY _to_ M. LE VERRIER.
"'Royal Observatory, Greenwich, _1846, June 26_.
[Sidenote: He puts the "radius-vector" question to Le Verrier, but
makes no mention of Adams.]
"'I have read, with very great interest, the account of your
investigations on the probable place of a planet disturbing the
motions of _Uranus_, which is contained in the _Compte Rendu de
l'Académie_ of June 1; and I now beg leave to trouble you with the
following question. It appears, from all the later observations of
_Uranus_ made at Greenwich (which are most completely reduced in the
_Greenwich Observations_ of each year, so as to exhibit the effect of
an error either in the tabular heliocentric longitude, or the tabular
radius vector), that the tabular radius vector is considerably too
small. And I wish to inquire of you whether this would be a
consequence of the disturbance produced by an exterior planet, now in
the position which you have indicated?'"
There is more of the letter, but this will suffice to show that he wrote
to Le Verrier in the same way as to Adams, and, as already stated,
received a reply dated three or four days later. But the rest of the
letter contains no mention of Adams, and thus arises a second difficulty
in understanding Airy's conduct. It seems extraordinary that when he
wrote to Le Verrier he made no mention of the computations which he had
previously received from Adams; or that he should not have written to
Adams, and made some attempt to understand his long silence, now that, as
he himself states, he "felt no doubt of the accuracy of both
calculations." The omission may have been, and probably was, mere
carelessness or forgetfulness; but he could hardly be surprised if others
mistook it for deliberate action.
[Sidenote: Airy announces the likelihood of a new planet, and suggests a
search for it at Cambridge not having suitable telescope at Greenwich]
However, attention had now been thoroughly attracted to the near
possibility of finding the planet. On June 29, 1846, there was a special
meeting of the Board of Visitors of Greenwich Observatory, and Airy
incidentally mentioned to them this possibility. The impression produced
must have been definite and deep; for Sir John Herschel, who was present,
was bold enough to say on September 10th following to the British
Association assembled at Southampton: "We see it (the probable new planet)
as Columbus saw America from the shores of Spain. Its movements have been
felt trembling along the far-reaching line of our analysis with a
certainty hardly inferior to that of ocular demonstration." Airy discussed
the matter with Professor Challis (who, it will be remembered, had
originally written to him on behalf of Adams), suggesting that he should
immediately commence a search for the supposed planet at Cambridge. It may
be asked why Airy did not commence this search himself at Greenwich, and
the answer is that he had no telescope which he regarded as large enough
for the purpose. The Royal Observatory at Greenwich has always been, and
is now, better equipped in some respects than any other observatory, as
might be expected from its deservedly great reputation; but to possess the
largest existing telescope has never been one of its ambitions. The
instruments in which it takes most pride are remarkable for their
steadiness and accuracy rather than for their size; and at that time the
best telescope possessed by the observatory was not, in Airy's opinion,
large enough to detect the planet with certainty. In this opinion we now
know that he was mistaken; but, again, we must not judge his conduct
before the event in the light of what we have since discovered. It may be
recalled here that it was not until Le Verrier's third paper, published on
August 31, that he (Le Verrier) emphatically pointed out that the new
planet might be of such a size as to have a sensible disc; and it was this
remark which led immediately to its discovery. Until this was so
decisively stated, it must have seemed exceptionally improbable; for we
saw in the last chapter how diligently the Zodiac had been swept in the
search for minor planets,--how, for instance, Hencke had searched for
fifteen years without success; and it might fairly be considered that if
there were a fairly bright object (such as Neptune has since been found to
be) it would have been discovered earlier. Hence Airy not unreasonably
considered it necessary to spread his net for very small objects. On July
9 he wrote to Professor Challis as follows:--
No. 15.--G. B. AIRY _to_ PROFESSOR CHALLIS.
"THE DEANERY, ELY, _1846, July 9_.
"You know that I attach importance to the examination of that part of
the heavens in which there is ... reason for suspecting the existence
of a planet exterior to _Uranus_. I have thought about the way of
making such examination, but I am convinced that (for various
reasons, of declination, latitude of place, feebleness of light, and
regularity of superintendence) there is no prospect whatever of its
being made with any chance of success, except with the Northumberland
telescope.
"Now, I should be glad to ask you, in the first place, whether you
could make such an examination?
"Presuming that your answer would be in the negative, I would ask,
secondly, whether, supposing that an assistant were supplied to you
for this purpose, you would superintend the examination?
"You will readily perceive that all this is in a most unformed state
at present, and that I am asking these questions almost at a venture,
in the hope of rescuing the matter from a state which is, without the
assistance that you and your instruments can give, almost desperate.
Therefore I should be glad to have your answer, not only responding
simply to my questions, but also entering into any other
considerations which you think likely to bear on the matter.
"The time for the said examination is approaching near."
[Sidenote: Challis undertakes the search.]
[Sidenote: He finds too late that he had observed the planet.]
Professor Challis did not require an assistant, but determined to
undertake the work himself, and devised his own plan of procedure; but he
also set out on the undertaking with the expectation of a long and arduous
search. No such idea as that of finding the planet on the first night ever
entered his head. For one thing, he had no map of the region to be
examined, for although the map used by Galle had been published, no copy
of it had as yet reached Cambridge, and Professor Challis had practically
to construct a map for himself. In these days of photography to make such
a map is a simple matter, but at that time the process was terribly
laborious. "I get over the ground very slowly," he wrote on September 2nd
to Airy, "thinking it right to include all stars to 10-11 magnitude; and I
find that to scrutinise thoroughly in this way the proposed portion of the
heavens will require many more observations than I can take this year."
With such a prospect, it is not surprising that one night's observations
were not even compared with the next; there would be a certain economy in
waiting until a large amount of material had been accumulated, and then
making the comparisons all together, and this was the course adopted. But
when Le Verrier's third paper, with the decided opinion that the planet
would be bright enough to be seen by its disc, ultimately reached
Professor Challis, it naturally gave him an entirely different view of the
possibilities; he immediately began to compare the observations already
made, and found that he had observed the planet early in August. But it
was now too late to be first in the field, for Galle had already made his
announcement of discovery. Writing to Airy on October 12, Challis could
only lament that after four days' observing the planet was in his grasp,
_if_ only he had examined or mapped the observations, and _if_ he had not
delayed doing so until he had more observations to reduce, and _if_ he had
not been very busy with some comet observations. Oh! these terrible _ifs_
which come so often between a man and success! The third of them is a
peculiarly distressing one, for it represents that eternal conflict
between one duty and another, which is so constantly recurring in
scientific work. Shall we finish one piece of work now well under way, or
shall we attend to something more novel and more attractive? Challis
thought his duty lay in steadily completing the comet observations already
begun. We saw in the last lecture how the steady pursuit of the discovery
of minor planets, a duty which had become tedious and apparently led
nowhere, suddenly resulted in the important discovery of Eros. But
Challis was not so fortunate in electing to plod along the beaten track;
he would have done _better_ to leave it. There is no golden rule for the
answer; we must be guided in each case by the special circumstances, and
the dilemma is consequently a new one on every occasion, and perhaps the
more trying with each repetition.
[Sidenote: Sensation caused by the discovery.]
[Sidenote: Not all _national_ jealousy.]
Such are briefly the events which led to the discovery of Neptune, which
was made in Germany by direction from France, when it might have been made
in Cambridge alone. The incidents created a great stir at the time. The
"Account" of them, as read by Airy to the Royal Astronomical Society on
November 13, 1846, straightforward and interesting though it was, making
clear where he had himself been at fault, nevertheless stirred up angry
passions in many quarters, and chiefly directed against Airy himself.
Cambridge was furious at Airy's negligence, which it considered
responsible for costing the University a great discovery; and others were
equally irate at his attempting to claim for Adams some of that glory
which they considered should go wholly to Le Verrier. But it may be
remarked that feeling was not purely national. Some foreigners were
cordial in their recognition of the work of Adams, while some of those
most eager to oppose his claims were found in this country. In their
anxiety to show that they were free from national jealousy, scientific
men went almost too far in the opposite direction.
[Sidenote: The position of Cambridge in the matter.]
[Sidenote: Challis the weakest point.]
Airy's conduct was certainly strange at several points, as has already
been remarked. One cannot understand his writing to Le Verrier in June
1846 without any mention of Adams. He could not even momentarily have
forgotten Adams' work; for he tells us himself how he noticed the close
correspondence of his result with that of Le Verrier: and had he even
casually mentioned this fact in writing to the latter, it would have
prepared the way for his later statement. But we can easily understand the
unfavourable impression produced by this statement after the discovery had
been made, when there had been no previous hint on the subject at all. Of
those who abused him Cambridge had the least excuse; for there is no doubt
that with a reasonably competent Professor of Astronomy in Cambridge, she
need not have referred to Airy at all. It would not seem to require any
great amount of intelligence to undertake to look in a certain region for
a strange object if one is in possession of a proper instrument. We have
seen that Challis had the instrument, and when urged to do so was equal to
the task of finding the planet; but he was a man of no initiative, and the
idea of doing so unless directed by some authority never entered his head.
He had been accustomed for many years to lean rather helplessly upon Airy,
who had preceded him in office at Cambridge. For instance, when appointed
to succeed him, and confronted with the necessity of lecturing to
students, he was so helpless that he wrote to implore Airy to come back to
Cambridge and lecture for him; and this was actually done, Airy obtaining
leave from the Government to leave his duties at Greenwich for a time in
order to return to Cambridge, and show Challis how to lecture. Now it
seems to me that this helplessness was the very root of all the mischief
of which Cambridge so bitterly complained. I claimed at the outset the
privilege of stating my own views, with which others may not agree: and of
all the mistakes and omissions made in this little piece of history, the
most unpardonable and the one which had most serious consequences seems to
me to be this: that Challis never made the most casual inquiry as to the
result of the visit to Greenwich which he himself had directed Adams to
make. I am judging him to some extent by default; because I assume the
facts from lack of evidence to the contrary: but it seems practically
certain that after sending this young man to see Airy on this important
topic, Challis thereupon washed his hands of all responsibility so
completely that he never even took the trouble to inquire on his return,
"Well! how did you get on? What did the Astronomer Royal say?" Had he put
this simple question, which scarcely required the initiative of a machine,
and learnt in consequence, as he must have done, that the sensitive young
man thought Airy's question trivial, and did not propose to answer it, I
think we might have trusted events to right themselves. Even Challis might
have been trusted to reply, "Oh! but you must answer the Astronomer
Royal's question: you may think it stupid, but you had better answer it
politely, and show him that you know what you are about." It is
unprofitable to pursue speculation further; this did _not_ happen, and
something else did. But I have always felt that my old University made a
scapegoat of the wrong man in venting its fury upon Airy, when the real
culprit was among themselves, and was the man they had themselves chosen
to represent astronomy. He was presumably the best they had; but if they
had no one better than this, they should not have been surprised, and must
not complain, if things went wrong. If a University is ambitious of doing
great things, it must take care to see that there are men of ability and
initiative in the right places. This is a most difficult task in any case,
and we require all possible incentives towards it. To blink the facts when
a weak spot is mercilessly exposed by the loss of a great opportunity is
to lose one kind of incentive, and perhaps not the least valuable.
[Sidenote: Curious difference between actual and supposed planet.]
[Sidenote: Professor Peirce's contention that the discovery was a mere
accident.]
[Sidenote: The explanation.]
Let us now turn to some curious circumstances attending this remarkable
discovery of a planet by mathematical investigation, of which there are
several. The first is, that although Neptune was found so near the place
where it was predicted, its orbit, after discovery, proved to be very
different from that which Adams and Le Verrier had supposed. You will
remember that both calculators assumed the distance from the sun, in
accordance with Bode's Law, to be nearly twice that of Uranus. The actual
planet was found to have a mean distance less than this by 25 per cent.,
an enormous quantity in such a case. For instance, if the supposed planet
and the real were started round the sun together, the real planet would
soon be a long way ahead of the other, and the ultimate disturbing effect
of the two on Uranus would be very different. To explain the difference,
we must first recall a curious property of such disturbances. When two
planets are revolving, so that one takes just twice or three times, or any
exact number of times, as long to revolve round the sun as the other, the
usual mathematical expressions for the disturbing action of one planet on
the other would assign an _infinite_ disturbance, which, translated into
ordinary language, means that we must start with a fresh assumption, for
this state of things cannot persist. If the period of one were a little
_longer_ than this critical value, some of the mathematical expressions
would be of contrary sign from those corresponding to a period a little
_shorter_. Now it is curious that the supposed planet and the real had
orbits on opposite sides of a critical value of this kind, namely, that
which would assign a period of revolution for Neptune exactly half that of
Uranus; and it was pointed out in America by Professor Peirce that the
effect of the planet imagined by Adams and Le Verrier was thus totally
different from that of Neptune. He therefore declared that the
mathematical work had not really led to the discovery at all; but that it
had resulted from mere coincidence, and this opinion--somewhat paradoxical
though it was--found considerable support. It was not replied to by Adams
until some thirty years later, when a short reply was printed in
_Liouville's Journal_. The explanation is this: the expressions considered
by Professor Peirce are those representing the action of the planet
throughout an indefinite past, and did not enter into the problem, which
would have been precisely the same if Neptune had been suddenly created in
1690; while, on the other hand, if Neptune had existed up till 1690 (the
time when Uranus was first observed, although unknowingly), and then had
been destroyed, there would have been no means of tracing its previous
existence. In past ages it had no doubt been perturbing the orbit of
Uranus, and had effected large changes in it; but if it had then been
suddenly destroyed, we should have had no means of identifying these
changes. There might have been instead of Neptune another planet, such as
that supposed by Adams and Le Verrier; and its action in all past time
would have been very different from that of Neptune, as is properly
represented in the mathematical expressions which Professor Peirce
considered. In consequence the orbit of Uranus in 1690 would have been
very different from the orbit as it was actually found; but in either case
the mathematicians Adams and Le Verrier would have had to take it as they
found it; and the disturbing action which they considered in their
calculations was the comparatively small disturbance which began in 1690
and ended in 1846. During this limited number of years the disturbance of
the planet they imagined, although not precisely the same as that of
Neptune, was sufficiently like it to give them the approximate place of
the planet.
Still it is somewhat bewildering to look at the mathematical expressions
for the disturbances as used by Adams and Le Verrier, when we can now
compare with them the actual expressions to which they ought to
correspond; and one may say frankly that there seems to be no sort of
resemblance. Recently a memorial of Adams' work has been published by the
Royal Astronomical Society; they have reproduced in their Memoirs a
facsimile of Adams' MS. containing the "first solution," which he made in
1843 in the Long Vacation after he had taken his degree, and which would
have given the place of Neptune at that time with an error of 15°. In an
introduction describing the whole of the MSS., written by Professor R. A.
Sampson of Durham, it is shown how different the actual expressions for
Neptune's influence are from those used by Adams, and it is one of the
curiosities of this remarkable piece of history that some of them seem to
be actually _in the wrong direction_; and others are so little alike that
it is only by fixing our attention resolutely on the considerations above
mentioned that we can realise that the analytical work did indeed lead to
the discovery of the planet.
[Sidenote: Suggested elementary method for finding Neptune illusory.]
A second curiosity is that a mistaken idea should have been held by at
least one eminent man (Sir J. Herschel), to the effect that it would have
been possible to find the place of the planet by a much simpler
mathematical calculation than that actually employed by Adams or Le
Verrier. In his famous "Outlines of Astronomy" Sir John Herschel describes
a simple graphical method, which he declares would have indicated the
place of the planet without much trouble. Concerning it I will here merely
quote Professor Sampson's words:--
"The conclusion is drawn that _Uranus_ arrived at a conjunction with
the disturbing planet about 1822; and this was the case. Plausible as
this argument may seem, it is entirely baseless. For the maximum of
perturbations depending on the eccentricities has no relation to
conjunction, and the others which depend upon the differences of the
mean motions alone are of the nature of forced oscillations, and
conjunction is not their maximum or stationary position, but their
position of most rapid change."
Professor Sampson goes on to show that a more elaborate discussion seems
quite as unpromising; and he concludes that the refinements employed were
not superfluous, although it seems _now_ clear that a different mode of
procedure might have led more certainly to the required conclusion.
[Sidenote: The evil influence of Bode's Law.]
For the third curious point is that both calculators should have adhered
so closely to Bode's Law. If they had not had this guiding principle it
seems almost certain that they would have made a better approximation to
the place of the planet, for instead of helping them it really led them
astray. We have already remarked that if two planets are at different
distances from the sun, however slight, and if they are started in their
revolution together, they must inevitably separate in course of time, and
the amount of separation will ultimately become serious. Thus by assuming
a distance for the planet which was in error, however slight, the
calculators immediately rendered it impossible for themselves to obtain a
place for the planet which should be correct for more than a very brief
period. Professor Sampson has given the following interesting lists of the
dates at which Adams' six solutions gave the true place of the planet and
the intervals during which the error was within 5° either way.
I. II. III. IV. V. VI.
Correct 1820 1835 1872 1830 1861 1856
Within ±5° {1812 1827 1865 1813 1815 1826
{1827 1842 1877 1866 1871 1868
Now the date at which it was most important to obtain the correct place
was 1845 or thereabouts when it was proposed to look for the planet; but
no special precaution seems to have been taken by either investigator to
secure any advantage for this particular date. Criticising the procedure
after the event (and of course this is a very unsatisfactory method of
criticism), we should say that it would have been better to make several
assumptions as regards the distance instead of relying upon Bode's Law;
but no one, so far as I know, has ever taken the trouble to write out a
satisfactory solution of the problem as it might have been conducted. Such
a solution would be full of interest, though it could only have a small
weight in forming our estimation of the skill with which the problem was
solved in the first instance.
[Sidenote: Le Verrier's erroneous limits.]
Fourthly, we may notice a very curious point. Le Verrier went to some
trouble not only to point out the most likely place for the planet, but to
indicate limits outside which it was not necessary to look. This part of
his work is specially commented upon with enthusiasm by Airy, and I will
reproduce what he says. It is rather technical perhaps, but those who
cannot follow the mathematics will be able to appreciate the tone of
admiration.
[Sidenote: The visible disc.]
"M. Le Verrier then enters into a most ingenious computation of the
limits between which the planet must be sought. The principle is
this: assuming a time of revolution, all the other unknown
quantities may be varied in such a manner that though the
observations will not be so well represented as before, yet the
errors of observation will be tolerable. At last, on continuing the
variation of elements, one error of observation will be intolerably
great. Then, by varying the elements in another way, we may at length
make another error of observation intolerably great; and so on. If we
compute, for all these different varieties of elements, the place of
the planet for 1847, its _locus_ will evidently be a discontinuous
curve or curvilinear polygon. If we do the same thing with different
periodic times, we shall get different polygons; and the extreme
periodic times that can be allowed will be indicated by the polygons
becoming points. These extreme periodic times are 207 and 233 years.
If now we draw one grand curve, circumscribing all the polygons, it
is certain that the planet must be within that curve. In one
direction, M. Le Verrier found no difficulty in assigning a limit; in
the other he was obliged to restrict it, by assuming a limit to the
eccentricity. Thus he found that the longitude of the planet was
certainly not less than 321°, and not greater than 335° or 345°,
according as we limit the eccentricity to 0.125 or 0.2. And if we
adopt 0.125 as the limit, then the mass will be included between the
limits 0.00007 and 0.00021; either of which exceeds that of _Uranus_.
From this circumstance, combined with a probable hypothesis as to the
density, M. Le Verrier concluded that the planet would have a
visible disk, and sufficient light to make it conspicuous in ordinary
telescopes.
"M. Le Verrier then remarks, as one of the strong proofs of the
correctness of the general theory, that the error of radius vector is
explained as accurately as the error of longitude. And finally, he
gives his opinion that the latitude of the disturbing planet must be
small.
"My analysis of this paper has necessarily been exceedingly
imperfect, as regards the astronomical and mathematical parts of it;
but I am sensible that, in regard to another part, it fails totally.
I cannot attempt to convey to you the impression which was made on me
by the author's undoubting confidence in the general truth of his
theory, by the calmness and clearness with which he limited the field
of observation, and by the firmness with which he proclaimed to
observing astronomers, 'Look in the place which I have indicated, and
you will see the planet well.' Since Copernicus declared that, when
means should be discovered for improving the vision, it would be
found that _Venus_ had phases like the moon, nothing (in my opinion)
so bold, and so justifiably bold, has been uttered in astronomical
prediction. It is here, if I mistake not, that we see a character far
superior to that of the able, or enterprising, or industrious
mathematician; it is here that we see the philosopher."
[Sidenote: Peirce's views of the limits.]
But now this process of limitation was faulty and actually misleading. Let
us compare what is said about it by Professor Peirce a little later.
"Guided by this principle, well established, and legitimate, if
confined within proper limits, M. Le Verrier narrowed with consummate
skill the field of research, and arrived at two fundamental
propositions, namely:--
"1st. That the mean distance of the planet cannot be less than 35 or
more than 37.9. The corresponding limits of the time of sidereal
revolution are about 207 and 233 years.
"2nd. 'That there is only one region in which the disturbing planet
can be placed in order to account for the motions of Uranus; that the
mean longitude of this planet must have been, on January 1, 1800,
between 243° and 252°.'
"'Neither of these propositions is of itself necessarily opposed to
the observations which have been made upon Neptune, but the two
combined are decidedly inconsistent with observation. It is
impossible to find an orbit, which, satisfying the observed distance
and motion, is subject to them. If, for instance, a mean longitude
and time of revolution are adopted according with the first, the
corresponding mean longitude in 1800 must have been at least 40°
distant from the limits of the second proposition. And again, if the
planet is assumed to have had in 1800 a mean longitude near the
limits of the second proposition, the corresponding time of
revolution with which its motions satisfy the present observations
cannot exceed 170 years, and must therefore be about 40 years less
than the limits of the first proposition.'
"Neptune cannot, then, be the planet of M. Le Verrier's theory, and
cannot account for the observed perturbations of Uranus under the
form of the inequalities involved in his analysis"--(_Proc. Amer.
Acad. I._, 1846-1848, _p._ 66).
[Sidenote: Newcomb's criticism.]
At the time when Professor Peirce wrote, the orbit of Neptune was not
sufficiently well determined to decide whether one of the two limitations
might not be correct, though he could see that they could not both be
right, and we now know that they are _both wrong_. The mean distance of
Neptune is 30, which does _not_ lie between 35 and 37.9; and the longitude
in 1800 was 225°, which does _not_ lie between 243° and 252°. The
ingenious process which Airy admired and which Peirce himself calls
"consummately skilful" was wrong in principle. As Professor Newcomb has
said, "the error was the elementary one that, instead of considering all
the elements simultaneously variable, Le Verrier took them one at a time,
considering the others as fixed, and determining the limits between which
each could be contained on this hypothesis. No solver of least square
equations at the present day ought to make such a blunder. Of course one
trouble in Le Verrier's demonstration, had he attempted a rigorous one,
would have been the impossibility of forming the simultaneous equations
expressive of possible variations of all the elements."
[Sidenote: Element of good fortune.]
[Sidenote: The map used by Galle.]
The account of Le Verrier's limits by Professor Peirce, though it exhibits
the error with special clearness, is a little unfair to Le Verrier in one
point. If, instead of taking the limits for the date 1800, we take them
for 1846 (when the search for Neptune was actually made), we shall find
that they do include the actual place of the planet, as Airy found. The
erroneous mean motion of Le Verrier's planet allowed of his being right at
one time and wrong at another; and Airy examined the limits under
favourable conditions, which explains his enthusiasm. But we can scarcely
wonder that Professor Peirce came to the conclusion that the planet
discovered was not the one pointed out by Le Verrier, and had been found
by mere accident. And all these circumstances inevitably contribute to a
general impression that the calculators had a large element of good
fortune to thank for their success. Nor need we hesitate to make this
admission, for there is an element of good fortune in all discoveries. To
look no further than this--if a man had not been doing a particular thing
at a particular time, as he might easily not have been, most discoveries
would never have been made. If Sir William Herschel had not been looking
at certain small stars for a totally different purpose he would never have
found Uranus; and no one need hesitate to admit the element of chance in
the finding of Neptune. It is well illustrated by a glance at the map
which, as has been remarked, Galle used to compare with the sky on the
night when he made the actual discovery. The planet was found down near
the bottom corner of the map, and since the limits assigned for its place
might easily have varied a few degrees one way or the other, it might
easily have been off the map; in which case, it is probable that the
search would not have been successful, or at any rate that success would
have been delayed.
[Illustration: V.--CORNER OF THE BERLIN MAP, BY THE USE OF WHICH GALLE
FOUND NEPTUNE.]
[Sidenote: Every one made mistakes.]
Thus, it is a most remarkable feature of the discovery of Neptune that
mistakes were made by almost every one concerned, however eminent. Airy
made a mistake in regarding the question of the Radius Vector as of
fundamental importance; Sir J. Herschel was wrong in describing an
elementary method which he considered might have found the planet;
Professor Peirce was wrong in supposing that the actual and the supposed
planet were essentially different in their action on Uranus; Le Verrier
was wrong in assigning limits outside which it was not necessary to look
when the actual planet was outside them; Adams was more or less wrong in
thinking that the eccentricity of the new planet could be found from the
material already at disposal of man. Both Adams and Le Verrier gave far
too much importance to Bode's Law.
To review a piece of history of this kind and note the mistakes of such
men is certainly comforting, and need not in any way lessen our
admiration. In the case of the investigators themselves, much may be set
down to excitement in the presence of a possible discovery. Professor
Sampson has provided us with a small but typical instance of this fact.
When Adams had carried through all his computations for finding Neptune,
and was approaching the actual place of the planet, he, "who could carry
through fabulous computations without error," for the first time wrote
down a wrong figure. The mistake was corrected upon the MS., "probably as
soon as made," but no doubt betrays the excitement which the great worker
could not repress at this critical moment. There is a tradition that,
similarly, when the mighty Newton was approaching the completion of his
calculations to verify the Law of Gravitation, his excitement was so great
that he was compelled to assign to a friend the task of finishing them.
Finally, we may remark how the history of the discovery of Neptune again
illustrates the difficulty of formulating any general principles for
guiding scientific work. Sometimes it is well to follow the slightest
clue, however imperfectly understood; at other times we shall do better to
refuse such guidance. Bode's Law pointed to the existence of minor
planets, and might conceivably have helped in finding Uranus: but by
trusting to it in the case of Neptune, the investigators were perilously
near going astray. Sometimes it is better to follow resolutely the work in
hand whatever it may be, shutting one's ears to other calls; but Airy and
Challis lost their opportunities by just this course of action. The
history of science is full of such contradictory experiences; and the only
safe conclusion seems to be that there are no general rules of conduct for
discovery.
CHAPTER III
BRADLEY'S DISCOVERIES OF THE ABERRATION OF LIGHT AND OF THE NUTATION OF
THE EARTH'S AXIS
[Sidenote: Biographical method adopted.]
In examining different types of astronomical discovery, we shall find
certain advantages in varying to some extent the method of presentation.
In the two previous chapters our opportunities for learning anything of
the life and character of those who made the discoveries have been slight;
but I propose to adopt a more directly biographical method in dealing with
Bradley's discoveries, which are so bound up with the simple earnestness
of his character that we could scarcely appreciate their essential
features properly without some biographical study. But the record of his
life apart from his astronomical work is not in any way sensational;
indeed it is singularly devoid of incident. He had not even a scientific
quarrel. There was scarcely a man of science of that period who had not at
least one violent quarrel with some one, save only Bradley, whose gentle
nature seems to have kept him clear of them all. Judged by ordinary
standards his life was uneventful: and yet it may be doubted whether, to
him who lived it, that life contained one dull moment. Incident came for
him in his scientific work: in the preparation of apparatus, the making of
observations, above all in the hard-thinking which he did to get at the
clue which would explain them; and after reviewing his biography,[2] I
think we shall be inclined to admit that if ever there was a happy life,
albeit one of unremitting toil, it was that of James Bradley.
[Sidenote: Bradley's birth and early life.]
[Sidenote: Brief clerical career.]
He was born at Sherbourn, in Gloucestershire, in 1693. We know little of
his boyhood except that he went to the Grammar School at Northleach, and
that the memory of this fact was preserved at the school in 1832 when
Rigaud was writing his memoir. [The school is at present shut up for want
of funds to carry it on; and all inquiries I have made have failed to
elicit any trace of this memory.] Similarly we know little of his
undergraduate days at Oxford, except that he entered as a commoner at
Balliol in 1710, took his B.A. in the regular course in 1714, and his M.A.
in 1717. As a career he chose the Church, being ordained in 1719, and
presented to the vicarage of Bridstow in Monmouthshire; but he only
discharged the duties of vicar for a couple of years, for in 1721 he
returned to Oxford as Professor of Astronomy, an appointment which
involved the resignation of his livings; and so slight was this
interruption to his career as an astronomer that we may almost disregard
it, and consider him as an astronomer from the first. But to guard against
a possible misconception, let me say that Bradley entered on a clerical
career in a thoroughly earnest spirit; to do otherwise would have been
quite foreign to his nature. When vicar of Bridstow he discharged his
duties faithfully towards that tiny parish, and moreover was so active in
his uncle's parish of Wansted that he left the reputation of having been
curate there, although he held no actual appointment. And thirty years
later, when he was Astronomer Royal and resident at Greenwich, and when
the valuable vicarage of Greenwich was offered to him by the Chancellor of
the Exchequer, he honourably refused the preferment, "because the duty of
a pastor was incompatible with his other studies and necessary
engagements."
[Sidenote: Learnt astronomy _not_ at Oxford, but from his uncle, James
Pound.]
[Sidenote: Pound a first-rate observer.]
But now let us turn to Bradley's astronomical education. I must admit,
with deep regret, that we cannot allow any of the credit of it to Oxford.
There was a great astronomer in Oxford when Bradley was an undergraduate,
for Edmund Halley had been appointed Savilian Professor of Geometry in
1703, and had immediately set to work to compute the orbits of comets,
which led to his immortal discovery that some of these bodies return to us
again and again, especially the one which bears his name--Halley's
Comet--and returns every seventy-five years, being next expected about
1910. But there is no record that Bradley came under Halley's teaching or
influence as an undergraduate. In later years the two men knew each other
well, and it was Halley's one desire towards the close of his life that
Bradley should succeed him as Astronomer Royal at Greenwich; a desire
which was fulfilled in rather melancholy fashion, for Halley died without
any assurance that his wish would be gratified. But Bradley got no
astronomical teaching at Oxford either from Halley or others. The art of
astronomical observation he learnt from his maternal uncle, the Rev. James
Pound, Rector of Wansted, in Essex. He is the man to whom we owe Bradley's
training and the great discoveries which came out of it. He was, I am glad
to say, an Oxford man too; very much an Oxford man; for he seems to have
spent some thirteen years there migrating from one Hall to another. His
record indeed was such as good tutors of colleges frown upon; for it was
seven years before he managed to take a degree at all; and he could not
settle to anything. After ten years at Oxford he thought he would try
medicine; after three years more he gave it up and went out in 1700 as
chaplain to the East Indies. But he seems to have been a thoroughly
lovable man, for news was brought of him four years later that he had a
mind to come home, but was dissuaded by the Governor saying that "if Dr.
Pound goes, I and the rest of the Company will not stay behind." Soon
afterwards the settlement was attacked in an insurrection, and Pound was
one of the few who escaped with his life, losing however all the property
he had gradually acquired. He returned to England in 1706, and was
presented to the living of Wansted; married twice, and ended his days in
peace and fair prosperity in 1724. Such are briefly the facts about
Bradley's uncle, James Pound; but the most important of all remains to be
told--that somehow or other he had learnt to make first-rate astronomical
observations, how or when is not recorded; but in 1719 he was already so
skilled that Sir Isaac Newton made him a present of fifty guineas for some
observations; and repeated the gift in the following year; and even three
years before this we find Halley writing to ask for certain observations
from Mr. Pound.
[Sidenote: Bradley worked with him.]
With this excellent man Bradley used frequently to stay. To his nephew he
seems to have been more like a father than an uncle. When his nephew had
smallpox in 1717, he nursed him through it; and he supplemented from his
own pocket the scanty allowance which was all that Bradley's own father
could afford. But what concerns us most is that he fostered, if he did not
actually implant, a love of astronomical observation in his nephew. The
two worked together, entering their observations one after the other on
the same paper; and it was to the pair of them together, rather than to
the uncle alone, that Newton made his princely presents, and Halley wrote
for help in his observations. There seems to be no doubt that the uncle
and nephew were about this time the best astronomical observers in the
world. There was no rivalry between them, and therefore there is no need
to discuss whether the partnership was one of equal merit on both sides;
but it is interesting to note that it probably was. The ability of Pound
was undoubted; many were keenly desirous that he, and not his nephew,
should be elected to the Oxford Chair in 1721, but he felt unequal to the
duties at his advanced age. On the other hand, when Bradley lost his
uncle's help, there was no trace of faltering in his steps to betray
previous dependence on a supporting or guiding hand. He walked erect and
firm, and trod paths where even his uncle might not have been able to
follow.
[Sidenote: The work done by Pound and Bradley.]
[Sidenote: Use of very long telescopes.]
[Sidenote: Reason for great length.]
A few instances will suffice to show the kind of observations made by this
notable firm of Pound and Bradley. They observed the positions of the
fixed stars and nebulæ: these being generally the results required by
Halley and Newton. They also observed the places of the planets among the
stars, and especially the planet Mars, and determined its distance from
the Earth by the method of parallax, thus anticipating the modern standard
method of finding the Sun's distance; and though with their imperfect
instruments they did not obtain a greater accuracy than 1 in 10, still
this was a great advance on what had been done before, and excited the
wonder and admiration of Halley. They also paid some attention to double
stars, and did a great deal of work on Jupiter's satellites. We might
profitably linger over the records of these early years, which are full of
interest, but we must press on to the time of the great discoveries, and
we will dismiss them with brief illustrations of three points: Bradley's
assiduity, his skill in calculation, and his wonderful skill in the
management of instruments. Of his assiduity an example is afforded by his
calculations of the orbits of two comets which are still extant. One of
them fills thirty-two pages of foolscap, and the other sixty; and it must
be remembered that the calculations themselves were quite novel at that
time. Of his _skill_ in calculation, apart from his assiduity, we have a
proof in a paper communicated to the Royal Society rather later (1726),
where he determines the longitudes of Lisbon and New York from the
eclipses of Jupiter's satellites, using observations which were not
simultaneous, and had therefore to be corrected by an ingenious process
which Bradley devised expressly for this purpose. And finally, his skill
in the management of instruments is shown by his measuring the diameter of
the planet Venus with a telescope actually 212-1/4 feet in length. It is
difficult for us to realise in these days what this means; even the
longest telescope of modern times does not exceed 100 feet in length, and
it is mounted so conveniently with all the resources of modern
engineering, in the shape of rising floors, &c., that the management of it
is no more difficult than that of a 10-foot telescope. But Bradley had no
engineering appliances beyond a pole to hold up one end of the telescope
and his own clever fingers to work the other; and he managed to point the
unwieldy weapon accurately to the planet, and measure the diameter with an
exactness which would do credit to modern times. A few words of
explanation may be given why such long telescopes were used at all. The
reason lay in the difficulty of getting rid of coloured images, due to the
composite character of white light. Whenever we use a _single_ lens to
form an image, coloured fringes appear. Nowadays we know that by making
two lenses of different kinds of glass and putting them together, we can
practically get rid of these coloured fringes; but this discovery had not
been made in Bradley's time. The only known ways of dealing with the evil
then were to use a reflecting telescope like Newton and Gregory, or if a
lens was used, to make one of very great focal length; and hence the
primary necessity for these very long telescopes. They had another
advantage in producing a large image, or they would probably have given
way to the reflector. This advantage is gradually bringing them back into
use, and perhaps in the eclipse of 1905 we may use a telescope as long as
Bradley's; but we shall not use it as he did in any case. It will be laid
comfortably flat on the ground, and the rays of light reflected into it by
a coelostat.
[Sidenote: Bradley appointed at Oxford, but continues to work at Wansted.]
In 1721 Bradley was appointed to the Savilian Professorship of Astronomy
at Oxford, vacant by the death of Dr. John Keill. Once it became clear
that there was no chance of securing his uncle for this position, Bradley
himself was supported enthusiastically by all those whose support was
worth having, especially by the Earl of Macclesfield, who was then Lord
Chancellor; by Martin Foulkes, who was afterwards the President of the
Royal Society; and by Sir Isaac Newton himself. He was accordingly elected
on October 31, 1721, and forthwith resigned his livings. His resignation
of the livings was necessitated by a definite statute of the University
relating to the Professorship, and not by the existence of any very
onerous duties attaching to it; indeed such duties seem to have been
conspicuously absent, and after Bradley's election he passed more time
than ever with his uncle in Wansted, making the astronomical observations
which both loved; for there was not the vestige of an observatory in
Oxford. His uncle's death in 1724 interrupted the continuity of these
joint observations, and by an odd accident prepared the way for Bradley's
great discovery. He was fain to seek elsewhere that companionship in his
work which had become so essential to him, and his new friend gave a new
bent to his observations.
[Sidenote: Samuel Molyneux.]
[Sidenote: Attempts to find stellar parallax.]
Samuel Molyneux was a gentleman of fortune much attached to science, and
particularly to astronomy, who was living about this time at Kew. He was
one of the few, moreover, who are not content merely to amuse themselves
with a telescope, but had the ambition to do some real earnest work, and
the courage to choose a problem which had baffled the human race for more
than a century. The theory of Copernicus, that the earth moved round the
sun, necessitated a corresponding apparent change in the places of the
stars, one relatively to another; and it was a standing difficulty in the
way of accepting this theory that no such change could be detected. In the
old days before the telescope it was perhaps easy to understand that the
change might be too small to be noticed, but the telescope had made it
possible to measure changes of position at least a hundred times as small
as before, and still no "parallax," as the astronomical term goes, could
be found for the stars. The observations of Galileo, and the measures of
Tycho Brahé, as reduced to systematic laws by Kepler, and finally by the
great Newton, made it clear that the Copernican theory was _true_: but no
one had succeeded in proving its truth in this particular way. Samuel
Molyneux must have been a man of great courage to set himself to try to
crack this hard nut; and we can understand the attraction which his
enterprise must have had for Bradley, who had just lost the beloved
colleague of many courageous astronomical undertakings. His co-operation
seems to have been welcomed from the first; his help was invited and
freely given in setting up the instrument, and he fortunately had the
leisure to spend considerable time at Kew making the observations with
Molyneux, just as he had been wont to observe with his uncle.
I must now briefly explain what these observations were. There is a bright
star [gamma] Draconis, which passes almost directly overhead in the
latitude of London. Its position is slowly changing owing to the
precession of the equinoxes, but for two centuries it has been, and is
still, under constant observation by London astronomers owing to this
circumstance, that it passes directly overhead, and so its position is
practically undisturbed by the refraction of our atmosphere.
[Sidenote: The instrument.]
[Sidenote: Expected results.]
It was therefore thought at the time that, there being no disturbance from
refraction, the disturbance from precession being accurately known, and
there being nothing else to disturb the position but "parallax" (the
apparent shift due to the earth's motion which it was desirable to find),
this star ought to be a specially favourable object for the determination
of parallax. Indeed it had been announced many years before by Hooke that
its parallax had been found; but his observations were not altogether
satisfactory, and it was with a view of either confirming them or seeing
what was wrong with them that Molyneux and Bradley started their search.
They set up a much more delicate piece of apparatus than Hooke had
employed. It was a telescope 24 feet long pointed upwards to the star, and
firmly attached to a large stack of brick chimneys within the house. The
telescope was not absolutely fixed, for the lower end could be moved by a
screw so as to make it point accurately to the star, and a plumb-line
showed how far it was from the vertical when so pointing. Hence if the
star changed its position, however slightly, the reading of this screw
would show the change. Now, before setting out on the observations, the
observers knew what to expect if the star had a real parallax; that is to
say, they knew that the star would seem to be farthest south in December,
farthest north in June, and at intermediate positions in March and
September; though they did not know _how much_ farther south it would
appear in December than in June--this was exactly the point to be decided.
[Illustration: FIG. 2.]
[Sidenote: Unexpected results.]
The reason of this will be clear from Fig. 2. [Remark, however, that this
figure and the corresponding figure 4 do not represent the case of
Bradley's star, [gamma] Draconis: another star has been chosen which
simplifies the diagram, though the principle is essentially the same.] Let
A B C D represent the earth's orbit, the earth being at A in June, at B in
September, and so on, and let K represent the position of the star on the
line D B. Then in March and September it will be seen from the earth in
the same direction, namely, D B K; but the directions in which it is seen
in June and December, viz. A K and C K, are inclined in opposite ways to
this line. The farther away the star is, the less will this inclination or
"parallax" be; and the star is actually so far away that the inclination
can only be detected with the utmost difficulty: the lines C K and A K are
sensibly parallel to D B K. But Bradley did not know this; it was just
this point which he was to examine, and he expected the greatest
inclination in one direction to be in December. Accordingly when a few
observations had been made on December 3, 5, 11, and 12 it was thought
that the star had been caught at its most southerly apparent position, and
might be expected thereafter to move northwards, if at all. But when
Bradley repeated the observation on December 17, he found to his great
surprise that the star was still moving southwards. Here was something
quite new and unexpected, and such a keen observer as Bradley was at once
on the alert. He soon found that the changes in the position of the star
were of a totally unexpected character. Instead of the extreme positions
being occupied in June and December, they were occupied in March and
September, just midway between these. And the range in position was quite
large, about 40"--not a quantity which could have been detected in the
days before telescopes, but one which was unmistakable with an instrument
of the most moderate measuring capacity.
[Sidenote: Tentative explanations.]
What, then, was the cause of this quite unforeseen behaviour on the part
of the star? The first thought of the observers was that something might
be wrong with their instrument, and it was carefully examined, but without
result. The next was that the apparent movement was in the plumb-line, the
line of reference. If the whole earth, instead of carrying its axis round
the sun in a constant direction, were to be executing an oscillation, then
all our plumb-lines would oscillate, and when the direction of a star like
[gamma] Draconis was compared with that of the plumb-line it would seem to
vary, owing actually to the variation in the plumb-line. The earth might
have a motion of this kind in two ways, which it will be necessary for us
to distinguish, and the adopted names for them are "nutation of the axis"
and "variation of latitude" respectively. In the case of nutation the
North Pole remains in the same geographical position, but points to a
different part of the heavens. The "variation of latitude," on the other
hand, means that the North Pole wanders about on the earth itself. We
shall refer to the second phenomenon more particularly in the sixth
chapter.
[Sidenote: Nutation?]
[Sidenote: Anomalous refraction.]
But it was the first kind of change, the nutation, which Bradley
suspected; and very early in the series of observations he had already
begun to test this hypothesis. If it was not the star, but the earth and
the plumb-line, which were in motion, then other stars ought to be
affected. The telescope had been deliberately restricted in its position
to suit [gamma] Draconis; but since the stars circle round the Pole, if we
draw a narrow belt in the heavens with the Pole as centre, and including
[gamma] Draconis, the other stars included would make the same circuit,
preceding or following [gamma] Draconis by a constant interval. Most of
them would be too faint for observation with Bradley's telescope; but
there was one bright enough to be observed, which also came within its
limited range, and it was promptly put under _surveillance_ when a
nutation of the earth's axis was suspected. Careful watching showed that
it was not affected in the same way as [gamma] Draconis, and hence the
movement could not be in the plumb-line. Was there, then, after all, some
effect of the earth's atmosphere which had been overlooked? We have
already remarked that since the star passes directly overhead there
should be practically no refraction; and this assumption was made by
Molyneux and Bradley in choosing this particular star for observation. It
follows at once, if we assume that the atmosphere surrounds the earth in
spherical layers. But perhaps this was not so? Perhaps, on the contrary,
the atmosphere was deformed by the motion of the earth, streaming out
behind her like the smoke of a moving engine? No possibility must be
overlooked if the explanation of this puzzling fact was to be got at.
[Illustration: FIG. 3.]
The way in which a deformation of the atmosphere might explain the
phenomenon is best seen by a diagram. First, it must be remarked that rays
of light are only bent by the earth's atmosphere, or "refracted," if they
enter it obliquely.
If the atmosphere were of the same density throughout, like a piece of
glass, then a vertical ray of light, A B (see Fig. 3), entering the
atmosphere at B would suffer no bending or refraction, and a star shining
from the direction A B would be seen truly in that direction from C. But
an oblique ray, D E, would be bent on entering the atmosphere at E along
the path EF, and a star shining along D E would appear from F to be
shining along the dotted line G E F. The atmosphere is not of the same
density throughout, but thins out as we go upwards from the earth; and in
consequence there is no clear-cut surface, B E, and no sudden bending of
the rays as at E: they are gradually bent at an infinite succession of
imaginary surfaces. But it still remains true that there is no bending at
all for vertical rays; and of oblique rays those most oblique are most
bent.
[Illustration: FIG. 4.]
Now, suppose the atmosphere of the earth took up, owing to its revolution
round the sun, an elongated shape like that indicated in diagram 4, and
suppose the star to be at a great distance away to the right of the
diagram. When the earth is in the position labelled "June," the light
would fall vertically on the nose of the atmosphere at A, and there would
be no refraction. Similarly in "December" the light would fall at C on the
stern, also vertically, and there would be no refraction. [The rays from
the distant star in December are to be taken as sensibly parallel to those
received in June, notwithstanding that the earth is on the opposite side
of the sun, as was remarked on p. 98.] But in March and September the rays
would strike obliquely on the sides of the supposed figure, and thus be
bent in opposite directions, as indicated by the dotted lines; and the
extreme positions would thus occur in March and September, as had been
observed. The explanation thus far seems satisfactory enough.
But we have assumed the star to lie in the plane of the earth's orbit; and
the stars under observation by Bradley did not lie in this plane, nor did
they lie in directions equally inclined to it. Making the proper allowance
for their directions, it was found impossible to fit in the facts with
this hypothesis, which had ultimately to be abandoned.
[Sidenote: Delay in finding real explanation.]
[Sidenote: Bradley sets up another instrument at Wansted.]
[Sidenote: Finds the right clue.]
[Sidenote: A wind-vane on a boat.]
It is remarkable to find that two or three years went by before the real
explanation of this new phenomenon occurred to Bradley, and during this
time he must have done some hard thinking. We have all had experience of
the _kind_ of thinking if only in the guessing of conundrums. We know the
apparent hopelessness of the quest at the outset: the racking of our
brains for a clue, the too frequent despair and "giving it up," and the
simplicity of the answer when once it is declared. But with scientific
conundrums the expedient of "giving it up" is not available. We must find
the answer for ourselves or remain in ignorance; and though we may feel
sure that the answer when found will be as simple as that to the best
conundrum, this expected simplicity does not seem to aid us in the search.
Bradley was not content with sitting down to think: he set to work to
accumulate more facts. Molyneux's instrument only allowed of the
observation of two stars, [gamma] Draconis and the small star above
mentioned. Bradley determined to have an instrument of his own which
should command a wider range of stars; and by this time he was able to
return to his uncle's house at Wansted for this purpose. His uncle had
been dead for two or three years, and the memory of the loss was becoming
mellowed with time. His uncle's widow was only too glad to welcome back
her nephew, though no longer to the old rectory, and she allowed him to
set up a long telescope, even though he cut holes in her floor to pass it
through. The object-glass end was out on the roof and the eye end down in
the coal cellar; and accordingly in this coal cellar Bradley made the
observations which led to his immortal discovery. He had a list of
seventy stars to observe, fifty of which he observed pretty regularly. It
may seem odd that he did not set up this new instrument at Oxford, but we
find from an old memorandum that his professorship was not bringing him in
quite £140 a year, and probably he was glad to accept his aunt's
hospitality for reasons of economy. By watching these different stars he
gradually got a clear conception of the laws of aberration. The real
solution of the problem, according to a well-authenticated account,
occurred to him almost accidentally. We all know the story of the apple
falling and setting Newton to think about the causes of gravitation. It
was a similarly trivial circumstance which suggested to Bradley the
explanation which he had been seeking for two or three years in vain. In
his own words, "at last, when he despaired of being able to account for
the phenomena which he had observed, a satisfactory explanation of them
occurred to him all at once when he was not in search of it." He
accompanied a pleasure party in a sail upon the river Thames. The boat in
which they were was provided with a mast which had a vane at the top of
it. It blew a moderate wind, and the party sailed up and down the river
for a considerable time. Dr. Bradley remarked that every time the boat put
about the vane at the top of the boat's mast shifted a little, as if there
had been a slight change in the direction of the wind. He observed this
three or four times without speaking; at last he mentioned it to the
sailors, and expressed his surprise that the wind should shift so
regularly every time they put about. The sailors told him that the wind
had not shifted, but that the apparent change was owing to the change in
the direction of the boat, and assured him that the same thing invariably
happened in all cases. This accidental observation led him to conclude
that the phenomenon which had puzzled him so much was owing to the
combined motion of light and of the earth. To explain exactly what is
meant we must again have recourse to a diagram; and we may also make use
of an illustration which has become classical.
[Illustration: FIG. 5.]
[Sidenote: Analogy of rain.]
If rain is falling vertically, as represented by the direction A B; and if
a pedestrian is walking horizontally in the direction C D, the rain will
appear to him to be coming in an inclined direction, E F, and he will find
it better to tilt his umbrella forwards. The quicker his pace the more he
will find it advisable to tilt the umbrella. This analogy was stated by
Lalande before the days of umbrellas in the following words: "Je suppose
que, dans un temps calme, la pluie tombe perpendiculairement, et qu'on
soit dans une voiture ouverte sur le devant; si la voiture est en repos,
on ne reçoit pas la moindre goutte de pluie; si la voiture avance avec
rapidité, la pluie entre sensiblement, comme si elle avoit pris une
direction oblique." Lalande's example, modified to suit modern conditions,
has been generally adopted by teachers, and in examinations candidates
produce graphic pictures of the stationary, the moderate-paced, and the
flying, possessors of umbrellas.
[Sidenote: Aberration.]
Applying it to the phenomenon which it is intended to illustrate, if light
is being received from a star by an earth, travelling across the direction
of the ray, the telescope (which in this case represents the umbrella)
must be tilted forward to catch the light. Now on reference to Fig. 4 it
will be seen that the earth is travelling across the direction of rays
from the star in March and September; and in opposite directions in the
two cases. Hence the telescope must be tilted a little, in opposite
directions, to catch the light; or, in other words, the star will appear
to be farthest south in March, farthest north in September. And so at last
the puzzle was solved, and the solution was found, as so often happens, to
be of the simplest kind; so simple when once we know, and so terribly hard
to imagine when we don't! It may comfort us in our struggles with minor
problems to reflect that Bradley manfully stuck to his problem for two or
three years. It was probably never out of his thoughts, waking or
sleeping; when at work it was the chief object of his labours, and when on
a pleasure party he was ready to catch at the slightest clue, in the
motion of a wind-vane on a boat, which might help him to the solution.
[Sidenote: Results of discovery.]
The discovery of aberration made Bradley famous at a bound. Oxford might
well be proud of her two Savilian Professors at this time, for they had
both made world-famous discoveries--Halley that of the periodicity of
comets, and Bradley of the aberration of light. How different their tastes
were and how difficult it would have been for either to do the work of the
other! Bradley was no great mathematician, and though he was quite able to
calculate the orbit of a comet, and carried on such work when Halley left
it, it was probably not congenial to him. Halley, on the other hand,
almost despised accurate observations as finicking. "Be sure you are
correct to a minute," he was wont to say, "and the fractions do not so
much matter." With such a precept Bradley would never have made his
discoveries. No quantity was too small in his eyes, and no sooner was the
explanation of aberration satisfactorily established than he perceived
that though it would account for the main facts, it would not explain all.
There was something left. This is often the case in the history of
science. A few years ago it was thought that we knew the constitution of
our air completely--oxygen, nitrogen, water vapour, and carbonic acid gas;
but a great physicist, Lord Rayleigh, found that after extracting all the
water and carbonic acid gas, all the oxygen and all the nitrogen, there
was something left--a very minute residuum, which a careless experimenter
would have overlooked or neglected, but which a true investigator like
Lord Rayleigh saw the immense importance of. He kept his eye on that
something left, and presently discovered a new gas which we now know as
argon. Had he repeated the process, extracting all the argon after the
nitrogen, he might have found by a scrutiny much more accurate still yet
another gas, helium, which we now know to exist in extremely minute
quantities in the air. But meantime this discovery was made in another
way.
[Sidenote: Still something to be explained.]
[Sidenote: Probably nutation.]
[Sidenote: His nineteen years' campaign.]
When Bradley had extracted all the aberration from his observations he
found that there was something left, another problem to be solved and some
more thinking to be done to solve it. But he was now able to profit by his
previous labours, and the second step was made more easily than the first.
The residuum was not the parallax of which he had originally been in
search, for it did not complete a cycle within the year; it was rather a
progressive change from year to year. But there was an important clue of
another kind. He saw that the apparent movements of all stars were in
this case the same; and he knew that a movement of this kind can be
referred, not to the stars themselves, but to the plumb-line from which
their directions are measured. He had thought out the possible causes of
such a movement of the plumb-line or of the earth itself, and had realised
that there might be a _nutation_ which would go through a cycle in about
nineteen years, the period in which the moon's nodes revolve. He was not
mathematician enough to work out the cause completely, but he saw clearly
that to trace the whole effect he must continue the observations for
nineteen years; and accordingly he entered on this long campaign without
any hesitation. His instrument was still that in his aunt's house at
Wansted, where he continued to live and make the observations for a few
years, but in 1732 he removed to Oxford, as we shall see, and he must have
made many journeys between Wansted and Oxford in the course of the
remaining fifteen years during which he continued to trace out the effects
of nutation. His aunt too left Wansted to accompany Bradley to Oxford, and
the house passed into other hands. It is to the lasting credit of the new
occupant, Mrs. Elizabeth Williams, that the great astronomer was allowed
to go on and complete the valuable series of observations which he had
commenced. Bradley was not lodged in her house; he stayed with a friend
close by on his visits to Wansted, but came freely in and out of his
aunt's old home to make his observations. How many of us are there who
would cheerfully allow an astronomer to enter our house at any hour of the
night to make observations in the coal-cellar! It says much, not only for
Bradley's fame, but for his personal attractiveness, that he should have
secured this permission, and that there should be no record of any
friction during these fifteen years. At the end of the whole series of
nineteen years his conclusions were abundantly verified, and his second
great discovery of nutation was established. Honours were showered upon
him, and no doubt the gentle heart of Mrs. Elizabeth Williams was uplifted
at the glorious outcome of her long forbearance.
[Sidenote: Residence at Oxford.]
But we may now turn for a few moments from Bradley's scientific work to
his daily life. We have said that in 1732, after holding his professorship
for eleven years, he first went definitely to reside in Oxford. He
actually had not been able to afford it previously. His income was only
£140 a year, and the statutes prevented him from holding a living: so
that he was fain to accept Mrs. Pound's hospitable shelter. But in 1729 an
opportunity of adding to his income presented itself, by giving lectures
in "experimental philosophy." The observations on nutation were not like
those on aberration: he was not occupied day and night trying to find the
solution: he had practically made up his mind about the solution, and the
actual observations were to go on in a quiet methodical manner for
nineteen years, so that he now had leisure to look about him for other
employment. Dr. Keill, who had been Professor of Astronomy before Bradley,
had attracted large classes to lectures, not on astronomy, but on
experimental philosophy: but had sold his apparatus and goodwill to Mr.
Whiteside, of Christ Church, one of the candidates who were disappointed
by Bradley's election. In 1729 Bradley purchased the apparatus from
Whiteside, and began to give lectures in experimental philosophy. His
discovery of aberration had made him famous, so that his classes were
large from the first, and paid him considerable fees. Suddenly therefore
he changed his poverty for a comfortable income, and he was able to live
in Oxford in one of two red brick houses in New College Lane, which were
in those days assigned to the Savilian Professors (now inhabited by New
College undergraduates). His aunt, Mrs. Pound, to whom he was devotedly
attached, came with him, and two of her nephews. In his time of prosperity
Bradley was thus able to return the hospitality which had been so
generously afforded him in times of stress.
[Sidenote: Astronomer Royal at Greenwich.]
[Sidenote: Letter from Earl of Macclesfield.]
Before he completed his observations for nutation another great change in
his fortunes took place. In 1742 he was elected to succeed Halley as
Astronomer Royal. It was Halley's dying wish that Bradley should succeed
him, and it is said that he was even willing to resign in his favour, for
his right hand had been attacked by paralysis, and the disease was
gradually spreading. But he died without any positive assurance that his
wish would be fulfilled. The chief difficulty in securing the appointment
of Bradley seems to have been that he was the obvious man for the post in
universal opinion. "It is not only my friendship for Mr. Bradley that
makes me so ardently wish to see him possessed of the position," wrote the
Earl of Macclesfield to the Lord Chancellor; "it is my real concern for
the honour of the nation with regard to science. For as our credit and
reputation have hitherto not been inconsiderable amongst the astronomical
part of the world, I should be extremely sorry we should forfeit it all at
once by bestowing upon a man of inferior skill and abilities the most
honourable, though not the most lucrative, post in the profession (a post
so well filled by Dr. Halley and his predecessor), when at the same time
we have amongst us a man known by all the foreign, as well as our own
astronomers, not to be inferior to either of them, and one whom Sir Isaac
Newton was pleased to call the best astronomer in Europe." And again, "As
Mr. Bradley's abilities in astronomical learning are allowed and confessed
by all, so his character in every respect is so well established, and so
unblemished, that I may defy the worst of his enemies (if so good and
worthy a man have any) to make even the lowest or most trifling objection
to it."
"After all," the letter goes on, "it may be said if Mr. Bradley's skill is
so universally acknowledged, and his character so established, there is
little danger of opposition, since no competitor can entertain the least
hope of success against him. But, my lord, we live in an age when most men
how little soever their merit may be, seem to think themselves fit for
whatever they can get, and often meet with some people, who by their
recommendations of them appear to entertain the same opinion of them, and
it is for this reason that I am so pressing with your lordship not to lose
any time."
Such recommendations had, however, their effect: the dreaded possibility
of a miscarriage of justice was averted, and Bradley became the third
Astronomer Royal, though he did not resign his professorship at Oxford.
Halley, Bradley, and Bliss, who were Astronomers Royal in succession, all
held the appointment along with one of the Savilian professorships at
Oxford; but since the death of Bliss in 1761, the appointment has always
gone to a Cambridge man.
[Sidenote: Instruments very defective.]
When Bradley went to Greenwich, in June 1742, he was at first unable to do
much from the wretched state in which he found the instruments. Halley was
not a good observer: his heart was not in the work, and he had not taken
the trouble to set the instruments right when they went wrong. The
counterpoises of that instrument which ought to have been the best in the
world at the time rubbed against the roof so that the telescope could
scarcely be moved in some positions: and some of the screws were broken.
There was no proper means of illuminating the cross-wires, and so on. With
care and patience Bradley set all this right, and began observations. He
had the good fortune to secure the help of his nephew, John Bradley, as
assistant, and the companionship seems to have been as happy as that
previous one of James Bradley and his uncle Pound. John Bradley was able
to carry on the observations when his uncle was absent in Oxford, and the
work the two got through together in the first year is (in the words of
Bradley's biographer Rigaud) "scarcely to be credited." The transit
observations occupy 177 folio pages, and no less than 255 observations
were taken on one night. And at the same time, it must be remembered,
Bradley was still carrying on his nutation observations at Wansted, still
lecturing at Oxford, and not content with all this, began a course of
experiments on the length of the seconds' pendulum. Truly a giant for hard
work!
[Sidenote: New instruments.]
But, in spite of his care in setting them right, the instruments in the
Observatory were found to be hopelessly defective. The history of the
instruments at the Royal Observatory is a curious one. When Flamsteed was
appointed the first Astronomer Royal he was given the magnificent salary
of £100 a year, and no instruments to observe with. He purchased some
instruments with his own money, and at his death they were claimed by his
executors. Hence Halley, the second Astronomer Royal, found the
Observatory totally unprovided in this respect. He managed to persuade the
nation to furnish the funds for an equipment; but Halley, though a man of
great ability in other ways, did not know a good instrument from a bad
one; so that Bradley's first few years at the Observatory were wasted
owing to the imperfection of the equipment. When this was fully realised
he asked for funds to buy new instruments, and such was the confidence
felt in him that he got what he asked for without much difficulty. More
than £1000, a large sum for those days, was spent under his direction,
the principal purchases being two quadrants for observation of the
position of the stars, one to the north and the other to the south. With
these quadrants, which represented the perfection of such apparatus at
that time, Bradley made that long and wonderful series of observations
which is the starting-point of our knowledge of the movements of the
stars. The instruments are still in the Royal Observatory, the more
important of the two in its original position as Bradley mounted it and
left it.
[Sidenote: Work at Greenwich.]
It seems needless to mention his work as Astronomer Royal, but I will give
quite briefly a summary of what he accomplished, and then recall a
particular incident, which shows how far ahead of his generation his
genius for observation placed him. The summary may be given as follows.
We owe to Bradley--
1. A better knowledge of the movements of Jupiter's satellites.
2. The orbits of several comets calculated directly from his own
observations, when such work was new and difficult.
3. Experiments on the length of the pendulum.
4. The foundation of our knowledge of the refraction of our atmosphere.
5. Considerable improvements in the tables of the moon, and the promotion
of the method for finding the longitude by lunar distances.
6. The proper equipment of our national Observatory with instruments, and
the use of these to form the basis of our present knowledge of the
positions and motions of the stars.
Many men would consider any one of these six achievements by itself a
sufficient title to fame. Bradley accomplished them all in addition to his
great discoveries of aberration and nutation.
[Sidenote: Might have found variation of latitude.]
And with a little more opportunity he might have added another great
discovery which has shed lustre on the work of the last decade. We said
earlier in this chapter that the axis of the earth may move in one or two
ways. Either it may point to a different star, remaining fixed relatively
to the earth, as in the nutation which Bradley discovered; or it may
actually change its position in the earth. This second kind of movement
was believed until twenty years ago not to exist appreciably; but the
work of Küstner and Chandler led to the discovery that it did exist, and
its complexities have been unravelled, and will be considered in the sixth
chapter. Now a century and a half ago Bradley was on the track of this
"variation of latitude." His careful observations actually showed the
motion of the pole, as Mr. Chandler has recently demonstrated; and,
moreover, Bradley himself noticed that there was something unexplained.
Once again there was a _residuum_ after (first) aberration and (next)
nutation had been extracted from the observations; and with longer life he
might have explained this residuum, and added a third great discovery to
the previous two. Or another coming after him might have found it; but
after the giant came men who could not tread in his footsteps, and the
world waited 150 years before the discrepancy was explained.
[Sidenote: Oxford's tardy recognition of Bradley.]
The attitude of our leading universities towards science and scientific
men is of sufficient importance to justify another glance at the relations
between Bradley and Oxford. We have seen that Oxford's treatment of
Bradley was not altogether satisfactory. She left him to learn astronomy
as he best could, and he owes no teaching to her. She made him Professor
of Astronomy, but gave him no observatory and a beggarly income which he
had to supplement by giving lectures on a different subject. But when he
had disregarded these discouragements and made a name for himself, Oxford
took her share in recognition. He was created D.D. by diploma in 1742; and
when his discovery of nutation was announced in 1748, and produced
distinctions and honours of all kinds from over the world, we are told
that "amidst all these distinctions, wide as the range of modern science,
and permanent as its history, there was one which probably came nearer his
heart, and was still more gratifying to his feeling than all. Lowth
(afterwards Bishop of London), a popular man, an elegant scholar, and
possessed of considerable eloquence, had in 1751 to make his last speech
in the Sheldonian Theatre at Oxford as Professor of Poetry. In recording
the benefits for which the University was indebted to its benefactors, he
mentioned the names of those whom Sir Henry Savile's foundation had
established there: 'What men of learning! what mathematicians! we owe to
Savile, Briggs, Wallis, Halley; to Savile we owe Greaves, Ward, Wren,
Gregory, Keill, and one whom I will not name, for posterity will ever have
his name on its lips.' Bradley was himself present; there was no one in
the crowded assembly on whom the allusion was lost, or who did not feel
the truth and justice of it; all eyes were turned to him, while the walls
rung with shouts of heartfelt affection and admiration; it was like the
triumph of Themistocles at the Olympic games."
[Sidenote: The study of "residual phenomena."]
These words of Rigaud indicate the fame deservedly acquired by an earnest
and simple-minded devotion to science: but can we learn anything from the
study of Bradley's work to guide us in further research? The chief lessons
would seem to be that if we make a series of careful observations, we
shall probably find some deviation from expectation: that we must follow
up this clue until we have found some explanation which fits the facts,
not being discouraged if we cannot hit upon the explanation at once, since
Bradley himself was puzzled for several years: that after finding one
_vera causa_, and allowing for the effect of it, the observations may show
traces of another which must again be patiently hunted, even though we
spend nineteen years in the chase: and that again we may have to leave the
complete rectification of the observations to posterity. But though we may
admit the general helpfulness of these directions, and that this patient
dealing with residual phenomena seems to be a method capable of frequent
application, we cannot deduce any universal principle of procedure from
them: witness the difficulty of dealing with meteorological observations,
for instance. It is not always possible to find any orderly arrangement of
the residuals which will give us a clue to start with. When such an
arrangement is manifested, we must certainly follow up the clue; it would
almost seem that no expense should be prohibitive, since it is impossible
to foresee the importance of the result.
CHAPTER IV
ACCIDENTAL DISCOVERIES
[Sidenote: The Oxford new star found during work on Astrographic Chart.]
In reviewing various types of astronomical discovery I have laid some
stress upon the fact that they are, generally speaking, far from being
accidental in character. A new planet does not "swim into our ken," at any
rate not usually, but is found only after diligent search, and then only
by an investigator of acute vision, or other special qualifications. But
this is, of course, not always the case. Some discoveries are made by the
merest accident, as we have had occasion to remark incidentally in the
case of the minor planets; and for the sake of completeness it is
desirable to include among our types at least one case of such accidental
discovery. As, however, the selection is a little invidious, I may perhaps
be pardoned for taking the instance from my own experience, which happens
to include a case where one of those remarkable objects called "new stars"
walked deliberately into a net spread for totally different objects. There
is the further reason for choosing this instance: that it will afford me
the opportunity of saying something about the special research in which we
were actually engaged, the work of mapping out the heavens by
photography, or, as it has been called, the Astrographic Chart--a great
scheme of international co-operation by which it is hoped to leave as a
legacy for future centuries a record of the state of the sky in our age.
Such a record cannot be complete; for however faint the stars included, we
know that there are fainter stars which might have been included had we
given longer exposures to the plates. Nor can it be in other ways final or
perfect; however large the scale, for instance, on which the map is made,
we can imagine the scale doubled or increased many-fold. But the map will
be a great advance on anything that has hitherto been made, and some
account of it will therefore no doubt be of interest.
[Sidenote: Origin of the chart.]
We may perhaps begin with a brief historical account of the enterprise.
Photographs of the stars were taken many years ago, but only by a few
enthusiasts, and with no serious hope of competing with eye observations
of the sky. The old wet-plate photography was, in fact, somewhat unsuited
to astronomical purposes; to photograph faint objects a long exposure is
necessary, and the wet plate may dry up before the exposure is
concluded--nay, even before it is commenced, if the observer has to wait
for passing clouds--and therefore it may be said that the successful
application of photography to astronomy dates from the time when the dry
plate was invented; when it became possible to expose a plate in the
telescope for hours, or by accumulation even for days. The dry plate
remains sensitive for a long period, and if it is desired to extend an
exposure beyond the limits of one night, it is quite easy to close up
the telescope and return to the operations again on the next fine night;
and so on, if not perhaps indefinitely, at any rate so long as to
transcend the limits of human patience up to the present.
[Illustration:
VII.--GREAT COMET OF NOV. 7TH, 1882
(_From a photograph taken at the Royal Observatory, Cape of Good Hope._)]
[Sidenote: Comet of 1882.]
[Sidenote: Stars shown on the pictures.]
But to consider our particular project. We may assign, perhaps, the date
1882 as that in which it first began to take shape. In that year there was
a magnificent bright comet, the last really large comet which we, in the
Northern Hemisphere, have had the good fortune to see. Some of us, of
course, were not born at that time, and perhaps others who were alive may
nevertheless not have seen that comet; for it kept somewhat uncomfortably
early morning hours, and I can well remember myself feeling rather more
resentment than gratitude to the man who waked me up about four o'clock to
see it. Many observations were of course made of this interesting visitor,
and what specially concerns us is that at the Cape of Good Hope some
enterprising photographers tried to photograph it. They tried in the first
instance with ordinary cameras, and soon found--what any astronomer could
have told them--that the movement of the earth, causing an apparent
movement of the comet and the stars in the opposite direction, frustrated
their efforts. The difficulties of obtaining pictures of moving objects
are familiar to all photographers. A "snap-shot" might have met the
difficulty, but the comet was scarcely bright enough to affect the plate
with a short exposure. Ultimately Dr. David Gill, the astronomer at the
Cape Observatory, invited one of the photographers to strap his camera to
one of the telescopes at the Observatory, a telescope which could be
carried round by clockwork in the usual way, so as to counteract the
earth's motion, and in effect to keep the comet steadily in view, as
though it were at rest. As a consequence, some very beautiful and
successful pictures of the comet were obtained, and on them a large number
of stars were also shown. They were, as I have said, not by any means the
first pictures of stars obtained by photography, but they represented in
facility and in success so great an advance upon what had been formerly
obtained that they attracted considerable attention. They were sent to
Europe and stimulated various workers to further experiments.
[Sidenote: The brothers Henry begin work.]
[Sidenote: Conference of 1887.]
The late Dr. Common in England, an amateur astronomer, began that
magnificent pioneer work in astronomical photography which soon brought
him the Gold Medal of the Royal Astronomical Society for his photographs
of nebulæ. But the most important result for our purpose was produced in
France. There had been started many years before by the French astronomer
Chacornac a series of star maps round the Zodiac similar in intention to
the Berlin maps which figured in the history of the discovery of Neptune.
Chacornac died before his enterprise was very far advanced, and the work
was taken up by two brothers, Paul and Prosper Henry, who followed
Chacornac in adopting for the work the laborious method of eye
observation of each individual star. They proceeded patiently with the
work on these lines; but when they came to the region where the Zodiac is
crossed by the Milky Way, and the number of stars in a given area
increases enormously, they found the labour so great as to be practically
prohibitive, and were in doubt how to deal with the difficulty. It was at
this critical moment that these comet photographs, showing the stars so
beautifully, suggested the alternative of mapping the stars
photographically. They immediately set to work with a trial lens, and
obtained such encouraging results that they proceeded themselves to make a
larger lens of the same type; this again was satisfactory, and the idea
naturally arose of extending to the whole heavens the scheme which they
had hitherto intended only for the Zodiac, a mere belt of the heavens. But
this rendered the enterprise too large for a single observatory. It became
necessary to obtain the co-operation of other observatories, and with this
end in view an International Conference was summoned to meet in Paris in
1887 to consider the whole project. There were delegates from, if not all
nations, at any rate a considerable number:--
France 20
British Empire 8
Germany 6
Russia 3
Holland 3
U.S. America 3
Austria 2
Sweden 2
Denmark 2
Belgium 1
Italy 1
Spain 1
Switzerland 1
Portugal 1
Brazil 1
Argentine Republic 1
[Sidenote: Choice of instrument.]
[Sidenote: Expense of "doublet."]
[Sidenote: Advantages of reflector.]
[Sidenote: Refractor chosen.]
The Conference had a number of very important questions to discuss, for
knowledge of the photographic method and its possibilities was at that
time in its infancy. There was, for instance, the question whether all the
instruments need be of the same pattern, and if so what that pattern
should be. The first of these questions was settled in the affirmative, as
we might expect; in the interests of uniformity it was desirable that the
maps should be as nearly similar as possible. The second question was not
so easy; there were at least three different types of instruments which
might be used. First of all, there was the photographic lens, such as is
familiar to all who have used an ordinary camera, consisting of two lenses
with a space between; though since each of these lenses is itself made up
of two, we should more correctly say four lenses in all. It was with a
lens of this kind that the comet pictures had been taken at the Cape of
Good Hope, and it might seem the safest plan to adopt what had been shown
to be capable of such good work. But there was this difficulty; the
pictures of the comet were on a very small scale, and taken with a small
lens; a much larger lens was required for the scheme now under
contemplation, and when there are four separate lenses to be made, each
with two surfaces to polish, and each requiring a perfectly sound clear
piece of glass, it will be obvious that the difficulties of making a large
compound lens of this kind are much greater, and the expense much more
serious than in the case of a single lens, or even a pair. It was this
question of expense which had led the brothers Henry to experiment with a
different kind of instrument, in which only one pair of lenses was used
instead of two. Their instrument was, in fact, very similar to the
ordinary telescope, excepting that they were bound to make their lenses
somewhat different in shape in order to bring to focus the rays of light
suitable for photography, which are not the same as those suitable for eye
observation with the ordinary telescope. Dr. Common, again, had used a
third kind of instrument, mainly with the view of reducing the necessary
expense still further, or, perhaps, of increasing the size of the
instrument for the same expense. His telescope had no lens at all, but a
curved mirror instead, the mirror being made of glass silvered on the face
(not on the back as in the ordinary looking-glass). In this case there is
only one surface to polish instead of four, as in the Henrys' telescope,
or eight, as in the case of the photographic doublet; and, moreover, since
the rays of light are reflected from the surface of the glass, and do not
pass _through_ it at all, the internal structure of the glass is not so
strictly important as in the other cases. Hence the reflector is a very
cheap instrument, and it is, moreover, quite free from some difficulties
attached to the other instruments. No correction for rays of light of
different colours is required, since all rays of whatever colour come to
the same focus automatically. These advantages of the reflector were so
considerable as to almost outweigh one well-known disadvantage, which is,
however, not very easily expressed in words. The reflector might be
described as an instrument with a temper; sometimes it gives excellent
results, but at others _something_ seems to be wrong, though the worried
observer does not exactly know what. Long experience and patience are
requisite to humour the instrument and get the best results from it, and
it was felt that this uncertainty was sufficient to disqualify the
instrument for the serious piece of routine work contemplated in mapping
the heavens. Accordingly the handier and more amiable instrument with
which the brothers Henry had done such good work was selected as the
pattern to be adopted.
[Sidenote: Doublet would have been better.]
It is curious that at the Conference of 1887 nothing at all was said about
the type of instrument first mentioned (the "doublet lens"), although a
letter was written in its favour by Professor Pickering of Harvard College
Observatory. Since that time we have learnt much of its advantages, and it
is probable that if the Conference were to meet now they might arrive at a
different decision; but at that time they were, to put it briefly,
somewhat afraid of an instrument which seemed to promise, if anything, too
well, especially in one respect. With the reflector and the refractor it
had been found that the field of good images was strictly limited. The
Henrys' telescope would not photograph an area of the sky greater in
extent than 2° in diameter at any one time, and the reflector was more
limited still; within this area the images of the stars were good, and it
had been found that their places were accurately represented. Now the
"doublet" seemed to be able to show much larger areas than this with
accuracy, but no one had been able to test the accuracy to see whether it
was sufficient for astronomical purposes; and although no such feeling was
openly expressed or is on record, I think there is no doubt that a feeling
existed of general mistrust of an instrument which seemed to offer such
specious promises. Whatever the reason, its claims were passed over in
silence at the Conference, and the safer line (as it was then thought) of
adopting as the type the Henrys' instrument, was taken.
[Sidenote: The eighteen observatories.]
This was perhaps the most important question settled at the Conference,
and the answers to many of the others naturally followed. The size of the
plates, for instance, was settled automatically. The question down to what
degree of faintness should stars be included, resolved itself into the
equivalent question, What should be the length of time during which the
plates were exposed? Then, again, the question, What observatories should
take part in the work? became simply this: What observatories could
afford to acquire the instruments of this new pattern and get other funds
for carrying out the work specified? It was ultimately found that eighteen
observatories were able to obtain the apparatus and funds, though
unfortunately three of the eighteen have since found it impossible to
proceed. The following is the original list, and in brackets are added the
names of three other observatories which in 1900 undertook to fill the
places of the defaulters.
OBSERVATORIES CO-OPERATING FOR THE ASTROGRAPHIC CHART.
+----------------------+------------+----------+
| Observatory. | Zones of | Number |
| |Declination.|of Plates.|
+----------------------+------------+----------+
|Greenwich |+90° to +65°| 1149 |
|Rome |+64° " +55°| 1140 |
|Catania |+54° " +47°| 1008 |
|Helsingfors |+46° " +40°| 1008 |
|Potsdam |+39° " +32°| 1232 |
|Oxford |+31° " +25°| 1180 |
|Paris |+24° " +18°| 1260 |
|Bordeaux |+17° " +11°| 1260 |
|Toulouse |+10° " + 5°| 1080 |
|Algiers |+ 4° " - 2°| 1260 |
|San Fernando |- 3° " - 9°| 1260 |
|Tacubaya |-10° " -16°| 1260 |
|Santiago (Monte Video)|-17° " -23°| 1260 |
|La Plata (Cordoba) |-24° " -31°| 1360 |
|Rio (Perth, Australia)|-32° " -40°| 1376 |
|Cape of Good Hope |-41° " -51°| 1512 |
|Sydney |-52° " -64°| 1400 |
|Melbourne |-65° " -90°| 1149 |
+----------------------+------------+----------+
[Sidenote: Sky covered twice.]
In the list is also shown the total number of plates that were to be taken
by each observatory. When once the size of the plates had been settled,
it was a straightforward matter to divide up the sky into the proper
number of regions necessary to cover it completely, not only without gaps
between the plates, but with actually a small overlap of contiguous
plates. And more than this, it was decided that the whole sky should be
completely covered _twice over_. It was conceivable that a question might
arise whether an apparent star image on a plate was, on the one hand, a
dust speck, or, on the other hand, a planet, or perhaps a variable or new
star. By taking two different plates at slightly different times,
questions of this kind could be settled; and to make the check more
independent it was decided that the plates should not be exactly repeated
on the same portion of sky, but that in the second series the centre of a
plate should occupy the point assigned to the corner of a plate in the
first series.
[Sidenote: Times of exposure.]
Then there came the important question of time of exposure, which involved
a long debate between those who desired the most modest programme possible
consistent with efficiency, and those enthusiasts who were anxious to
strain the programme to the utmost limits attainable. Ultimately it was
resolved to take two series of plates; one series of long exposure which
was set in the first instance at 10 minutes, then became 15, then 30, then
40, and has by some enterprising observers been extended to 1-1/2 hours;
the other a series of short exposures which have been generally fixed at
6 minutes. Thus instead of covering the sky twice, it was decided to cover
it in all four times, and the number of plates assigned to each
observatory in the above list must be regarded as doubled by this new
decision. And further still, on the series of short-exposure plates it was
decided to add to the exposure of six minutes another one of three
minutes, having slightly shifted the telescope between the two so that
they should not be superimposed; and later still, a third exposure of
twenty seconds was added to these. It would take too long to explain here
the reasons for these details, but it will be clear that the general
result of the discussion was to extend the original programme
considerably, and render the work even more laborious than it had appeared
at the outset.
[Sidenote: Measurement of plates.]
[Sidenote: The réseau.]
[Sidenote: The microscope.]
[Sidenote: Reversal of plates.]
[Sidenote: Personal equation.]
When all these plates have been taken, the work is by no means finished;
indeed, it is only just commencing. There remains the task of measuring
accurately on each of the short-exposure plates the positions of the stars
which it represents, numbering on the average some 300 or 400; so that for
instance at Oxford the total number of stars measured on the twelve
hundred plates is nearly half a million. These are not all separate stars;
for the sky is represented twice over, and there is also the slight
overlap of contiguous plates; but the number of actual separate stars
measured at this one observatory is not far short of a quarter of a
million, and it has taken nearly ten years to make the measurements, with
the help of three or four measurers trained for the purpose. To render the
measures easy, a network or réseau of cross lines is photographed on each
plate by artificial light after it has been exposed to the stars, so that
on development these cross lines and the stars both appear. We can see at
a glance the approximate position of a star by counting the number of the
space from left to right and from top to bottom in which it occurs; and we
can also estimate the fraction of a space in addition to the whole number;
but it is necessary for astronomical purposes to estimate this fraction
with the greatest exactness. The whole numbers are already given with
great exactness by the careful ruling of the cross lines, which can be
spaced with extraordinary perfection. To measure the fraction, we place
the plate under a microscope in the eye-piece of which there is a finally
divided cross scale; the centre of the cross is placed over a star image,
and then it is noted where the lines of the réseau cut the cross scale. In
this way the position of the image of a star is read off with accuracy,
and after a little practice with considerable rapidity. It has been found
at Oxford that under favourable conditions the places of nearly 200 stars
per hour can be recorded in this way by a single measurer, if he has some
one to write down for him the numbers he calls out. This is only one form
of measuring apparatus; there are others in which, instead of a scale in
the eye-piece, micrometer screws are used to measure the fractions; but
the general principle in all these instruments is much the same, and the
rate of work is not very different; while to the minor advantages and
disadvantages of the different types there seems no need here to refer.
One particular point, however, is worth noting. After a plate has been
measured, it is turned round completely, so that left is now right, and
top is now bottom, and the measurements are repeated. This repetition has
the advantage first of all of checking any mistakes. When a long piece of
measuring or numerical work of any kind is undertaken there are invariably
moments when the attention seems to wander, and some small error is the
result. But there are also certain errors of a systematic character
similar to those denoted by the term "personal equation," which has found
its way into other walks of life. In the operation of placing a cross
exactly over the image of a star, different observers would show slight
differences of habit; one might place it a little more to the right than
another. But when the plate is turned round the effect of this habit on
the measure is exactly reversed, and hence if we take the mean of the two
measures any personal habit of this kind is eliminated. It has been found
by experience that such personal habits are much smaller for measures of
this kind than for those to which we have long been accustomed in
observations made by eye on the stars themselves. The troubles from
"personal equation" have been much diminished by the photographic method,
and certain peculiarities of the former method have been clearly exhibited
by the comparison. For instance, it has gradually become clear that with
eye observations personal equation is not a constant quantity, but is
different for stars of different brightness. When observing the transit of
a bright star the observer apparently records an instant definitely
earlier than in recording the transit of a faint one; and this peculiarity
seems to be common to the large majority of observers, which is perhaps
the reason why it was not noticed earlier. But when positions of the stars
determined in this way are compared with their positions measured on the
photographic plates, the peculiarity is made clearly manifest. For
example, at Oxford, our first business after making measurements is to
compare them with visual observations on a limited number of the brighter
stars made at Cambridge about twenty years ago. (About 14,000 stars were
observed at Cambridge, and we are dealing with ten times that number.) The
comparison shows that the Cambridge observations are affected with the
following systematic errors:--
If stars of magnitude 10 are observed correctly,
then " " 9 " 0.10 secs. too early
" " 8 " 0.16 "
" " 7 " 0.19 "
" " 6 " 0.21 "
" " 5 " 0.23 "
[Sidenote: Main object of the work.]
This may serve as an illustration of various incidental results which are
already flowing from the enormous and laborious piece of work which, as
far as the University Observatory at Oxford is concerned, we have just
completed, though some of the other colleagues are not so far advanced.
But the main results will not appear just yet. The work must be repeated,
and the positions of the stars just obtained must be compared with those
which they will be found to occupy at some future date, in order to see
what kind of changes are going on in the heavens. Whether this future date
shall be one hundred years hence, or fifty, or ten, or whether we should
begin immediately to repeat what has been done, is a matter not yet
decided, and one which requires some little consideration.
[Sidenote: The concluding year.]
I have said perhaps enough to give you a general idea of the work on which
we have been engaged at Oxford for the last ten years. Ten years ago it
seemed to stretch out in front of us rather hopelessly; the pace we were
able to make seemed so slow in view of the distance to be covered. We felt
rather like the schoolboy who has just returned to school and sees the
next holidays as a very remote prospect, and we solaced ourselves much in
the same way as he does, by making a diagram representing the total number
of plates to be dealt with and crossing off each one as it was finished,
just as he sometimes crosses off the days still remaining between him and
the prospective holidays. It was pleasant to watch the growth of the
number of crosses on this diagram, and by the end of the year 1902 we had
the satisfaction of seeing very little blank space remaining. Now, up to
this point it had not much mattered whether any particular plate was
secured in any particular year, or in a subsequent year, so long as there
were always sufficient plates to keep us occupied in measuring them. But
it then became a matter of importance to secure each plate at the proper
time of year; for the sun, as we know, travels round the Zodiac among the
stars, obliterating by his radiance a large section of the sky for a
period of some months, and in this way a particular region of the heavens
is apt to "run into daylight," as the observatory phrase goes, and ceases
to be available for photography during several months, until the sun is
again far enough away to allow of the particular region being seen at
night.
[Sidenote: A disappointment.]
[Sidenote: A curious plate.]
[Sidenote: A strange object.]
[Sidenote: A new star?]
Roughly speaking then, if a plate which should be taken in February is not
secured in this month owing to bad weather, the proper time for taking it
will not occur again until the following February; and when there was a
fair prospect of finishing our work in 1903, it became important to secure
each plate at the proper time in that year. Hence we were making special
efforts to utilise to the full any fine night that Providence sent in our
way, and on such occasions it is clearly an economy, if not exactly to
"make hay while the sun shines," at any rate to take plates vigorously
while the sun is _not_ shining and the night is fine; leaving the
development of them until the daytime. There is, of course, the risk that
the whole night's work may in this way be lost owing to some fault in the
plates, which might have been detected if some of them were immediately
developed. Perhaps in the early days of our work it would have been
reckless or foolish to neglect this little precaution; but we had for
years been accustomed to rely upon the excellence of the plates without
finding our trust betrayed; and the sensitiveness of the plates had
increased rather than diminished as time went on. Hence it will be readily
understood that when one fatal morning we developed a series of some
thirty plates, and found that owing to some unexplained lack of
sensitiveness they were all unsuitable for our purpose, it came as a most
unwelcome and startling surprise. It was, of course, necessary to make
certain that there was no oversight, that the developer was not at fault,
and that the weather had not been treacherous. All such possibilities were
carefully considered before communication with the makers of the plates,
but it ultimately became clear that there had been some unfortunate
failure in sensitiveness, and that it would be necessary to repeat the
work with opportunities restricted by the intervening lapse of time.
However, disappointments from this or similar causes are not unknown in
astronomical work; and we set about this repetition with as little loss of
time and cheerfulness as was possible. Under the circumstances, however,
it seemed desirable to examine carefully whether anything could be saved
from the wreck--whether any of the plates could be admitted as _just_
coming up to the minimum requirements. And I devoted a morning to this
inquiry. In the course of it I came across one plate which certainly
seemed worth an inclusion among our series from the point of view of the
number of stars shown upon it. It seemed quite rich in stars, perhaps even
a little richer than might have been expected. On inquiry I was told that
this was not one of the originally condemned plates, but one which had
been taken since the failure in sensitiveness of the plates had been
detected; was from a new and specially sensitive batch with which the
courteous makers had supplied us; but though there were certainly a
sufficient number of stars upon the plate, owing to some unexplained cause
the telescope had been erroneously pointed, and the region taken did not
correspond to the region required. To investigate the cause of the
discrepancy I thereupon took down from our store of plates the other one
of the same region which had been rejected for insufficiency of stars, and
on comparing the two it was at once evident that there was a strange
object on the plate taken later of the two, a bright star or other
heavenly body, which was not on the former plate. I have explained that by
repeating the exposure more than once, it is easily possible to recognise
whether a mark upon the plate is really a celestial body or is an
accidental blot or dust speck, and there was no doubt that this was the
image of some strange celestial body. It might, of course, be a new
planet, or even an old one which had wandered into the region; but a few
measures soon showed that it was not in movement. The measures consisted
in comparing the separation of the three exposures with the separation of
the corresponding exposures of obvious stars, for the exposures were not,
of course, simultaneous, and if the body were a planet and had moved in
the interval between them, this would be made manifest on measuring the
separations. No such movements could be detected; and the possibilities
were thus restricted to two. So far as we knew the object was a star, but
might be either a star of the class known as _variable_ or of that known
as _new_. In the former case it would become bright and faint at more or
less regular intervals, and might possibly have been already catalogued;
for the number of these bodies already known amounts to some hundreds.
Search being made in the catalogues, no entry of it was found, though it
still might be one of this class which had hitherto escaped detection. Or
it might be a "new star," one of those curious bodies which blaze up quite
suddenly to brightness and then die away gradually until they become
practically invisible. The most famous perhaps of these is the star which
appeared in 1572, and was so carefully observed by Tycho Brahé; but such
apparitions are rare, and altogether we have not records as yet of a score
altogether; so that in this latter case the discovery would be of much
greater interest than in the former. In either event it was desirable to
inform other observers as soon as possible of the existence of a strange
body; already some time had elapsed since the plate had been taken, March
16th, for the examination of which I have spoken was not made until March
24th. Accordingly, a telegram was at once despatched to the Central Office
at Kiel, which undertakes to distribute such information all over the
world, and a few post-cards were sent to observers close at hand who might
be able to observe the star the same night. Certain observations with the
spectroscope soon made it clear that the object was really a "new star."
[Sidenote: The discovery accidental.]
[Sidenote: Mrs. Fleming's discoveries.]
This, therefore, is the discovery which we made at Oxford: as you will
see, in an entirely accidental manner, during the course of a piece of
work in which it was certainly never contemplated. Its purely accidental
nature is sufficiently illustrated by the fact that if the plates
originally supplied by the makers had been of the proper quality, the
plate which led to the discovery would never have been taken. If the
plates exposed in February had been satisfactory, we should have been
content, and should not have repeated the exposure on March 16th. Again I
can testify personally how purely accidental it was that the examination
was made on March 24th to see whether anything could be saved, as I have
said, from the wreck. The idea came casually into my mind as I was walking
through the room and saw the neat pile of rejected plates; and one may
fairly call it an accidental impulse. This new star is not, however, the
first of such objects to have been discovered "accidentally"; many of the
others were found just as much by chance, though a notable exception must
be made of those discovered at the Harvard Observatory, which are the
result of a deliberate search for such bodies by the careful examination
of photographic plates. Mrs. Fleming, who spends her life in such work,
has had the good fortune to detect no less than six of these wonderful
objects as the reward of her laborious scrutiny; and she is the _only_
person who has thus found new stars by photography until this accidental
discovery at Oxford. The following is a complete list of new stars
discovered to date:--
LIST OF NEW STARS.
+----------------------------------------------+
|Ref. No.| Constellation. | Year.| Discoverer. |
+----------------------------------------------+
| 1 | Cassiopeia | 1572 | Tycho Brahé.|
| 2 | Cygnus | 1600 | Janson. |
| 3 | Ophiuchus | 1604 | Kepler. |
| 4 | Vulpecula | 1670 | Anthelm. |
| 5 | Ophiuchus | 1848 | Hind. |
| 6 | Scorpio | 1860 | Auwers. |
| 7 | Corona Borealis| 1866 | Birmingham. |
| 8 | Cygnus | 1876 | Schmidt. |
| 9 | Andromeda | 1885 | Hartwig. |
| 10 | Perseus | 1887 | Fleming. |
| 11 | Auriga | 1891 | Anderson. |
| 12 | Norma | 1893 | Fleming. |
| 13 | Carina | 1895 | Fleming. |
| 14 | Centaurus | 1895 | Fleming. |
| 15 | Sagittarius | 1898 | Fleming. |
| 16 | Aquila | 1899 | Fleming. |
| 17 | Perseus | 1901 | Anderson. |
| 18 | Gemini | 1903 | At Oxford. |
+----------------------------------------------+
[Illustration:
MARCH 1, 1903 MARCH 14, 1903
VIII.--THE OXFORD NEW STAR.
A PAIR OF PHOTOGRAPHS TAKEN AT THE HARVARD COLLEGE OBSERVATORY BEFORE
AND AFTER ITS APPEARANCE
(_The arrow indicates the place of the new star. It will be seen that
the left-hand picture though it shews fainter stars than the other, has
not a trace of the new star._)]
[Sidenote: Dr. Anderson.]
[Sidenote: Nova Persei.]
Generally these stars have been noted by eye observation, as in the case
of the two found by Dr. Anderson of Edinburgh. In these cases also we may
say that deliberate search was rewarded; for Dr. Anderson is probably the
most assiduous "watcher of the skies" living, though he seldom uses a
telescope; sometimes he uses an opera-glass, but usually the naked eye. He
describes himself as an "Astrophil" rather than as an astronomer. "I love
the stars," he says; "and whenever they are shining, I must be looking."
And so on every fine night he stands or sits at his open study window
gazing at the heavens. I believe he was just about to leave them for his
bed, near 3 A.M. on the night of February 21, 1901, when, throwing a last
glance upward, he suddenly saw a brilliant star in the constellation
Perseus. His first feeling was actually one of disappointment, for he felt
sure that this object must have been there for some time past without his
knowing of it, and he grudged the time lost when he might have been
regarding it. More in a spirit of complaint than of inquiry, he made his
way to the Royal Observatory at Edinburgh next day to hear what they had
to say about it, though he found it difficult to approach the subject. He
first talked about the weather, and the crops, and similar topics of
general interest; and only after some time dared he venture a casual
reference to the "new portent in the heavens." Seeing his interlocutor
look somewhat blank, he ventured a little farther, and made a direct
reference to the new star in Perseus; and then found to his astonishment,
as also to his great delight, that he was the first to bring news of it.
The news was soon communicated to other observers; all the telescopes of
the world were soon trained upon it; and this wonderful "new star of the
new century" has taught us more of the nature of these extraordinary
bodies than all we knew before.
[Sidenote: Records previous to discovery.]
[Sidenote: Was Nova Geminorum previously shining faintly?]
[Sidenote: The suspicion negatived.]
Perhaps I may add a few remarks on one or two features of these bodies.
Firstly, let us note that Professor Pickering of Harvard is now able to
make a most important contribution to the _former_ history of these
objects--that is to say, their history preceding their actual detection.
We remember that, after Uranus had been discovered, it was found that
several observers had long before recorded its place unknowingly; and
similarly Professor Pickering and his staff have usually photographed
other new objects unknowingly. There are on the shelves at Harvard vast
stores of photographs, so many that they are unable to examine them when
they have been taken; but once any object of interest has been discovered,
it is easy to turn over the store and examine the particular plates which
may possibly show it at an earlier date. In this way it was found that Dr.
Anderson's new star had been visible only for a few days before its
discovery, there being no trace of it on earlier plates. Similarly, in
the case of the new star found at Oxford, plates taken on March 1st and
6th, fifteen days and ten days respectively before the discovery-plate of
March 16th, showed the star. But, in this particular instance, greater
interest attaches to two still earlier plates taken elsewhere, and with
exposures much longer than any available at Harvard. One had been obtained
at Heidelberg by Dr. Max Wolf, and another at the Yerkes Observatory of
Chicago University, by Mr. Parkhurst; and on both there appeared to be a
faint star of about the fourteenth or fifteenth magnitude, in the place
subsequently occupied by the Nova; and the question naturally arose, Was
this the object which ultimately blazed up and became the new star? To
settle this point, it was necessary to measure its position, with
reference to neighbouring stars, with extreme precision; and here it was
unfortunate that the photographs did not help us as much as they might,
for they were scarcely capable of being measured with the requisite
precision. The point was an important one, because if the identity of the
Nova with this faint star could be established, it would be the second
instance of the kind; but so far as they went, measurements of the
photographs were distinctly against the identity. Such was the conclusion
of Mr. Parkhurst from his photograph alone; and it was confirmed by
measures made at Oxford on copies of both plates, which were kindly sent
there for the purpose. The conclusion seemed to be that there was a faint
star _very near_, but _not at_, the place of the new star; and it was
therefore probable that, although this faint star was temporarily
invisible from the brightness of the adjacent Nova, as the latter became
fainter (in the way with which we have become familiar in the case of new
stars), it might be possible to see the two stars alongside each other.
This critical observation was ultimately made by the sharp eyes of
Professor Barnard, aided by the giant telescope of the Yerkes Observatory;
and it seems clear therefore that the object which blazed up to become the
Nova of 1903 could not have previously been so bright as a faint star of
the fourteenth magnitude. Although this is merely a negative conclusion,
it is an important one in the history of these bodies.
[Sidenote: Nebula round Nova Persei.]
[Sidenote: Its changes.]
[Sidenote: Due to travelling illumination.]
The second point to which I will draw your attention is from the history
of the other Nova just mentioned--Dr. Anderson's New Star of 1901. In this
instance it is not the history previous to discovery, but what followed
many months after discovery, that was of engrossing interest; and again
Yerkes Observatory, with its magnificent equipment, played an important
part in the drama. When, with its giant reflecting telescope, photographs
were taken of the region of Nova Persei after it had become comparatively
faint, it was found that there was an extraordinarily faint nebulosity
surrounding the star. Repeating the photographs at intervals, it was
found that this nebulosity was rapidly changing in shape. "Rapidly" is, of
course, a relative term, and a casual inspection of two of the photographs
might not convey any impression of rapidity; it is only when we come to
consider the enormous distance at which the movements, or apparent
movements, of the nebulæ must be taking place that it becomes clear how
rapid the changes must be. It was not possible to determine this distance
with any exactness, but limits to it could be set, and it seemed probable
that the velocity of the movement was comparable with that of light. The
conclusion suggested itself that the velocity might actually be identical
with that of light, in which case what we saw was not the movement of
actual matter, but merely that of illumination, travelling from point to
point of matter already existing.
[Illustration:
SEPT. 20, 1901 NOV. 13, 1901
IX--NEBULOSITY ROUND NOVA PERSEI
(_From photographs taken at the Yerkes Observatory by G. W. Ritchey._)]
[Sidenote: When did it all happen?]
An analogy from the familiar case of sound may make clearer what is meant.
If a loud noise is made in a large hall, we hear echoes from the walls.
The sound travels with a velocity of about 1100 feet per second, reaches
the walls, is reflected back from them, and returns to us with the same
velocity. From the interval occupied in going and returning we could
calculate the distance of the walls. The velocity of light is so enormous
compared with that of sound that we are usually quite unable to observe
any similar phenomenon in the case of light. If we strike a match in the
largest hall, all parts of it are illuminated so immediately that we
cannot possibly realise that there was really an interval between the
striking of the match, the travelling of the light to the walls, and its
return to our eyes. The scale of our terrestrial phenomenon is far too
small to render this interval perceptible. But those who accept the theory
above mentioned regarding the appearances round Nova Persei (although
there are some who discredit it) believe that we have in this case an
illustration of just this phenomenon of light echoes, on a scale large
enough to be easily visible. They think that, surrounding the central star
which blazed up so brightly in February 1901, there was a vast dark
nebula, of which we had no previous knowledge, because it was not shining
with any light of its own. When the star blazed up, the illumination
travelled from point to point of this dark nebula and lighted it up; but
the size of the nebula was so vast that, although the light was travelling
with the enormous velocity of 200,000 miles per second, it was not until
months afterwards that it reached different portions of this nebula; and
we accordingly got news of the existence of this nebula some months after
the news reached us of the central conflagration, whatever it was. Remark
that all we can say is that the news of the nebula reached us _some months
later_ than that of the outburst. The actual date when either of the
actual things happened, we have as yet no means of knowing; it may have
been hundreds or even thousands of years ago that the conflagration
actually occurred of which we got news in February 1901, the light having
taken all that time to reach us from that distant part of space; and the
light reflected from the nebula was following it on its way to us all
these years at that same interval of a few months.
[Sidenote: An objection.]
Now, let me refer before leaving this point to the chief objection which
has been urged against this theory. It has been maintained that the
illumination would necessarily appear to travel outwards from the centre
with an approach to uniformity, whereas the observed rate of travel is not
uniform, and has been even towards the centre instead of away from it;
which would seem as though portions of the nebula more distant from the
centre were lighted up sooner than those closer to it. By a simple
illustration from our solar system, we shall see that these curious
anomalies may easily be explained. Let us consider for simplicity two
planets only, say the Earth and Saturn. We know that Saturn travels round
the sun in an orbit which is ten times larger than the orbit of the earth.
Suppose now that the sun were suddenly to be extinguished; light takes
about eight minutes to travel from the sun to the earth, and consequently
we should not get news of the extinction for some eight minutes; the sun
would appear to us to still go on shining for eight minutes after he had
really been extinguished. Saturn being about ten times as far away from
the sun, the news would take eighty minutes to reach Saturn; and from the
earth we should see Saturn shining more[3] than eighty minutes after the
sun had been extinguished, although we ourselves should have lost the
sun's light after eight minutes. I think we already begin to see
possibilities of curious anomalies; but they can be made clearer than
this. Instead of imagining an observer on the earth, let us suppose him
removed to a great distance away in the plane of the two orbits; and let
us suppose that the sun is now lighted up again as suddenly as the new
star blazed up in February 1901. Then such an observer would first see
this blaze in the centre; eight minutes afterwards the illumination would
reach the earth, a little speck of light near the sun would be
illuminated, just as we saw a portion of the dark nebula round Nova Persei
illuminated; eighty minutes later another speck, namely, Saturn, would
begin to shine. But now, would Saturn necessarily appear to the distant
observer to be farther away from the sun than the earth was? Looking at
the diagram, we can see that if Saturn were at S{1} then it would present
this natural appearance of being farther away from the sun than the earth;
but it might be at S{2} or S{3}, in which case it would seem to be nearer
the sun, and the illumination would seem to travel inwards towards the
central body instead of outwards. Without considering other cases in
detail, it will be tolerably clear that almost any anomalous appearance
might be explained by choosing a suitable arrangement of the nebulous
matter which we suppose lighted up by the explosion of Nova Persei.
Another objection urged against the theory I have sketched is that the
light reflected from such a nebula would be so feeble that it would not
affect our photographic plates. This depends upon various assumptions
which we have no time to notice here; but I think we may say that there is
certainly room for the acceptance of the theory.
[Illustration: FIG. 6.]
[Sidenote: Did the nebula cause the outburst?]
Now, if this dark nebula was previously existing in this way all round the
star which blazed up, the question naturally arises whether the nebula had
anything to do with the conflagration. Was there previously a star, either
so cold or so distant as not to be shining with appreciable light, which,
travelling through space, encountered this vast nebula, and by the
friction of the encounter was suddenly rendered so luminous as to outshine
a star of the first magnitude? The case of meteoric stones striking our
own atmosphere seems to suggest such a possibility. These little stones
are previously quite cold and invisible, and are travelling in some way
through space, many of them probably circling round our sun. If they
happen in their journey to encounter our earth, even the extremely tenuous
atmosphere, so thin that it will scarcely bend the rays of light
appreciably, even this is sufficient by its friction to raise the stones
to a white heat, so that they blaze up into the falling stars with which
we are familiar. This analogy is suggested, but we must be cautious in
accepting it; for we know so very little of the nature of nebulæ such as
that of which we have been speaking. But in any case, a totally new series
of phenomena have been laid open to our study by those wonderful
photographs taken at the Yerkes Observatory and the Lick Observatory in
the few years which the present century has as yet run.
[Sidenote: Importance of new stars]
One thing is quite certain: we must lose no opportunity of studying such
stars as may appear, and no diligence spent in discovering them at the
earliest possible moment is thrown away. We have only known up to the
present, as already stated, less than a score of them, and of these many
have told us but little; partly because they were only discovered too late
(after they had become faint), and partly because the earlier ones could
not be observed with the spectroscope, which had not then been invented.
It seems clear that in the future we must not allow accident to play so
large a part in the discovery of these objects; more must be done in the
way of deliberate search. Although we know beforehand that this will
involve a vast amount of apparently useless labour, that months and years
must be spent in comparing photographic plates, or portions of the sky
itself, with one another without detecting anything remarkable, it will
not be the first time that years have been cheerfully spent in such
searches without result. We need only recall Hencke's fifteen years of
fruitless search, before finding a minor planet, to realise this fact.
[Sidenote: Superposition of plates.]
[Sidenote: The stereo-comparator.]
One thing of importance may be done; we may improve our methods of making
the search, so as to economise labour, and several successful attempts
have already been made in this direction. The simplest plan is to
superpose two photographs taken at different dates, so that the stars on
one lie very close to those on the other; then if an image is seen to be
unpaired we _may_ have found a new star, though of course the object may
be merely a planet or a variable. The superposition of the plates may be
either actual or virtual. A beautiful instrument has been devised on the
principle of the stereoscope for examining two plates placed side by side,
one with each eye. We know that in this way two photographs of the same
object from different points of view will appear to coalesce, and at the
same time to give an appearance of solidity to the object or landscape,
portions of which will seem to stand out in front of the background.
Applying this principle to two photographs of stars, what happens is this:
if the stars have all remained in the same positions exactly, the two
pictures will seem to us to coalesce, and the images all to lie on a flat
background; but if in the interval between the exposures of the two plates
one of the stars has appreciably moved or disappeared, it will seem, when
looked at with this instrument, to stand out in front of this background,
and is accordingly detected with comparatively little trouble. This new
instrument, to which the name Stereo-comparator has been given, promises
to be of immense value in dredging the sky for strange bodies in the
future. I am glad to say that a generous friend has kindly presented the
University Observatory at Oxford with one of these beautiful instruments,
which have been constructed by Messrs. Zeiss of Jena after the skilful
designs of Dr. Pulfrich. Whether we shall be able to repeat by deliberate
search the success which mere accident threw in our way remains to be
seen.
CHAPTER V
SCHWABE AND THE SUN-SPOT PERIOD
[Sidenote: Discoveries contrary to expectation.]
In preceding chapters we have reviewed discoveries, some of which have
been made as a result of a deliberate search, and others accidentally in
the course of work directed to a totally different end; but so far we have
not considered a case in which the discoverer entered upon an enterprise
from which he was positively dissuaded.
[Sidenote: Nothing expected from spots.]
In the next chapter we shall come across a very striking instance of this
type; but even in the discovery that there was a periodicity in the solar
spots, with which I propose to deal now, Herr Schwabe began his work in
the face of deterrent opinions from eminent men. His definite announcement
was first made in 1843, though he had himself been convinced some years
earlier. In 1857 the Royal Astronomical Society awarded him their gold
medal for the discovery; and in the address delivered on the occasion the
President commenced by drawing attention to this very fact, that
astronomers who had expressed any opinions on the subject had been
uniformly and decidedly against the likelihood of there being anything
profitable in the study of the solar spots. I will quote the exact words
of the President, Mr. Manuel Johnson, then Radcliffe Observer at Oxford.
"It was in 1826 that Heinrich Schwabe, a gentleman resident in
Dessau, entered upon those researches which are now to engage our
attention. I am not aware of the motive that induced him--whether any
particular views had suggested themselves to his own mind--or whether
it was a general desire of investigating, more thoroughly than his
predecessors had done, the laws of a remarkable phenomenon, which it
had long been the fashion to neglect. He could hardly have
anticipated the kind of result at which he has arrived; at the same
time we cannot imagine a course of proceeding better calculated for
its detection, even if his mind had been prepared for it, than that
which he has pursued from the very commencement of his career.
Assuredly if he entertained such an idea, it was not borrowed from
the authorities of the last century, to whom the solar spots were
objects of more attention than they have been of late years.
"'Nulla constanti temporum lege apparent aut evanescunt,' says Keill
in 1739.--_Introduct. ad Physic. Astronom._, p. 253.
"'Il est manifest par ce que nous venons de rapporter qu'il n'y a
point de règle certaine de leur formation, ni de leur nombre et de
leur figure,' says Cassini II. in 1740.--_Elém d'Astron._, vol. i. p.
82.
"'Il semble qu'elles ne suivent aucune loi dans leur apparitions,'
says Le Monnier in 1746.--_Instit. Astron._, p. 83.
"'Solar spots observe no regularity in their shape, magnitude,
number, or in the time of their appearance or continuance,' says Long
in 1764.--_Astron._, vol. ii. p. 472.
"'Les apparitions des tâches du soleil n'ont rien de regulier,' says
Lalande in 1771.--_Astron._, vol. iii. § 3131, 2nd edit.
"And Delambre's opinion may be inferred from a well-known passage in
the third volume of his 'Astronomy' (p. 20), published in 1814, where
treating of the solar spots he says, 'Il est vrai qu'elles sont plus
curieuses que vraiment utiles.'"[4]
It will thus be evident that Herr Schwabe had the courage to enter upon a
line of investigation which others had practically condemned as likely to
lead nowhere, and that his discovery was quite contrary to expectation. It
is a lesson to us that not even the most unlikely line of work is to be
despised; for the outcome of Schwabe's work was the first step in the
whole series of discoveries which have gradually built up the modern
science of Solar Physics, which occupies so deservedly large a part of the
energies of, for instance, the great observatory attached to the
University of Chicago.
[Sidenote: Schwabe's announcement.]
It has been our practice to recall the actual words in which the
discoverer himself stated his discovery, and I will give the original
modest announcement of Schwabe, though for convenience of those who do not
read German I will attempt a rough translation. He had communicated year
by year the results of his daily counting of the solar spots to the
_Astronomische Nachrichten_, and after he had given ten years' results in
this way he collected them together, but he made no remark on the curious
sequence which they undoubtedly showed at that time. Waiting patiently six
years for further material, in 1843 he ventured to make his definite
announcement as follows:--"From my earlier observations, which I have
communicated annually to this journal, there was manifest already a
certain periodicity of sun-spots; and the probability of this being really
the case is confirmed by this year's results. Although I gave in volume 15
the total numbers of groups for the years 1826-1837, nevertheless I will
repeat here a complete series of all my observations of sun-spots, giving
not only the number of groups, but also the number of days of observation,
and further the days when the sun was free from spots. The number of
groups alone will not in itself give sufficient accuracy for determination
of a period, since I have convinced myself that when there are a large
number of sun-spots the number will be reckoned somewhat too small, and
when few sun-spots, the number somewhat too large; in the first case
several groups are often counted together in one, and in the second it is
easy to divide a group made up of two component parts into two separate
groups. This must be my excuse for repeating the early catalogue, as
follows:--
+---------------------------------------------+
| Year.| Number of | Days free | Days of |
| | Groups. | from Spots.| Observation.|
|---------------------------------------------|
| 1826 | 118 | 22 | 277 |
| 1827 | 161 | 2 | 273 |
| 1828 | 225 | 0 | 282 |
| 1829 | 199 | 0 | 244 |
| 1830 | 190 | 1 | 217 |
|---------------------------------------------|
| 1831 | 149 | 3 | 239 |
| 1832 | 84 | 49 | 270 |
| 1833 | 33 | 139 | 267 |
| 1834 | 51 | 120 | 273 |
| 1835 | 173 | 18 | 244 |
|---------------------------------------------|
| 1836 | 272 | 0 | 200 |
| 1837 | 333 | 0 | 168 |
| 1838 | 282 | 0 | 202 |
| 1839 | 162 | 0 | 205 |
| 1840 | 152 | 3 | 263 |
|---------------------------------------------|
| 1841 | 102 | 15 | 283 |
| 1842 | 68 | 64 | 307 |
| 1843 | 34 | 149 | 324 |
|(1844)| (52) | (111) | (320) |
+---------------------------------------------+
"If we now compare together the number of groups, and the days free from
spots, we find that the sun-spots have a period of about ten years, and
that for about five years they are so numerous that during this period few
days, if any, are free from spots. The sequel must show whether this
period is constant, whether the minimum activity of the sun in producing
spots lasts for one or two years, and whether this activity increases more
quickly than it decreases."
[Illustration:
FEB. 18, 1894. FEB. 19, 1894.
X.--PHOTOGRAPHS OF THE SUN TAKEN AT THE ROYAL OBSERVATORY, GREENWICH,
SHEWING SUNSPOTS.]
[Sidenote: Attracted little attention, until eight years later.]
This brief announcement is all that the discoverer says upon the subject;
and it is perhaps not remarkable that it attracted very little attention,
especially when we remember that it related to a matter which the
astronomical world had agreed to put aside as unprofitable and not worth
attention. Next year, in giving his usual paper on the spots for 1844 he
recurs to the subject in the following sentence: "The periodicity of spots
of about ten years which was indicated in my summary published last year,
is confirmed by this year's observations." I have added in brackets to the
table above reproduced the numbers for 1844 subsequently given, and it
will be seen how nearly they might have been predicted.
[Sidenote: Other phenomena sympathetic and others not.]
Still the subject attracted little attention. Turning over the leaves of
the journal at random, I came across the annual report of the Astronomer
Royal of England, printed at length. But in it there is no reference to
this discovery, which opened up a line of work now strongly represented in
the annual programme of the Royal Observatory at Greenwich. Mr. Johnson
remarks that the only person who had taken it up was Julius Schmidt, who
then resided near Hamburg. But Schwabe went on patiently accumulating
facts; and in 1851 the great Von Humboldt in the third volume of his
_Cosmos_, drew attention to the discovery, which was accordingly for the
first time brought into general notice. It will be seen that there are not
many facts of general interest relating to the actual discovery beyond the
courage with which the work was commenced in a totally unpromising
direction, and the scant attention it received after being made for us. We
may admit that interest centres chiefly in the tremendous consequences
which flowed from it. We now recognise that many other phenomena are bound
up with this waxing and waning of the solar spots. We might be prepared
for a sympathy in phenomena obviously connected with the sun itself; but
it was an unexpected and startling discovery that magnetic phenomena on
the earth had also a sympathetic relation with the changes in sun-spots,
and it is perhaps not surprising that when once this connection of solar
and terrestrial phenomena was realised, various attempts have been made to
extend it into regions where we cannot as yet allow that it has earned a
legitimate right of entry. We have heard of the weather and of Indian
famines occurring in cycles identical with the sun-spot cycle; and it is
obvious how tremendously important it would be for us if this were found
to be actually the case. For we might in this way predict years of
possible famine and guard against them; or if we could even partially
foretell the kind of weather likely to occur some years hence, we might
take agricultural measures accordingly. The importance of the connection,
if only it could be established, is no doubt the reason which has misled
investigators into laying undue stress on evidence which will not bear
close scrutiny. For the present we must say decidedly that no case has
been made out for paying serious attention to the influence of sun-spots
on weather. Nevertheless, putting all this aside, there is quite enough of
first-rate importance in the sequel to Schwabe's discovery.
[Sidenote: Greenwich sun records.]
[Sidenote: The sun's rotation.]
Let us review the facts in order. Most of us, though we may not have had
the advantage of seeing an actual sun-spot through a telescope, have seen
drawings or photographs of spots. There is a famous drawing made by James
Nasmyth (of steam-hammer fame), in July, 1864, which is of particular
interest, because at that time Nasmyth was convinced--and he convinced
many others with him--that the solar surface was made up of a
miscellaneous heap of solid bodies in shape like willow leaves, or grains
of rice, thrown together almost at random, and the drawing was made by him
to illustrate this idea. Comparing a modern photograph with it, we see
that there is something to be said for Nasmyth's view, which attracted
much attention at the time and occasioned a somewhat heated controversy.
But since the invention of the spectroscope it has become quite obsolete;
it probably does not correspond in any way to the real facts. But instead
of looking at pictures which have been enlarged to show the detailed
structure in and near a spot, we will look at a series of pictures of
the whole sun taken on successive days at Greenwich in which the spots are
necessarily much smaller, but which show the behaviour of the spots from
day to day. (See Plates X. and XI.) From the date at the foot of each it
will be seen that they gradually cross the disc of the sun (a fact first
discovered by Galileo in 1610), showing that the sun rotates on an axis
once in about every twenty-five days. There are many interesting facts
connected with this rotation; especially that the sun does not rotate as a
solid body, the parts near the (Sun's) Equator flowing quicker than those
nearer the Poles; but for the present we cannot stop to dwell upon them.
What interests us particularly is the history, not from day to day, but
from year to year, as Schwabe has already given it for a series of years.
[Illustration:
FEB. 20, 1894. FEB. 21, 1894.
XI.--PHOTOGRAPHS OF THE SUN TAKEN AT THE ROYAL OBSERVATORY, GREENWICH,
SHEWING SUNSPOTS]
[Sidenote: Wolf's numbers.]
[Sidenote: Greenwich areas.]
[Sidenote: Magnetic fluctuations.]
When it became generally established that this periodicity existed, Rudolf
Wolf of Zurich collected the facts about sun-spots from the earliest
possible date, and represented this history by a series of numbers which
are still called Wolf's Sun-Spot Numbers. You will see from the diagram
the obvious rise and fall for eleven years,--not ten years, as Schwabe
thought, but just a little over eleven years. The facts are, however,
given more completely by the work done at the Royal Observatory at
Greenwich. It is part of the regular daily work of that Observatory to
photograph the sun at least twice. Many days are of course cloudy or wet,
so that photographs cannot be obtained; but there are available
photographs similarly taken in India or in Mauritius, where the weather is
more favourable, and from these the gaps are so well filled up that very
few days, if any, during the whole year are left without some photograph
of the sun's surface. On these photographs the positions and the areas of
the spots are carefully measured under a microscope, and the results when
submitted to certain necessary calculations are published year by year. It
is clearly a more accurate estimate of the spottedness of the sun to take
the total _area_ of all the spots rather than their mere _number_, for in
the latter case a large spot and a small one count equally. Hence the
Greenwich records will perhaps give us an even better idea of the
periodicity than Wolf's numbers. Now, at the same observatory magnetic
observations are also made continuously. If a magnet be suspended freely
we are accustomed to say that it will point to the North Pole; but this is
only very roughly true. In the first place, it is probably well known to
you that there is a considerable deviation from due north owing to the
fact that the magnetic North Pole is not the same as the geographical
North Pole; but this for the present need not concern us. What does
concern us is, that if the needle is hung up and left long enough to come
to rest, it does not then remain steadily at rest, but executes slow and
small oscillations backwards and forwards, up and down, throughout the
day; repeating nearly the same oscillations on the following day, but at
the same time gradually changing its behaviour so as to oscillate
differently in summer and winter. These changes are very small, and would
pass unnoticed by the naked eye; but when carefully watched through a
telescope, or better still, when photographed by some apparatus which will
at the same time magnify them, they can be rendered easily visible. When
the history of these changes is traced it is seen at once that there is a
manifest connection with the cycle of sun-spot changes; for instance, if
we measure the range of swing backwards and forwards during the day and
take the average for all the days in the year, and then compare this with
the average number of sun-spots, we shall see that the averages rise and
fall together. Similarly we may take the up and down swing, find the
average amount of it throughout the year, and again we shall find that
this corresponds very closely with the average number of sun-spots.
[Illustration: PLATE XII. NUMBER OF SUNSPOTS (Wolf) Compared with DAILY
RANGE of MAGNETIC DECLINATION & DAILY RANGE of MAGNETIC HORZL. FORCE
(as observed at Greenwich.)]
[Sidenote: Daily curves.]
[Sidenote: Difference between summer and winter, and between sun-spot
maximum and minimum.]
[Sidenote: Cause unknown.]
But perhaps the most striking way to exhibit the sympathy is to combine
different variations of the needle into one picture. And first we must
remark that there is another important variation of the earth's magnetic
action which we have not yet considered. We have mentioned the swing of
the needle to and fro, and the swing up and down, and these correspond to
changes in the _direction_ of the force of attraction on the needle. But
there may be also changes in _intensity_ of this action; the pull may be a
little stronger or a little weaker than before, and these variations are
not represented by any actual movement of the needle, though they can be
measured by proper experiments. We can, however, imagine them represented
by a movement of the end of the needle if we suppose it made of elastic
material, so that it would lengthen when the force was greater and
contract slightly when the force was less. If a pencil were attached to
the end of such an elastic needle so as to make a mark on a sheet of
paper, and if for a moment we exclude the up and down movements, the
pencil would describe during the day a curve on the paper, as the end of
the needle swung backwards and forwards with the change in direction, and
moved across the direction of swing with the change in intensity. Now when
curves of this kind are described for a day in each month of the year,
there is a striking difference between the forms of them. During the
summer months they are, generally speaking, comparatively large and open,
and during the winter months they are small and close. This change in form
is seen by a glance at Plate XIII., which gives the curves throughout the
whole of one year. Let us now, instead of forming a curve of this kind for
each month, form a single average curve for the whole year; and let us
further do this for a series of years. (Plate XIV.) We see that the curves
change from year to year in a manner very similar to that in which they
change from month to month in any particular year, and the law of change
is such that in years when there are many sun-spots we get a large open
curve similar to those found in the summer, while for years when there are
few sun-spots we get small close curves very like those in the winter.
Hence we have two definite conclusions suggested: firstly, that the
changes of force are sympathetic with the changes in the sun-spots; and
secondly, that times of maximum sun-spots correspond to summer, and times
of minimum to winter. And here I must admit that this is about as far as
we have got at present in the investigation of this relationship. _Why_
the needle behaves in this way we have as yet only the very vaguest ideas;
suggestions of different kinds have certainly been put forward, but none
of them as yet can be said to have much evidence in favour of its being
the true one. For our present purpose, however, it is sufficient to note
that there is this very real connection, and that consequently Schwabe's
sun-spot period may have a very real importance with regard to changes in
our earth itself.
[Illustration:
GREENWICH MAGNETIC CURVES
1859-60
PLATE XIII.
GREENWICH MAGNETIC CURVES FOR APRIL 1841-1860]
[Sidenote: Illustration of spurious connection.]
But I may perhaps repeat the word of caution already uttered against
extending without sufficient evidence this notion of the influence of
sun-spots to other phenomena, such as weather. A simple illustration will
perhaps serve better than a long argument to show both the way in which
mistakes have been made and the way in which they can be seen to be
mistakes. There is at the Royal Observatory at Greenwich an instrument for
noting the direction of the wind, the essential part being an ordinary
wind-vane, the movements of which are automatically recorded on a sheet of
paper. As the wind shifts from north to east the pencil moves in one
direction, and when it shifts back again towards the north the pencil
moves in the reverse way. But sometimes the wind shifts continuously from
north to east, south, west, and back to north again, the vane making a
complete revolution; and this causes the pencil to move continuously in
one direction, until when the vane has come to north again, the pencil is
far away from the convenient place of record; on such occasions it is
often necessary to replace it by hand. Then again, the vane may turn in
the opposite direction, sending the pencil inconveniently to the other
side of the record. During the year it is easy to count the number of
complete changes of wind in either direction, and subtracting one number
from the other, we get the excess of complete revolutions of the vane in
one direction over that in the other. Now if these rather arbitrary
numbers are set down year by year, or plotted in the shape of a diagram,
we get a curve which may be compared with the sun-spot curve, and during a
period of no less than sixteen years--from 1858 to 1874--there was a
remarkable similarity between the two diagrams. From this evidence _alone_
it might fairly be inferred that the sun-spots had some curious effect
upon the weather at Greenwich, traceable in this extraordinary way in the
changes of the wind. But the particular way in which these changes are
recorded is so arbitrary that we should naturally feel surprise if there
was a real connection between the two phenomena; and fortunately there
were other records preceding these years and following them which enabled
us to test the connection further, and it was found, as we might naturally
expect, that it was not confirmed. On looking at diagrams (Plate XV.) for
the periods before and after, no similarity can be traced between the
sun-spot curve and the wind-vane curve, and we infer that the similarity
during the period first mentioned was entirely accidental. This shows that
we must be cautious in accepting, from a limited amount of evidence, a
connection between two phenomena as real and established; for it may be
purely fortuitous. We may particularly remark that it is desirable to have
repetitions through several complete periods instead of one alone. It is
possible to reduce to mathematical laws the rules for caution in this
matter; and much useful work has already been done in this direction by
Professor Schuster of Manchester and others, though as yet too little
attention has been paid to their rules by investigators naturally eager to
discover some hitherto unthought-of connection between phenomena.
[Sidenote: Faculæ follow spots and the chromosphere.]
With this example of the need for caution, we may return to phenomena of
which we can certainly say that they vary sympathetically with the
sun-spots. Roughly speaking, the whole history of the sun seems to be
bound up with them. Besides these dark patches which we call spots (which,
by the way, are not really dark but only less bright than the surrounding
part of the disc), there are patches brighter than the rest which have
been called faculæ. With ordinary telescopes, either visual or
photographic, these can generally only be detected near the edge of the
sun's disc; but even with this limitation it can easily be established
that the faculæ vary in number and size from year to year much in the same
way as the spots, and this conclusion is amply confirmed by the beautiful
method of observing the faculæ with the new instrument designed by
Professor Hale of the Yerkes Observatory. With this instrument, called a
spectroheliograph, it is possible to photograph the faculæ in all parts of
the sun's disc, and thus to obtain a much more complete history of them,
and there is no doubt whatever of their variation sympathetically with the
spots. Nor is there any doubt about similar variations in other parts of
the sun which we cannot see _at all_ with ordinary telescopes, except on
the occasions when the sun is totally eclipsed. Roughly speaking, these
outlying portions of the sun consist of two kinds, the chromosphere and
the corona, the former looking like an irregular close coating of the
ordinary sun, and the latter like a pearly halo of light extending to
many diameters of the sun's disc, but not with any very regular form.
[Illustration: PLATE XV. SMOOTHED SUNSPOT CURVE (WOLF) COMPARED WITH THE
NUMBER OF TURNS MADE IN EACH YEAR BY THE OSLER ANEMOMETER VANE OF THE
ROYAL OBSERVATORY, GREENWICH (THE EXCESS OF THE DIRECT TURNS (D) OVER THE
RETROGRADE TURNS (R) OR _VICE VERSA_.)
THE UPPER CURVE IS IN EACH CASE THE SUNSPOT CURVE, THE LOWER THE VANE
CURVE. THE BREAK IN 1882 IN THE VANE CURVE IS DUE TO THE OMISSION OF
EVIDENTLY ACCIDENTAL TURNS FROM THAT DATE.]
The chromosphere, from which shoot out the prominences or "red flames,"
can now be observed without an eclipse if we employ the beautiful
instrument above-mentioned, the spectroheliograph; and Professor Hale has
succeeded in photographing spots, faculæ, and prominences all on the same
plate. But although many have made the attempt (and Professor Hale,
perhaps, a more determined attempt than any man living), no one has yet
succeeded in obtaining any picture or evidence of the existence of the
corona excepting on the occasion of a total solar eclipse.
[Sidenote: Eclipses of sun.]
[Sidenote: Total eclipses rare.]
Now these occasions are very rare. There are two or three eclipses of the
sun every year, but they are generally of the kind known as partial; when
the moon does indeed come between us and the sun to some extent, but only
cuts off a portion of his light--a clean-cut black disc is seen to
encroach more or less on the surface of the sun. Most of us have had an
opportunity of seeing a partial eclipse, probably more than once; but few
have seen a total eclipse. For this the moon must come with great
exactness centrally between us and the sun; and the spot where this
condition is fulfilled completely only covers a few hundred miles of the
earth's surface at one moment. As the earth turns round, and as the moon
revolves in its orbit, this patch from which the sun is totally eclipsed
travels over the earth's surface, marking out a track some thousands of
miles in length possibly, but still not more than 200 miles wide; and in
order to see the sun totally eclipsed even on the rare occasions when it
is possible at all (for, as already remarked, in the majority of cases the
eclipse is only partial), we must occupy some station in this narrow belt
or track, which often tantalisingly passes over either the ocean or some
regions not easily accessible to civilised man. Moreover, if we travel to
such favoured spots the whole time during which the sun is totally
eclipsed cannot exceed a few minutes, and hence observations are made
under rather hurried and trying conditions. In these modern days of
photography it is easier to take advantage of these precious moments than
it used to be when there was only the eye and memory of an excited
observer to rely upon. It is perhaps not surprising that some of the
evidence collected on these earlier occasions was conflicting; but
nowadays the observers, generally speaking, direct their energies in the
first place to mounting accurately in position photographic apparatus of
different kinds, each item of it specially designed to settle some
particular problem in the most feasible way; secondly, to rehearsing very
carefully the exact programme of exposures necessary during the critical
few minutes; and finally, to securing these photographs with as few
mistakes as possible when the precious moments actually arrive. Even then
the whole of their efforts are quite likely to be rendered unavailing by a
passing cloud; and bitter is the disappointment when, after travelling
thousands of miles, and spending months in preparation, the whole
enterprise ends in nothing owing to some caprice of the weather.
[Sidenote: Corona follows spots.]
Hence it will easily be imagined that our knowledge of the corona, the
part of the sun which we can still only study on occasions of a total
solar eclipse, advances but slowly. During the last twenty years there has
been altogether scarcely half-an-hour available for this research, though
it may fairly be said that the very best possible use has been made of
that half-hour. And, what is of importance for our immediate purpose, it
has gradually been established by comparing the photographs of one eclipse
with those of another, that the corona itself undergoes distinct changes
in form in the same period which governs the changes of sun-spots. When
there are many sun-spots the corona spreads out in all directions from the
edge of the sun's disc; when there are few sun-spots the corona extends
very much further in the direction of the sun's equator, so that at
sun-spot minimum there is an appearance of two huge wings. Although the
evidence is necessarily collected in a scrappy manner, by this time there
is sufficient to remove this relationship out of the region of mere
suspicion, and to give it a well-established place in our knowledge of the
sun's surroundings.
[Sidenote: Corona may influence magnets.]
Now the corona of the sun may be compared to some rare animal which we
only see by paying a visit to some distant land, and may consider
ourselves even then fortunate to get a glimpse of; and it might be thought
that the habits of such an animal are not likely to be of any great
importance in our everyday life. But so far from this being the case in
regard to the corona, it is more than possible that the knowledge of its
changes may be of vital interest to us. I have already said that, as yet,
we have no satisfactory account of the reason why changes in sun-spots
seem to influence changes in our magnets on the earth; but one of the
theories put forward in explanation, and one by no means the least
plausible, is that this influence may come, not from the sun-spots
themselves, but from some other solar phenomenon which varies in sympathy
with them; and in particular that it may come from the corona. These wings
which reach out at sun-spot minimum can be seen to extend a considerable
distance, and there is no reason to suppose that they actually cease at
the point where they become too faint for us to detect them further; they
may extend quite as far as the earth itself and even beyond; and they may
be of such a nature as to influence our magnets. As the earth revolves
round the sun it may sometime plunge into them, to emerge later and pass
above or below them; as again the wings spread themselves at sun-spot
minimum and seem to shrink at maximum, so our magnets may respond by
sympathetic though very small vibrations. Hence it is quite possible that
the corona is directly influencing the magnetic changes on the earth.
[Sidenote: Possible importance of corona.]
But it may be urged that these changes are so slight as to be merely of
scientific interest. That may be true to-day, but who will be bold enough
to say that it will be true to-morrow? If we are thinking of practical
utility alone, we may remember that two great forces of Nature which we
have chained into the service of man, steam and electricity, put forth
originally the most feeble manifestations, which might readily have been
despised as valueless; but by careful attention to proper conditions
results of overwhelming practical importance have been obtained from these
forces, which might have been, and for many centuries were, neglected as
too trivial to be worth attention. Recently the world has been startled by
the discovery of new elements, such as radium, whose very existence was
only detected by a triumph of scientific acuteness in investigation, and
yet which promise to yield influences on our lives which may overwhelm in
importance all that has gone before. And similarly it may be that these
magnetic changes, when properly interpreted or developed, may become of an
importance in the future out of all proportion to the attention which they
have hitherto attracted. Hence, although perhaps sufficient has already
been established to show the immense consequences which flow from
Schwabe's remarkable discovery of the periodicity in solar spots, we may
be as yet only on the threshold of its real value.
From what little causes great events spring! How little can Schwabe have
realised, when he began to point his modest little telescope at the sun,
and to count the number of spots--the despised spots which he had been
assured were of no interest and exhibited no laws, and were generally
unprofitable--that he was taking the first step in the invention of the
great science of Solar Physics!--a science which is, I am glad to say,
occupying at the present moment so much of the attention, not only of the
great Yerkes Observatory, but of many other observatories scattered over
the globe.
CHAPTER VI
THE VARIATION OF LATITUDE
If we should desire to classify discoveries in order of merit, we must
undoubtedly give a high place to those which are made under direct
discouragements. In the last chapter we saw that Schwabe entered upon his
work under conditions of this kind, it being the opinion of experienced
astronomers who had looked at the facts that there was nothing of interest
to be got by watching sun-spots. In the present chapter I propose to deal
with a discovery made in the very teeth of the unanimous opinion of the
astronomical world by an American amateur, Mr. S. C. Chandler of Cambridge
(Massachusetts). It is my purpose to allow him to himself explain the
steps of this discovery by giving extracts from the magnificent series of
papers which he contributed to the _Astronomical Journal_ on the subject
in the years 1891-94, but it may help in the understanding of these
extracts if I give a brief summary of the facts. And I will first explain
what is meant by the "Variation of Latitude."
[Sidenote: Latitude.]
[Sidenote: Precession.]
We are all familiar with the existence of a certain star in the heavens
called the Pole Star, and we know that at any particular place it is seen
constantly in the north at a definite height above the horizon, which is
the latitude of the place. When watched carefully with a telescope it is
found to be not absolutely stationary, but to describe a small circle in
the heavens day by day, or rather night by night. These simple facts are
bound up with the phenomenon of the earth's rotation in this way: the axis
about which it is rotating points to the centre of that little circle, and
any change in the position of the axis can therefore be determined by
observing these motions of the Pole Star. Such changes may be of two
kinds: firstly, we might find that the size of the circle increased or
diminished, and this would mean that the earth's axis was pointing farther
away from the Pole Star or nearer to it--pointing, that is to say, in a
different direction in space. This actually happens (as has been known for
some thousands of years) owing to the phenomenon called "precession"; the
circle described by our Pole Star is at present getting a little smaller,
but it will ultimately increase in size, and after thousands of years
become so large that the Pole Star will entirely lose its character as a
steady guide to the North.
[Sidenote: Change of latitude.]
[Sidenote: Twenty years ago disbelieved.]
Secondly (and this is what more immediately concerns us), the centre of
the circle may alter its position and be no longer at the same height
above the horizon of any given place. This would mean that the earth's
axis was shifting _in the earth itself_--that the North Pole which our
explorers go to seek is not remaining in the same place. That it does not
change appreciably in position we know from familiar experience; our
climates, for instance, would suffer considerably if there were any large
changes. But astronomers are concerned with minute changes which would not
have any appreciable effect on climate, and the question has long been
before them whether, putting aside large movements, there were any minute
variations in position of the North Pole. Twenty years ago the answer to
this question would have been given decidedly in the negative; it was
considered as certain that the North Pole did not move at all within the
limits of our most refined astronomical observations. Accepted theory
seemed to indicate that any movements must in any case recur after a
period of ten months, and careful discussion of the observations showed
that there was no oscillation in such a period. Now we know that the
theory itself was wrong, or rather was founded upon a mistaken assumption;
and that the facts when properly examined show clearly a distinct movement
of the North Pole, not a very large one, for all its movements take place
within the area occupied by a moderate-sized room, but still a movement
easily measurable by astronomical observations, and Mr. Chandler was the
first to point out the law of these movements, and very possibly the first
to suspect them.
[Sidenote: Chandler's papers.]
With these few words of explanation I will let Mr. Chandler tell his own
story. His first paper appeared in the _Astronomical Journal_ in November
1891, and is courageously headed, "On the Variation of Latitude"--I say
courageously, because at that time it was believed that the latitude did
_not_ vary, and Mr. Chandler himself was only in possession of a small
portion of the facts. They unravelled themselves as he went forward; but
he felt that he had firm hold of the end of the thread, and he faced the
world confidently in that belief. He begins thus:--
[Sidenote: First signs of change.]
"In the determination of the latitude of Cambridge[5] with the
Almucantar, about six years and a half ago, it was shown that the
observed values, arranged according to nights of observation,
exhibited a decided and curious progression throughout the series,
the earlier values being small, the later ones large, and the range
from November 1884 to April 1885 being about four-tenths of a second.
There was no known or imaginable instrumental or personal cause for
this phenomenon, yet the only alternative seemed to be an inference
that the latitude had actually changed. This seemed at the time too
bold an inference to place upon record, and I therefore left the
results to speak for themselves. The subsequent continuation of the
series of observations to the end of June 1885 gave a maximum about
May 1, while the discussion of the previous observations from May to
November 1884 gave a minimum about September 1, indicating a range of
0".7 within a half-period of about seven months."
Mr. Chandler then gives some figures in support of these statements,
presenting them with the clearness which is so well marked a feature of
the whole series of papers, and concludes this introductory paper as
follows:--
"It thus appears that the apparent change in the latitude of
Cambridge is verified by this discussion of more abundant material.
The presumption that it is real, on this determination alone, would
justify further inquiry.
[Sidenote: Confirmed in Europe.]
"Curiously enough Dr. Küstner, in his determination of the
aberration from a series of observations coincident in time with
those of the Almucantar, came upon similar anomalies, and his
results, published in 1888, furnish a counterpart to those which I
had pointed out in 1885. The verification afforded by the recent
parallel determinations at Berlin, Prague, Potsdam, and Pulkowa,
which show a most surprising and satisfactory accordance, as to the
character of the change, in range and periodicity, with the
Almucantar results, has led me to make further investigations on the
subject. They seem to establish the nature of the law of those
changes, and I will proceed to present them in due order."
The second paper appeared on November 23, and opens with the following
brief statement of his general results at that time:--
[Sidenote: 427 days' period.]
"Before entering upon the details of the investigations spoken of in
the preceding number, it is convenient to say that the general result
of a preliminary discussion is to show a revolution of the earth's
pole in a period of 427 days, from west to east, with a radius of
thirty feet, measured at the earth's surface. Assuming provisionally,
for the purpose of statement, that this is a motion of the north pole
of the principal axis of inertia about that of the axis of rotation,
the direction of the former from the latter lay towards the Greenwich
meridian about the beginning of the year 1890. This, with the period
of 427 days, will serve to fix approximately the relative positions
of these axes at any other time, for any given meridian. It is not
possible at this stage of the investigation to be more precise, as
there are facts which appear to show that the rotation is not a
perfectly uniform one, but is subject to secular change, and perhaps
irregularities within brief spaces of time."
[Sidenote: Contrary to received views.]
It is almost impossible, now that we have become familiar with the ideas
conveyed in this paragraph, to understand, or even fully to remember, the
impression produced by them at the time; the sensation caused in some
quarters, and the ridicule excited in others. They were in flat
contradiction to all accepted views; and it was believed that these views
were not only theoretically sound, but had been matured by a thorough
examination of observational evidence. The only period in which the
earth's pole could revolve was believed to be ten mouths; and here was Mr.
Chandler proclaiming, apparently without any idea that he was
contradicting the laws of dynamics, that it was revolving in fourteen
months! The radius of its path had been found to be insensible by careful
discussion of observations, and now he proclaimed a sensible radius o£
thirty feet. Finally, he had the audacity to announce a _variable_ period,
to which there was nothing at all corresponding in the mathematical
possibilities. This was the bitterest pill of all. Even after Professor
Newcomb had shown us how to swallow the other two, he could not recommend
any attempt at the third, as we shall presently see; and Mr. Chandler was
fain ultimately to gild it a little before it could be gulped.
[Sidenote: Pulkowa puzzle solved, also Washington.]
But this is anticipating, and it is our intention to follow patiently the
evidence adduced in support of the above statements, made with such
splendid confidence to a totally disbelieving world. Mr. Chandler first
examines the observations of Dr. Küstner of Berlin, quoted at the end of
his last paper, and shows how well they are suited by the existence of a
variation in the latitude of 427 days; and that this new fact is
added--when the Cambridge (U.S.A.) latitudes were the smallest those of
Berlin were the largest, and _vice versâ_, as would clearly be the case if
the phenomenon was due to a motion of the earth's pole; for if it moved
nearer America it must move further from Europe. He then examines a long
series of observations made in the years 1864-1873 at Pulkowa, near St.
Petersburg, and again finds satisfactory confirmation of his law of
variation. Now it had long been known that there was something curious
about these observations, but no one could tell what it was. The key
offered by Mr. Chandler fitted the lock exactly, and the anomalies which
had been a puzzle were removed. This was in itself a great triumph; but
there was another to come, which we may let Mr. Chandler describe in his
own words:--
"In 1862 Professor Hubbard began a series of observations of [a]
Lyræ at the Washington Observatory with the prime vertical transit
instrument, for the purpose of determining the constants of
aberration and nutation and the parallax of the star. The methods of
observation and reduction were conformed to those used with such
success by W. Struve. After Hubbard's death the series was continued
by Professors Newcomb, Hall, and Harkness until the beginning of
1867. Professor Hall describes these observations as the most
accurate determinations of declination ever made at the Naval
Observatory. The probable error of a declination from a single
transit was ±0".141, and judging from the accidental errors, the
series ought to give trustworthy results. Upon reducing them,
however, it was found that some abnormal source of error existed,
which resulted in anomalous values of the aberration-constant in the
different years, and a negative parallax in all. A careful
verification of the processes of reduction failed to discover the
cause of the trouble, and Professor Hall says that the results must
stand as printed, and that probably some annual disturbance in the
observations or the instrument occurred, which will never be
explained, and which renders all deductions from them uncertain. The
trouble could not be connected with personal equation, the anomalies
remaining when the observations of the four observers who took part
were separately treated. Nor, as Professor Hall points out, will the
theoretical ten-month period in the latitude furnish the explanation.
"It is manifest, however, that if the 427-day period exists, its
effect ought to appear distinctly in declination-measurements of such
high degree of excellence as these presumably were, and, as I hope
satisfactorily to show, actually are. When this variation is taken
into account the observations will unquestionably vindicate the high
expectations entertained with regard to them by the accomplished and
skilful astronomers who designed and carried them out."
[Sidenote: Direction of revolution of Pole.]
[Sidenote: Example of results.]
From this general account I am excluding technical details and figures,
and unfortunately a great deal is thereby lost. We lose the sense of
conviction which the long rows of accordant figures force upon us, and we
lose the opportunities of admiring both the astonishing amount of work
done and the beautiful way in which the material is handled by a master.
But I am tempted to give one very small illustration of the numerical
results from near the end of the paper. After discussing the Washington
results, and amply fulfilling the promise made in the preceding extract,
Mr. Chandler compares them with the Pulkowa results, and shows that the
Earth's Pole must be revolving from west to east, and not from east to
west. And then he writes down a simple formula representing this motion,
and compares his formula with the observations. He gives the results in
seconds of arc, but for the benefit of those not familiar with
astronomical measurements we may readily convert these into feet; and in
the following tables are shown the distances of the Earth's Pole _in feet_
from its average position,[6] as observed at Washington and at Pulkowa,
and the same distances calculated according to the formula which Mr.
Chandler was able to write down at this early stage. The signs + and - of
course indicate opposite directions of displacement:--
WASHINGTON.
_Deviation of Pole._
+-------------------------------------+
| Date. | Observed.| Formula. |
|-------------------------------------|
| 1864, Dec. 28 | -28 feet | -23 feet |
| 1865, Mar. 19 | - 1 " | -12 " |
| " June 1 | +15 " | +12 " |
| " Aug. 11 | +22 " | +23 " |
| " Oct. 9 | +11 " | +15 " |
| " Dec. 13 | -17 " | - 6 " |
+-------------------------------------+
PULKOWA.
_Deviation of Pole._
+-------------------------------------+
| Date. | Observed.| Formula. |
|-------------------------------------|
| 1865, July 25 | -18 feet | -12 feet |
| " Sept. 9 | + 3 " | + 3 " |
| " Nov. 22 | +26 " | +22 " |
| 1866, Feb. 22 | +18 " | +13 " |
| " June 4 | -11 " | -18 " |
| " July 17 | -16 " | -23 " |
+-------------------------------------+
Of course the figures are not exact in every case, but they are never many
feet wrong; and it may well be imagined that it is a difficult thing to
deduce, even from the most refined observations, the position of the
earth's pole to within a foot. The difficulty is exactly the same as that
of measuring the length of an object 300 miles away to within an inch!
Mr. Chandler winds up his second paper thus:--
"We thus find that the comparison of the simultaneous series at
Pulkowa and Washington, 1863-1867, leads to the same conclusion as
that already drawn from the simultaneous series at Berlin and
Cambridge, 1884-1885. The direction of the polar motion may therefore
be looked upon as established with a large degree of probability.
"In the next paper I will present the results derived from PETERS,
STRUVE, BRADLEY, and various other series of observations, after
which the results of all will be brought to bear upon the
determination of the best numerical values of the constants
involved."
[Sidenote: Bradley's observations.]
[Sidenote: Latitude varied in twelve months then.]
The results were not, however, presented in this order. In the next paper,
which appeared on December 23, 1891, Mr. Chandler begins, with the work of
Bradley, the very series of observations at Kew and Wansted which led to
the discoveries of aberration and nutation, and which we considered in the
third chapter. He first shows that, notwithstanding the obvious accuracy
of the observations, there is some unexplained discordance. The very
constant of aberration which Bradley discovered from them differs by
half-a-second of arc from our best modern determinations. Attempts have
been made to ascribe the discordance to changes in the instrument, but Mr.
Chandler shows that such changes, setting aside the fact that Bradley
would almost certainly have discovered them, will not fit in with the
facts. The facts, when analysed with the skill to which we have become
accustomed, are that there is a periodic swing in the results _with a
period of about a year_, and not fourteen months, as before, "a result so
curious," as he admits, that "if we found no further support, it might
lead us to distrust the above reasoning, and throw us back to the
possibility that, after all, BRADLEY'S observations may have been vitiated
by some kind of annual instrumental error. But it will abundantly appear,
when I have had the opportunity to print the deductions from all the other
series of observations down to the present time, that the inference of an
increase in the period of polar revolution is firmly established by their
concurrent testimony." We shall presently return to this curious result,
which might well have dismayed a less determined researcher than Mr.
Chandler, but which only led him on to renewed exertions.
The results obtained from Bradley's observations may be put in the form
of a diagram thus:--
[Illustration: FIG. 7.]
It will be seen that the maxima and minima fall in the spring and autumn,
and this fact alone seemed to show that the effect could not be due to
temperature, for we should expect the greatest effect in that case in
winter and summer. It could not be due to the parallax of the stars for
which Bradley began his search, for stars in different quarters of the
heavens would then be differently affected, and this was not the case.
"There remains," concluded Mr. Chandler after full discussion, "the only
natural conclusion of an actual displacement of the zenith, in other
words, a change of latitude." And he concludes this paper with the
following fine passage:--
"So far, then, as the results of this incomparable series of
observations at Kew and Wansted, considered by themselves alone, can
now be stated, the period of the polar rotation at that epoch appears
to have been probably somewhat over a year, and certainly shorter by
about two months than it is at the present time. The range of the
variation was apparently in the neighbourhood of a second of arc, or
considerably larger than that shown by the best modern observations.
[Sidenote: Bradley's greatness.]
"Before taking leave of these observations for the present I cannot
forbear to speak of the profound impression which a study of them
leaves upon the mind, and the satisfaction which all astronomers must
feel in recognising that, besides its first fruits of the phenomena
of aberration and nutation, we now owe also our first knowledge of
the polar motion to this same immortal work of Bradley. Its
excellence, highly appreciated as it has been, has still been
hitherto obscured by the presence of this unsuspected phenomenon.
When divested of its effects, the wonderful accuracy of this work
must appear in a finer light, and our admiration must be raised to
higher pitch. Going back to it after one hundred and sixty years
seems indeed like advancing into an era of practical astronomy more
refined than that from which we pass. And this leads to a suggestion
worthy of serious practical consideration--whether we can do better
in the future study of the polar rotation, than again to avail
ourselves of Bradley's method, without endangering its elegant
simplicity and effectiveness by attempts at improvement, other than
supplying certain means of instrumental control which would without
doubt commend themselves to his sagacious mind.
[Sidenote: Other puzzles explained.]
"In the next article Bradley's later observations at Greenwich, the
results of which are not so distinct, will be discussed; and also
those of Brinkley at Dublin, 1808-13 and 1818-22. This will bring
again to the surface one of the most interesting episodes in
astronomical history, the spirited and almost acrimonious dispute
between Brinkley and Pond with regard to stellar parallaxes. I hope
to show that the hitherto unsolved enigma of Brinkley's singular
results finds its easy solution in the fact of the polar motion. The
period of his epoch appears to have been about a year, and its range
more than a second. Afterwards will follow various discussions
already more or less advanced towards completion. These include
Bessel's observations at Königsberg, 1820-24, with the Reichenbach
circle, and in 1842-44 with the Repsold circle; the latitudes derived
from the polar-point determinations of Struve and Mädler with the
Dorpat circle, 1822-38; Struve's observations for the determination
of the aberration; Peters' observations of _Polaris_, 1841-43, with
the vertical-circle; the results obtained from the reflex zenith-tube
at Greenwich, 1837-75, whose singular anomalies can be referred in
large part to our present phenomenon, complicated with instrumental
error, to which until now they have been exclusively attributed; the
Greenwich transit-circle results, 1851-65, in which case, however, a
similar complication and the large accidental errors of observation
seem to frustrate efforts to get any pertinent results; the Berlin
prime-vertical observations of Weyer and Brünnow, 1845-46, in which I
hope to show that the parallax of [beta] _Draconis_ derived from them
is simply a record of the change of latitude; the conflicting
latitude determinations at Cambridge, England; the Washington
observation of _Polaris_ and other close Polars, 1866-87, with the
transit-circle; also those at Melbourne, 1863-84, a portion of which
have already been drawn upon in the last number of the _Journal_,
and some others. While the list is a considerable one, I shall be
able to compress the statement of results for many of the series into
a short space.
[Sidenote: Provisional nature of results.]
"In connection with this synopsis of the scope of the investigations,
one or two particulars may be of interest, which at the present
writing seem to foreshadow the probable outcome. I beg, however, that
the statement will be regarded merely as a provisional one. First,
while the period is manifestly subject to change, as has already once
or twice been intimated, I have hitherto failed in tracing the
variations to any regular law, expressible in a numerical formula.
Indeed, the general impression produced by a study of these changes
in the length of the period is that the cause which produces them
operates capriciously to a certain degree, although the average
effect for a century has been to diminish the velocity of the
revolution of the pole. How far this impression is due to the
uncertainty of the observations, and to the complication of the
phenomenon with other periodical changes of a purely instrumental
kind, I cannot say. Almost all of the series of any extent which have
been examined, have the peculiarity that they manifest the
periodicity quite uniformly and distinctly for a number of years,
then for a while obscurely. In some cases, however, what at first
appears to be an objective irregularity proves not to be so by
comparison with overlapping series at other observatories.
"Another characteristic which has struck my attention, although
somewhat vaguely, is that the variations in the length of the period
seem to go hand in hand with simultaneous alterations in the
amplitude of the rotation; the shorter periods being apparently
associated with the larger coefficients for the latter. The
verification of these surmises awaits a closer comparative scrutiny,
the opportunity for which will come when the computations are in a
more forward state. If confirmed, these observations will afford a
valuable touchstone, in seeking for the cause of a phenomenon which
now seems to be at variance with the accepted laws of terrestrial
rotation."
[Sidenote: Reception of discovery.]
Let us now for a few moments turn aside from the actual research to see
how the announcement was received. It would be ungracious to reprint here
any of the early statements of incredulity which found their way into
print, especially in Germany. But the first note of welcome came from
Simon Newcomb, in the same number of the _Astronomical Journal_ as the
paper just dealt with, and the following extract will indicate both the
difficulties felt in receiving Mr. Chandler's results and the way in which
Newcomb struck at the root of them.
[Sidenote: Newcomb's explanation.]
"Mr. Chandler's remarkable discovery, that the apparent variations in
terrestrial latitudes may be accounted for by supposing a revolution
of the axis of rotation of the earth around that of figure, in a
period of 427 days, is in such disaccord with the received theory of
the earth's rotation that at first I was disposed to doubt its
possibility. But I am now able to point out a _vera causa_ which
affords a complete explanation of this period. Up to the present time
the treatment of this subject has been this: The ratio of the moment
of inertia of the earth around its principal axis to the mean of the
other two principal moments, admits of very accurate determination
from the amount of precession and nutation. This ratio involves what
we might call, in a general way, the solid ellipticity of the earth,
or the ellipticity of a homogeneous spheroid having the same moments
of inertia as the earth.
"When the differential equations of the earth's rotation are
integrated, there appear two arbitrary constants, representing the
position of any assigned epoch of the axis of rotation relative to
that of figure. Theory then shows that the axis of rotation will
revolve round that of figure, in a period of 306 days, and in a
direction from west toward east. The attempts to determine the value
of these constants have seemed to show that both are zero, or that
the axes of rotation and figure are coincident. Several years since,
Sir William Thomson published the result of a brief computation from
the Washington Prime-Vertical observations of [alpha] Lyrae which I
made at his request and which showed a coefficient 0".05. This
coefficient did not exceed the possible error of the result; I
therefore regarded it as unreal.
[Sidenote: The forgotten assumption.]
"The question now arises whether Mr. Chandler's result can be
reconciled with dynamic theory. I answer that it can, because the
theory which assigns 306 days as the time of revolution is based on
the hypothesis that the earth is an absolutely rigid body. But, as a
matter of fact, the fluidity of the ocean plays an important part in
the phenomenon, as does also the elasticity of the earth. The
combined effect of this fluidity and elasticity is that if the axis
of rotation is displaced by a certain amount, the axis of figure
will, by the changed action of the centrifugal force, be moved
toward coincidence with the new axis of rotation. The result is, that
the motion of the latter will be diminished in a corresponding ratio,
and thus the time of revolution will be lengthened. An exact
computation of the effect is not possible without a knowledge of the
earth's modulus of elasticity. But I think the result of
investigation will be that the rigidity derived from Mr. Chandler's
period is as great as that claimed by Sir William Thomson from the
phenomena of the tides."
[Sidenote: But Chandler's work still mistrusted.]
This was very satisfactory. Professor Newcomb put his finger on the
assumption which had been made so long ago that it had been forgotten: and
the lesson is well worth taking to heart, for it is not the first time
that mistaken confidence in a supposed fact has been traced to some
forgotten preliminary assumption: and we must be ever ready to cast our
eyes backward over all our assumptions, when some new fact seems to
challenge our conclusions. It might further be expected that this
discovery of the way in which theory had been defective would as a
secondary consequence inspire confidence in the other conclusions which
Mr. Chandler had arrived at in apparent contradiction to theory; or at
least suggest the suspension of judgment. But Professor Newcomb did not
feel that this was possible in respect of the _change_ of period, from
about twelve months in Bradley's time to fourteen months in ours. We have
seen that Mr. Chandler himself regarded this as a "curious result"
requiring confirmation: but since the confirmation was forthcoming, he
stated it with full confidence, and drew the following remarks from
Professor Newcomb in July 22, 1892:--
"The fact of a periodic variation of terrestrial latitudes, and the
general law of that variation, have been established beyond
reasonable doubt by the observations collected by Mr. Chandler. But
two of his minor conclusions, as enumerated in No. 3 of this volume,
do not seem to me well founded. They are--
"1. That the period of the inequality is a variable quantity.
"2. That the amplitude of the inequality has remained constant for
the last half century."
Professor Newcomb proceeds to give his reasons for scepticism, which are
too technical in character to reproduce here. But I will quote the
following further sentence from his paper:--
"The question now arises how far we are entitled to assume that the
period must be invariable. I reply that, perturbations aside, any
variation of the period is in such direct conflict with the laws of
dynamics that we are entitled to pronounce it impossible. But we know
that there are perturbations, and I do not see how one can doubt
that they have so acted as to increase the amplitude of the variation
since 1840."
[Sidenote: Chandler's reply.]
In other words, while recognising that there may be a way of reconciling
one of the "minor" conclusions with theory, Professor Newcomb considers
that in this case the other must go. Mr. Chandler's answer will speak for
itself. It was delayed a little in order that he might present an immense
mass of evidence in support of his conclusions, and was ultimately printed
on August 23, 1892.
"The material utilised in the foregoing forty-five series aggregates
more than thirty-three thousand observations. Of these more than
one-third were made in the southern hemisphere, a fact which we owe
principally to Cordoba. It comprises the work of seventeen
observatories (four of them in the southern hemisphere) with
twenty-one different instruments, and by nine distinct methods of
observation. Only three of the series (XXI., XXV., and XXXV.), and
these among the least precise intrinsically, give results
contradictory of the general law developed in No. 267. This degree of
general harmony is indeed surprising when the evanescent character of
the phenomenon under investigation is considered.
"The reader has now before him the means for independent scrutiny of
the material on which the conclusions already drawn, and those which
are to follow, are based. The space taken in the printing may seem
unconscionable, but I hope this will be charged to the extent of the
evidence collected, and not to diffuseness or the presentation of
needless detail; for I have studiously sought to compress the form of
statement without omitting anything essential for searching
criticism. That it was important to do this is manifest, since the
conclusions, if established, overthrow the existing theory of the
earth's rotation, as I have pointed out on p. 21. I am neither
surprised nor disconcerted, therefore, that Professor Newcomb should
hesitate to accept some of these conclusions on the ground (_A. J._,
No. 271) that they are in such conflict with the laws of dynamics
that we are entitled to pronounce them impossible. He has been so
considerate and courteous in his treatment of my work thus far, that
I am sure he will not deem presumptuous the following argument in
rebuttal.
[Sidenote: He "put aside all teachings of theory," and "is not
dismayed."]
"It should be said, first, that in beginning these investigations
last year, I deliberately put aside all teachings of theory, because
it seemed to me high time that the facts should be examined by a
purely inductive process; that the nugatory results of all attempts
to detect the existence of the Eulerian period probably arose from a
defect of the theory itself; and that the entangled condition of the
whole subject required that it should be examined afresh by processes
unfettered by any preconceived notions whatever. The problem which I
therefore proposed to myself was to see whether it would not be
possible to lay the numerous ghosts--in the shape of numerous
discordant residual phenomena pertaining to determinations of
aberration, parallaxes, latitudes, and the like--which had heretofore
flitted elusively about the astronomy of precision during the
century; or to reduce them to tangible form by some simple consistent
hypothesis. It was thought that if this could be done, a study of the
nature of the forces, as thus indicated, by which the earth's
rotation is influenced, might lead to a physical explanation of them.
"Naturally, then, I am not much dismayed by the argument of conflict
with dynamic laws, since all that such a phrase means must refer
merely to the existent state of the theory at any given time. When
the 427-day period was propounded, it was as inconsistent with known
dynamic law as the variation of it now appears to be. Professor
Newcomb's own happy explanation has already set aside the first
difficulty, as it would appear, and advanced the theory by an
important step. Are we so sure yet of a complete knowledge of all the
forces at work as to exclude the chance of a _vera causa_ for the
second?"
[Sidenote: Faraday's words.]
There is a splendid ring of resolution about these words. Let us compare
them with a notable utterance of Faraday:--
"The philosopher should be a man willing to listen to every
suggestion, but determined to judge for himself. He should not be
biassed by appearances; have no favourite hypothesis; be of no
school; and in doctrine have no master. He should not be a respecter
of persons, but of things. Truth should be his primary object. If to
these qualities be added industry, he may indeed hope to walk within
the veil of the temple of Nature."
[Sidenote: Chandler's other work at this time.]
[Sidenote: His ultimate satisfactory solution.]
[Sidenote: Interference of two waves.]
Tested by this severe standard, Mr. Chandler fails in no particular, least
of all in that of industry. The amount of work he got through about this
time was enormous, for besides the main line of investigation, of which we
have only had after all a mere glimpse, he had been able to turn aside to
discuss a subsidiary question with Professor Comstock; he had examined
with great care some puzzling characteristics in the variability of stars;
he computed some comet ephemerides; and he was preparing a new catalogue
of variable stars--a piece of work involving the collection and
arrangement of great masses of miscellaneous material. Yet within a few
months after replying as above to Professor Newcomb's criticism, he was
able to announce that he had found the key to the new puzzle, and that
"theory and observation were again brought into complete accord." We will
as before listen to the account of this new step in his own words, but a
slight preliminary explanation may help those unaccustomed to the
terminology. The polar motion was found to be compounded of _two_
independent motions, both periodic, but having different periods. Now, the
general results of such a composition are well known in several different
branches of physics, especially in the theory of sound. If two notes of
nearly the same pitch be struck at the same time, we hear the resultant
sound alternately swell and die away, because the vibrations caused by the
two notes are sometimes going in the same direction, and after an interval
are going exactly in opposite directions. Diagrammatically we should
represent the vibrations by two waves, as below; the upper wave goes
through its period seven and a half times between A and D, the lower only
six times; and it is easily seen that at A and C the waves are
sympathetic, at B and D antipathetic. At A and C the compound vibration
would be doubled; at B and D reduced to insensibility. The point is so
important that perhaps a numerical illustration of it will not be
superfluous. The waves are now represented by rows of figures as below.
The first series recurs after every 6, the second after every 7.
[Illustration: FIG. 8.]
First Wave 1 2 3 4 3 2 1 2 3 4 3 2 1 2 3 4 3 2 1 2 3 4 3 2 1 2 3 4 3 2 1
Second Wave 1 2 3 4 4 3 2 1 2 3 4 4 3 2 1 2 3 4 4 3 2 1 2 3 4 4 3 2 1 2 3
-------------------------------------------------------------
Combined Effect 2 4 6 8 7 5 3 3 5 7 7 6 4 4 4 6 6 6 5 5 5 5 5 5 5 6 6 6 4 4 4
Great disturbance. Calm.
-----------------------------------------------------------------------------
First Wave 2 3 4 3 2 1 2 3 4 3 2 1 2 3 4 3 2 1 2 3 4 3 2 1 2 3 4 3 2 1 2
Second Wave 4 4 3 2 1 2 3 4 4 3 2 1 2 3 4 4 3 2 1 2 3 4 4 3 2 1 2 3 4 4 3
-------------------------------------------------------------
Combined Effect 6 7 7 5 3 3 5 7 8 6 4 2 4 6 8 7 5 3 3 5 7 7 6 4 4 4 6 6 6 5 5
Great disturbance.
[Sidenote: Illustration from ocean travel.]
Adding the two rows together, the oscillations at first reinforce one
another and we get numbers ranging from 2 to 8 instead of from 1 to 4; but
one wave gains on the other, until it is rising when the other is falling,
and the numbers add up to a steady series of 5's. It will be seen that
there are no less than seven consecutive 5's, and all the variation seems
to have disappeared. But presently the waves separate again, and the
period of great disturbance recurs; it will be seen that in the "combined
effect" the numbers repeat exactly after the 42nd term. Now those
unfamiliar with the subject may not be prepared for the addition of one
physical wave to another, as though they were numbers, but the analogy is
perfect. Travellers by some of the fast twin-screw steamers have had
unpleasant occasion to notice this phenomenon, when the engineer does not
run the two screws precisely at the same speed; there come times when the
ship vibrates violently, separated by periods of comparative stillness.
Instances from other walks of life may recur to the memory when once
attention is called to the general facts; but enough has been said to
explain the point numbered (2) in the subjoined statement. To understand
the rest, we must remember that if the two waves are not equal in
"amplitude," _i.e._ if the backward and forward motion is not the same in
both, they cannot annul one another, but the greater will always
predominate. Those interested in following the matter further should have
no difficulty in constructing simple examples to illustrate such points.
We will proceed to give Mr. Chandler's statements:--
[Sidenote: Chandler's final formulæ.]
"We now come upon a new line of investigation. Heretofore, as has
been seen, the method has been to condense the results of each series
of observations into the interval comprised by a single period, then
to determine the mean epoch of minimum and the mean range for each
series, and, finally, by a discussion of these quantities, to
establish the general character of the law of the rotation of the
pole. It is now requisite to analyse the observations in a different
way, and discover whether the deviations from the general provisional
law, in the last column of Table II., are real, and also in what
manner the variation of the period is brought about. The outcome of
this discussion, which is to be presented in the present paper, is
extremely satisfactory. The real nature of the phenomenon is most
distinctly revealed, and may be described as follows:--
"1. The observed variation of the latitude is the resultant curve
arising from two periodic fluctuations superposed upon each other.
The first of these, and in general the more considerable, has a
period of about 427 days, and a semi-amplitude of about 0".12. The
second has an annual period with a range variable between 0".04 and
0".20 during the last half-century. During the middle portion of this
interval, roughly characterised as between 1860 and 1880, the value
represented by the lower limit has prevailed, but before and after
those dates, the higher one. The minimum and maximum of this annual
component of the variation occur at the meridian of Greenwich, about
ten days before the vernal and autumnal equinoxes respectively, and
it becomes zero just before the solstices.
"2. As the resultant of these two motions, the effective variation of
the latitude is subject to a systematic alternation in a cycle of
seven years' duration, resulting from the commensurability of the two
terms. According as they conspire or interfere, the total range
varies between two-thirds of a second as a maximum, to but a few
hundredths of a second, generally speaking, as a minimum.
"3. In consequence of the variability of the coefficient of the
annual term above mentioned, the apparent average period between 1840
and 1855 approximated to 380 or 390 days; widely fluctuated from
1855 to 1865; from 1865 to about 1885 was very nearly 427 days, with
minor fluctuations; afterwards increased to near 440 days, and very
recently fell to somewhat below 400 days. The general course of these
fluctuations is quite faithfully represented by the law of eq. (3),
(No. 267), and accurately, even down to the minor oscillations of
individual periods, by the law of eq. (15), hereafter given, and
verbally interpreted above. This law also gives a similarly accurate
account of the corresponding oscillations in the amplitude. The
closeness of the accordance between observation and the numerical
theory, in both particulars, places the reality of the law beyond
reasonable doubt."
Those who cannot follow the details of the above statement will
nevertheless catch the general purport--that the difficulties felt by
Professor Newcomb have been surmounted; and this is made clearer by a
later extract:--
"A very important conclusion necessarily follows from the agreement
of the values of the 427-day term, deduced from the intervals between
the consecutive values of T in Table XII., namely, that there has
been no discontinuity in the revolution, such as Professor Newcomb
regarded as so probable that he doubted the possibility of drawing
any conclusions from the comparison of observations before and after
1860 (_A. J._, 271, p. 50).
[Sidenote: Theory must go, if it will not fit observation.]
"The present investigation demonstrates that the way out of the
apparently irreconcilable contradiction of theory and observation in
this matter does not lie in the direction of discrediting the
observations, as he is inclined to do. On the contrary, the result is
a beautiful vindication of the trustworthiness of the latter, and, at
the same time, of the theory that demands an invariable rate of
motion; providing a perfectly fitting key to the riddle by showing
that another cause has intervened to produce the variability of the
period. I feel confident that Professor Newcomb will agree with the
reality of the explanation here set forth, and will reconsider his
view that the perturbations in the position of the Pole must be of
the nature of chance accumulations of motion, a view which he then
considered necessary to the maintenance of the constancy in the
period of latitude-variation."
[Sidenote: The final paper.]
The paper from which these words are taken appeared on November 4, 1892.
The next paper on the main theme did not appear till a year later, though
much work was being done in the meantime on the constant of aberration and
other matters arising immediately after the discovery. On November 14,
1893, Mr. Chandler winds up the series of eight papers "On the Variation
of Latitude," which he had commenced just two years before. His work was
by no means done; rather was it only beginning, for the torch he had lit
illuminated many dark corners. But he rightly regarded his discovery as
now so firmly established that the series of papers dealing with it as
still under consideration might be terminated. In this final paper he
first devotes the most careful attention to one point of detail. He had
shown earlier in the series that the North Pole must be revolving from
West to East, and not from East to West; but this was when the motion was
supposed to be simple and not complex, and it was necessary to re-examine
the question of direction for each of the components. After establishing
conclusively that the original direction holds for each of the components,
he almost apologises for the trouble he has taken, thus:--
"It is therefore proved beyond reasonable doubt that the directions
of the rotations is from West to East in both elements; whence the
general form of the equation for the variation of latitude adopted in
_A. J._, 284, p. 154, eq. (19). It may be thought that too much pains
have been here bestowed upon a point which might be trusted to theory
to decide. I cannot think so. One of the most salient results of
these articles has been the proof of the fact that theory has been a
blind guide with regard to the velocity of the Polar rotation,
obscuring truth and misleading investigators for a half a century.
And even if we were certain, which we are not, that the fourteen
months' term is the Eulerian period in a modified form. It would
still be necessary to settle by observation the direction of the
annual motion, with regard to which theory is powerless to inform us.
To save repetition of argument, I must refer to the statement in _A.
J._, 273, pp. 68, 70, of the principles adopted in beginning these
inquiries in 1891."
Finally, he answers one of the few objectors of eminence who still
lingered, the great French physicist Cornu:--
[Sidenote: Cornu answered.]
"The ground is now cleared for examination of the only topic
remaining to be covered, to establish, upon the foundation of fact,
every point in the present theory of these remarkable movements of
the earth's axis. This is the question of the possibility that these
movements are not real, but merely misinterpretations of the observed
phenomena; being in whole or in part an illusory effect of
instrumental error due to the influence of temperature. Such a
possibility has been a nightmare in practical astronomy from the
first, frightening us in every series of unexplained residuals,
brought to light continually in nearly all attempts at delicate
instrumental research. A source of danger so subtile could not fail
to be ever present in the mind of every astronomer and physicist who
has given even a superficial attention to the question of the
latitude variations, and there is no doubt that some are even now
thus deterred from accepting these variations as proved facts.
Perhaps the most explicit and forcible statement of the doubts that
may arise on this subject has been given very recently by Mr. Cornu.
The views of so distinguished a physicist, and of others who are
inclined to agree with him, call for careful attention, and cannot be
neglected in the present closing argument upon the theory presented
in these articles. It is unnecessary, for the purpose of disposing of
objections of the sort raised by Cornu, to insist that it is not
sufficient to show that the observed variations, attributed to the
unsteadiness of the Earth's Pole, are near the limit of precision
attainable in linear differential measures, and in the indication of
the direction of gravity by means of the air bubble of the level; or
to show that there are known variations in divided circles and in
levels, dependent on temperature and seasons. Nor need we require of
objectors the difficult, although essential, task--which they have
not distinctly attempted--of showing that these errors are not
eliminated, as they appear to be, by the modes in which astronomers
use their instruments. Neither need we even urge the fact that a
large portion of the data which have been utilised in the present
researches on the latitude were derived by methods which dispense
with levels, or with circles, a part of them indeed with both, and
yet that the results of all are harmonious. On the contrary, let us
admit, although merely for argument's sake, that all the known means
of determining the direction of gravity--including the plumb-line,
the level, and a fluid at rest, whether used for a reflecting surface
or as a support for a floating instrument--are subject to a common
law of periodical error which vitiates the result of astronomical
observation, obtained by whatever methods, and in precisely the same
manner. Now, the observed law of latitude variation includes two
terms, with periods of fourteen and twelve months respectively. Since
the phases of the first term are repeated at intervals of two months
in successive years, and hence in a series of years come into all
possible relations to conditions of temperature dependent on season,
the argument against the reality of this term, on this ground,
absolutely fails, and needs no further notice. As to the second, or
annual term, while the phases, as observed in any given longitude,
are indeed synchronical with the seasons, they are not so as regards
different longitudes. If, therefore, the times of any given phase, as
observed in the same latitude, but in successively increasing
longitudes, occurred at the same date in all of them, there would be
a fatal presumption against the existence of an annual period in the
polar motion. If, on the contrary, they occur at times successively
corresponding to the differences of longitude, the presumption is
equally fatal to the hypothesis that they can possibly be due to
temperature variation as affecting instrumental measurement. But the
facts given in the foregoing section correspond most distinctly to
the latter condition. Therefore, unless additional facts can be
brought to disprove successively these observed results, we may
dismiss for ever the bugbear which has undoubtedly led many to
distrust the reality of the annual component of the
latitude-variation, while they admit the existence of the 427-day
term."
[Sidenote: Consequences of the discovery.]
[Sidenote: Suspected observers acquitted.]
At this point we must leave the fascinating account of the manner in which
this great discovery was established, in the teeth of opposition such as
might have dismayed and dissuaded a less clear-sighted or courageous man.
It is my purpose to lay more stress upon the method of making the
discovery than upon its results; but we may afford a brief glance at some
of the consequences which have already begun to flow from this step in
advance. Some of them have indeed already come before us, especially that
large class represented by the explanation of anomalies in series of
observations which had been put aside as inexplicable. We have seen how
the observations made in Russia, or in Washington, or at Greenwich, in all
of which there was some puzzling error, were immediately straightened out
when Chandler applied his new rule to them. We in England have special
cause to be grateful to Chandler; not only has he demonstrated more
clearly than ever the greatness of Bradley, but he has rehabilitated Pond,
the Astronomer Royal of the beginning of the nineteenth century; showing
that his observations, which had been condemned as in some way erroneous,
were really far more accurate than might have been expected; and further
he has shown that the beautiful instrument designed by Airy, and called
the Reflex Zenith Tube, which seemed to have unaccountably failed in the
purpose for which it was designed, was really all the time accumulating
observations of this new phenomenon, the Variation of Latitude. Instead of
Airy having failed in his design, he had in Chandler's words "builded
better than he knew."
[Sidenote: Constant of Aberration improved.]
Secondly, there is the modifying influence of this new phenomenon on other
phenomena already known, such, for instance, as that of "aberration." We
saw in the third chapter how Bradley discovered this effect of the
velocity of light, and how the measure of it is obtained by comparing the
velocity of light with that of the earth. This comparison can be effected
in a variety of ways, and we should expect all the results to agree within
certain limits; but this agreement was not obtained, and Chandler has been
able to show one reason why, and to remove some of the more troublesome
differences. It is impossible to give here an idea of the far-reaching
consequences which such work as this may have; so long as there are
differences of this kind we cannot trust any part of the chain of
evidence, and there is in prospect the enormous labour of examining each
separate link until the error is found. The velocity of light, for
instance, may be measured by a terrestrial experiment; was there anything
wrong in the apparatus? The velocity of the earth in its journey round the
sun depends directly upon the distance of the sun: have we measured this
distance wrongly, and if so what was the error in the observations made?
These are some of the questions which may arise so long as the values for
the _Constant of Aberration_ are still conflicting; but it requires
considerable knowledge of astronomy to appreciate them fully.
[Sidenote: Latitude Variation Tide.]
[Sidenote: Earthquakes.]
Another example will, perhaps, be of more general interest. If the axis of
the earth is executing small oscillations of this kind, there should be an
effect upon the tides; the liquid ocean should feel the wobble of the
earth's axis in some way; and an examination of tidal registers showed
that there was in fact a distinct effect. It may cause some amusement when
I say that the rise and fall are only a few inches in any case; but they
are unmistakable evidences that the earth is not spinning smoothly, but
has this kind of unbalanced vibration, which I have compared to the
vibrations felt by passengers on an imperfectly engineered twin-screw
steamer. A more sensational effect is that apparently earthquakes are more
numerous at the time when the vibration is greatest. We remarked that the
vibration waxes and wanes, much as that of the steamer waxes and wanes if
the twin-screws are not running quite together. Now the passengers on the
steamer would be prepared to find that breakages would be more numerous
during the times of vigorous oscillation; and it seems probable that in a
similar way the little cracks of the earth's skin which we call great
earthquakes are more numerous when these unbalanced vibrations are at
their maximum; that is to say, about once every seven years. This result
is scarcely yet worthy of complete confidence, for our observations of
earthquakes have only very recently been reduced to proper order; but if
it should turn out to be true, it is scarcely necessary to add any words
of mine to demonstrate the importance of this rather unexpected result of
the Latitude Variation.
[Sidenote: The Kimura phenomenon.]
Finally I will mention another phenomenon which seems to be at present
more of a curiosity than anything else, but which may lead to some future
great discovery. It is the outcome of observations which have been
recently made to watch these motions of the Pole; for although there seems
good reason to accept Mr. Chandler's laws of variation as accurate, it is
necessary to establish their accuracy and complete the details by making
observations for some time yet to come; and there could be no better proof
of this necessity than the discovery recently made by Mr. Kimura, one of
those engaged in this watch of the Pole in Japan. Perhaps I can give the
best idea of it by mentioning one possible explanation, which, however, I
must caution you may not be by any means the right one. We are accustomed
to think of this great earth as being sufficiently constant in shape; if
asked, for instance, whether its centre of gravity remains constantly in
the same place inside it, we should almost certainly answer in the
affirmative, just as only twenty years ago we thought that the North Pole
remained in the same place. But it seems possible that the centre of
gravity moves a few feet backwards and forwards each year--this would at
any rate explain certain curious features in the observations to which Mr.
Kimura has drawn attention. Whatever the explanation of them may be, or to
settle whether this explanation is correct, we want more observations,
especially observations in the Southern Hemisphere; and it is a project
under consideration by astronomers at the present moment whether three
stations can be established in the Southern Hemisphere for the further
observation of this curious phenomenon. The question resolves itself
chiefly into a question of money; indeed, most astronomical projects do
ultimately resolve themselves into questions of money; and I fear the
world looks upon scientific men as insatiable in this respect. One can
only hope that on the whole the money is expended so as to give a
satisfactory return. In this instance I have no hesitation in saying that
an immediate return of value for a comparatively modest expenditure is
practically certain, if only in some way we can get the means of making
the observations.
It would be natural, at the conclusion of this brief review of some types
of astronomical discovery, to summarise the lessons indicated: but there
is the important difficulty that there appear to be none. It has been
pointed out as we proceeded that what seemed to be a safe deduction from
one piece of history has been flatly contradicted by another; no sooner
have we learnt that important results may be obtained by pursuing steadily
a line of work in spite of the fact that it seems to have become tedious
and unprofitable (as in the search for minor planets) than we are
confronted with the possibility that by such simple devotion to the day's
work we may be losing a great opportunity, as Challis did. We can scarcely
go wrong in following up the study of residual phenomena in the wake of
Bradley; but there is the important difficulty that we may be wholly
unable to find a clue for the arrangement of our residuals, as is at
present largely the case in meteorology. And, in general, human
expectations are likely to be quite misleading, as has been shown in the
last two chapters; the discoveries we desire may lie in the direction
precisely opposite to that indicated by the best opinion at present
available. There is no royal road to discovery, and though this statement
may meet with such ready acceptance that it seems scarcely worth making,
it is hoped that there may be sufficient of interest in the illustrations
of its truth.
The one positive conclusion which we may derive from the examples studied
is that discoveries are seldom made without both hard work and conspicuous
ability. A new planet, even as large as Uranus, does not reveal itself to
a passive observer: thirteen times it may appear to such a one without
fear of detection, until at last it encounters an alert Herschel, who
suspects, tests, and verifies, and even then announces a comet--so little
did he realise the whole truth. Fifteen years of unrequited labour before
Astræa was found, nineteen years of observation before the discovery of
nutation could be announced: how seldom do these years of toil present
themselves to our imaginations when we glibly say that "Bradley discovered
nutation," or "Hencke discovered Astræa"! That the necessary labour is so
often forgotten must be my excuse for recalling attention to it somewhat
persistently in these examples.
But beyond the fact that he must work hard, it would seem as though there
were little of value to tell the would-be discoverer. The situation has
been well summarised by Jevons in his chapter on Induction in the
"Principles of Science;" and his words will form a fitting conclusion to
these chapters:--
"It would seem as if the mind of the great discoverer must combine
contradictory attributes. He must be fertile in theories and
hypotheses, and yet full of facts and precise results of experience.
He must entertain the feeblest analogies, and the merest guesses at
truth, and yet he must hold them as worthless till they are verified
in experiment. When there are any grounds of probability he must hold
tenaciously to an old opinion, and yet he must be prepared at any
moment to relinquish it when a clearly contradictory fact is
encountered."
INDEX
Aberration, 105-109, 111, 112, 117, 118, 185, 188, 192, 214, 215
Accidental discovery, 15, 73, 121-154
Adams, 12, 45-85;
resolution, 55
Airy, 32, 40-85, 214
Algiers, 130
Alleghenia, 26
Almucantar, 180, 181
Alphabet used for planets, 27
Anderson, Dr. T. C., 8, 142, 143, 144, 146
Anthelm, 142
Apollo, 9
Argon, 109
Ascension, 34
Assumption, forgotten, 196
Astræa, 22, 23, 219
Astrographic chart, 122, 125, 130
_Astronomical Journal_, 177-217
_Astronomische Nachrichten_, 52, 158
Astrophil, 143
Auwers, 142
Ball, Sir R., 24
Balliol College, 87
Banks, Sir J., 9
Barnard, E. E., 146, 220
Berlin, 181, 183, 184, 188, 193
Berlin star-map, 45, 66, 83, 124
Bessel, 192
Bettina, 26, 27
Birmingham, 142
"Black Drop" (in transit of Venus), 30
Bliss, 114
Board of Visitors of Greenwich Observatory, 63
Bode, 11, 14, 15, 22
Bode's Law, 12, 13, 38, 43, 45, 52, 72, 76, 77, 84
Bourdeaux, 130
Bouvard, 39, 40, 42, 48, 49, 50, 61
Bradley, 39, 86-120, 188-192, 213, 214, 218, 219
Bradley, John, 115
Bremen, 20
Bridstow, 87, 88, 94
Briggs, 119
Brinkley, 192
British Association, 63
Brünnow, 193
California, 26
Cambridge (Mass.), 180, 184, 188
Cambridge Observatory, 23, 42, 49, 52, 63, 65, 66, 135, 193
Cambridge University, 68-71, 114
Cape Observatory, 123, 124, 130
Cards, 11
Cassini II., 156
Catania, 130
Ceres, 14-22
Chacornac, 124
Challis, 49-54, 63-68, 71, 85, 218
Chandler, S. C., 118, 177-217
Chapman's "Homer," 2
Chicago, 157
Chromosphere, 170
Clarke, C. C., 2
Coelostat, 94
Columbus, 63
Comet, 4-8, 88, 108, 117, 123, 125
Commission, planetary, 27
Common, A. A., 124, 127
_Compte Rendu_, 62
Comstock, 202
Conference, Astrographic, 125-136
Copernicus, 79, 95
Cordoba, 130, 199
Cornu, 210-213
Corona, 170-175
_Cosmos_ (Humboldt's), 160
Delambre, 157
Deviation of Pole, 187
Disc of Neptune, 44, 64, 79
Disc of Uranus, 4-7
Dorpat, 192
Doublet (photographic), 127-129
Draconis, [gamma], 96-104
Draconis, [beta], 193
Driessen, 23
Dry plate, 122
Dublin, 192
Earthquakes, 215
Earth's Pole, 177-217
Eccentricity, 41, 83
Eclipses, 170-176
Edinburgh, 143
Eduarda, 26
Egeria, 22
Endymion, 25
Eriphyla, 26
Eros, 25, 26, 28, 35, 37, 68
Eulerian, 200, 209
Evelyn, 26
Exposure, times of, 122, 131
Faculæ, 170
Faraday, 201
Flamsteed, 39, 53, 115
Fleming, Mrs., 142
Flora, 22
Foulkes, Martin, 94
French Academy, 43, 51, 62
Galileo, 95, 163
Galle, 44, 45, 47, 66, 67, 83
Gasparis, 22
Gauge (railways), 56
Gauss, 17-20
Geminorum, H., 4
George III., 8, 10
"Georgian," 11
_Georgium Sidus_, 8, 10, 11
Gill, Sir D., 32, 34, 35, 123
Gilliss, 32
Gotha, 20
Gould, 32
Graham, 22, 23
Gravitation, law of, 38, 45, 59, 84, 105
Greaves, 119
Greenwich Observatory, 48-64, 88, 89, 114-117, 130, 160-169,
182, 192, 193, 206, 213
Gregory, 93, 119
Hale, G. E., 170, 171
Hall, A., 184, 185
Halley, 88-92, 108, 112-116, 119
Hansen, 41, 59
Harkness, 184
Hartwig, 142
Harvard College Observatory, 128, 142, 144, 145
Hebe, 22
Hegel, 15
Heidelberg, 145
Heliometer, 32, 34
Helium, 109
Helsingfors, 130
Hencke, 22, 23, 64, 153, 219
Henry brothers, 124-129
Herschel, Sir John, 63, 75, 83
Herschel, Sir William, 2-11, 39, 44, 82, 219
Herschel (Uranus), 11, 12
Hind, 22, 23, 25, 142
Hooke, 96, 97
Hubbard, 184
Humboldt, 160
Hussey, Rev. T. J., 40, 42
Hygeia, 22
Ilmata, 26
Industria, 26
Ingeborg, 26
Instruments at Greenwich, 114-116
Iris, 22, 23, 32, 35
Janson, 142
Jevons, 219
Johnson, M., 156, 160
Juno, 9, 21, 22
Jupiter, 9, 28, 43, 49, 50, 61;
satellites, 92, 117
Keats, 1-3, 7, 8
Keill, 94, 112, 119, 156
Kelvin, Lord, 196, 197
Kepler, 95, 142
Kew, 95, 96, 188, 190
Kiel, 141
Kimura, 216
Königsberg, 192
Küstner, 118, 181, 183
Lalande, 7, 11, 107, 157
Lameia, 26
Laplace, 61
La Plata, 130
Latitude variation, 99, 100, 117, 118, 177-217
Lemonnier, 39, 53, 157
Le Verrier, 12, 43-85
Libussa, 26
Lick Observatory, 152
_Liouville's Journal_, 73
Lisbon, longitude of, 92
London, 23, 25, 96
Long, 157
Longitude, 92, 117
Lowth, Bishop, 119
Lyrae, [alpha], 184, 196
Macclesfield, Earl of, 94, 113
Mädler, 192
Magnetic observations, 161, 164, 174
Magnitude equation, 135
Markree, 23
Mars, 9, 28, 32, 34, 35, 91
Mayer, 39
Measurement of plates, 132-135
_Mécanique Céleste_, 61
Melbourne, 130, 193
Memorandum (Adams), 55
Mercury, 9
Messier, 7
Meteorites, 59
Meteors (November), 60
Metis, 22, 23
Micrometer, 5, 133
Milky Way, 125
Minerva, 9
Minor planets, 13-28
Minor planets tables, 22, 24, 26
Mistakes, 71-83
Molyneux, Samuel, 94-96, 101, 104
Monte Video, 130
Moon, tables of, 117
Names of minor planets, 22-28
Nasmyth, 162
"Nautical Almanac," 11
Nebula, 124, 146-152
Neptune, 11, 12, 38-85, 124
New College Lane, 112
Newcomb, Simon, 81, 183, 184, 195-202, 207, 208
New stars, 121, 140-154
Newton, 38, 84, 90-95, 105, 113
New York, longitude, 92
Ninina, 26
Northleach, 87
Northumberland, 65
Nova Geminorum, 141, 145, 146
Nova Persei, 143, 146-152
Nutation, 99, 100, 110, 115, 117, 118, 188, 219
_Observatory_ (magazine), 26
Ocllo, 26
Olbers, 20-22
Olympic games, 119
Oriani, 15
Ornamenta, 26
Oxford University, 87-89, 94, 105-119
Oxford University Observatory, 121, 130, 132, 136, 142, 145, 154
Palermo, Observatory of, 18
Palisa, 26
Pallas, 9, 21, 22
Parallax, 34, 91, 95-98, 109, 185
Paris, 130
Parkhurst, J. A., 145
Parthenope, 22
Peirce, 73, 80-83
Pendulum, 117
Perseus, 8, 143
Personal equation, 31, 134, 135, 185
Perth, 130
Perturbations of Uranus, 12, 42, 51, 54, 55, 61, 75
Peters, 188, 192
Phaëtusa, 26
Philosopher, 201, 219
_Philosophical Transactions_, 3, 4, 9
Photographica, 26
Photographic methods, 24, 33, 36, 121-139;
lenses, 125, 126
Photographs of sun, 163, 170-173
Piazzi, 13-18, 22
Pickering, E. C., 128, 144
Pittsburghia, 26
Plana, 61
Planetary distances, 13;
commission, 27;
numbering, 27
Planets by photography, 24
Pole Star (_Polaris_), 177, 178, 192, 193
Pond, 192, 213
Potsdam, 130, 181
Pound, Mrs., 104, 110-112
Pound, Rev. James, 89-94, 104, 115
Prague, 181
Precession, 96, 178
Prymno, 26
Puiseux, 32
Pulfrich, 154
Pulkowa, 181-188, 213
Quadrants at Greenwich, 116
Radium, 175
Radius vector, 52-58, 60-62, 79, 83
Rayleigh, Lord, 109
Records before discovery, 144
Reflector, 93, 127, 128
Reflex zenith tube, 192, 214
Refraction, 96, 101-103, 117
Refractor, 93, 128
Réseau, 133
Residual phenomena, 108-110, 118, 120, 218
Rigaud, S. P., 87, 115, 119
Rome, 130
Rothschild, 27
Royal Astronomical Society, 40, 47, 68, 74, 124, 155, 157
Royal Society, 4, 9, 10, 92, 94
Sampson, R. A., 74-76, 84
San Fernando, 130
Santiago, 130
Sappho, 32, 35
Saturn, 9, 43, 61, 149, 150
Savile, Sir H., 119
Savilian professorship, 87-94, 108-119
Schmidt, Julius, 142, 160
Schuster, A., 169
Schwabe, 155-163, 176, 177
Sheldonian Theatre, 119
Sherbourn, 87
Solar eclipse, 26, 170-176
Spectro-heliograph, 170, 171
Star-maps, 45, 65, 83, 124
"Star-trap," 24
Stereo-comparator, 154
Stone, E. J., 32
Struve, 184, 188, 192
Sun's distance, 28-37
Sun-spots, 155-176
Sydney Observatory, 130
Tacubaya Observatory, 130
Telescopes, 92, 124-129
Thames River, 105
Themistocles, 119
_Theoria Motus_, 17
Theory and observation, 208
Thomson, Sir W., 196, 197
Tides, 215
Titius, 13
Toulouse Observatory, 130
Tycho Brahé, 95, 140, 142
Uranus, 2-14, 25, 38-85, 144, 219
Variable stars, 140
Variation of latitude, 99, 100, 117, 118, 177-217
Venus, 9, 79;
diameter of, 92;
transit of, 28-32, 34
Vesta, 21, 22
Victoria, 22, 25, 32, 35
Von Zach, 20
Wallace, 119
Wansted, 88-94, 104, 110, 115, 188, 190
Ward, 119
Washington Observatory, 184-188, 193, 196, 213
Weather and sun-spots, 161, 167-169
Weyer, 193
Whiteside, 112
Williams, Mrs. E., 110, 111
Wind-vane, revolutions, 167-169
Winnecke, 32
Wolf, Dr. Max, 145
Wolf, Rudolf, 163
Wren, Sir C., 119
Yerkes Observatory, 145, 146, 152, 157, 170, 176
Zeiss, 154
Zodiac, 64, 124, 137
THE END
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Footnotes:
[1] The inferior planet Venus comes closer, but is not visible throughout
the night.
[2] The facts were collected with great care and ability by S. P. Rigaud,
and published by the Oxford University Press in 1832 as "Miscellaneous
Works and Correspondence of the Rev. James Bradley."
[3] Since the light must travel from the sun to Saturn _and back again to
the earth_, the interval would be more nearly 150 minutes.
[4] Monthly Notices of the Royal Astronomical Society, vol. xvii. p. 126.
[5] This should be Cambridge, _Mass._
[6] The distances do not represent the _total_ displacement, but only the
displacement towards Washington in one case and towards Pulkowa in the
other.
Transcriber's Notes:
Passages in italics are indicated by _italics_.
Passages in bold are indicated by =bold=.
Subscripted letters are indicated by {subscript}.
The original text includes the Greek a, b, and g. For this text version
these letters are presented as [alpha], [beta], and [gamma].
All side notes belonging to a single paragraph have been moved to the
beginning of the paragraph.
Sidenotes split across pages have been joined together.
Punctuation has been corrected without note.
Corrections in the "Errata" have been made in this text version.
The following misprints have been corrected:
"Hencke'" corrected to "Hencke's" (page 23 sidenote)
"annouced" corrected to "announced" (page 45 sidenote)
"are are" corrected to "are" (page 119)
"Konigsberg" corrected to "Königsberg" (Index)
Other than the corrections listed above, inconsistencies in spelling and
hyphenation have been retained from the original.
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