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Appendix 1. On the Arrangement of a Triangulation. 179. [p. 223] In arranging the course of a triangulation, for a survey in which the distances are short, many questions require to be considered, which never arise in ordinary cases of delicate observing. The lineal errors of centreing the instrument and signals become in many, perhaps most, instances as great as the angular errors of the observations. And further, as some of the stations are merely needed in the course of the triangulating, while others are required to permanently fix certain ancient points, the different character of the classes of the stations have, therefore, to be taken into consideration. Of course, in every survey, the number of observations is limited; and the question therefore arises how to distribute the observations so as to obtain the most accurate results. As a general rule, if there be a number of equally determined stations around a point which has to be fixed, it will be best to distribute the observations to and from it, equally among all the stations, as thus their individual errors of position will be neutralized and not transmitted. But, if among the stations around the point, some are much better fixed than others, it will be best to take more observations to and from those superior stations. Hence it is concluded that every station must have a certain weight of observations (or accuracy) assigned to it, to be aimed at; and a suitable number of observations to — and from — it; giving it, of course, a greater number of observations if the conditions are bad, as when there is a want of good cross-bearing in the directions of the observations. 
180. Having, then, a given weight of accuracy, and a corresponding number of observations, assigned to each station, how should this be distributed? In considering this it must be remembered that shifting the instrument and signals takes time equivalent to a certain number of observations; hence it is desirable to limit the number of instrumental stations, or from-stations; and make some to be only to-stations, on which signals are observed. Again the time of putting up observing signals (or testing the adjustment of them) over the stations, is equal to making several observations; hence only those stations really required should be observed to. [p. 224] The distinction should also be kept in mind, between (1) stations required-for-themselves, to fix points needed in the plan; and (2) stations required-for-others, to complete triangles, carry forward triangulation, &c., but which are of no further value when the results are obtained. If stations are only required-for-themselves, observations to them are sufficient, and save time in moving the instrument : beside this, observing from a station requires extra observations; a point may be fixed by two observations to it, as there are two unknown quantities; whereas it needs three observations from it, as there are three unknowns — the two co-ordinates and the zero of azimuth of the circle. But, on the other hand, if a station is required-for-others, observations from the station are best, as thus the rotational stiffness of the azimuth of the instrument is increased. Another consideration is that if the distances are short, and lineal errors of centreings are greater than angular errors of instrument, all stations should be observed from as much as possible, so as to increase the number of centreings, and diminish their uncertainties; on the other hand, in long distances, observations to are the best, as more can be obtained from a smaller number of stations in a fixed time. In actually arranging, then, the distribution of observations, after assigning the number proportionate to the accuracy required at each station, the considerations are:— (1) Whether the station is required-for-itself; or required-for-others; (2) whether the station may be only a to station, and not a from station; i.e., whether the observations to the signal upon it will suffice, without placing the theodolite upon it; and (3) the distance of the stations apart, and the consequent relation of angular to lineal errors between them. Keeping these considerations in view, the number of observations to be taken from each point to each other point is to be allotted, and entered in a table of cross-columns; and then the field book is to be prepared, reading in accordance with this system of distribution.
181. Beside the distribution of the observations, the order of them is most important. Reference to one station at intervals, in order to detect any shifting of the instrument, is but a poor check, as the epoch of any rotational shift cannot be precisely defined. Observations should be broken into small groups, so that there shall be immediate repetitions of allied stations; since any undetected shift will be far more important between the azimuths of two stations close together, than if between those far apart. Supposing, then, the stations A, B, C, near together, K, L, M, another set, and R, S, T, another set, the observations to these stations should be distributed thus:— A, B, C; A, K, B, C; A, K, L, B, C; K, L, B, C; K, L, M, B; K, L, M, R; L, M, R, S; M, R, S, T; R, S, T. Now if a shift is suspected at any point, the values of the azimuths to each station are divided into two groups, one before and the other after that epoch; and the mean value of each group is taken, with its probable error. [p. 225] Then if there be a constant difference between the first and second groups, in each of the azimuths, which is well beyond the range of the probable errors, the shift may be taken as proved; or at least as having a certain and calculable probability of its truth. As examples, the following were the shifts detected and eliminated in the course of the 700 observations of the whole triangulation (or a shift on an average at each 80 observations), with the probable errors of each shift; 1.9" ± .4"; 2.4" ± .2"; 3.6" ± .4"; 3.8" ± .5"; 4.2" ± .4"; 4.6" ± .7"; 60" ± 1.5"; 9.2" ± .2"; 11.0" ± 1.0". Thus the shifts are on an average over 10 times the extent of their probable errors, showing a probability of their reality, which would run to 12 places of figures. The first reduction applied was always a search for shifts in the series of azimuths, by tabulating all the observations; and from one cause or other — heating of the instrument, vibration by the wind, accidental touches in handling, &c. — these shifts thus occur to a perceptible amount once on an average of 80 observations. If the observations are treated in the usual way, without eliminating shifts, either they will be vitiated to some extent, or else if the shift be large, they would be lost altogether by the rejection of the whole of a set of observations as "inaccurate." From the various considerations above mentioned, the distribution and order of the observations were arranged, and then entered in blank form in the field book; thus in field work the order of the stations as entered had simply to be followed, and the observations filled in as they were made. Such an arrangement may perhaps be set down as too complex for "practical" men; but a couple of days spent in planning out the work may easily double the value of a month's surveying, and so save a great amount of time on the whole. Of course, the physical features of the ground generally modify the arrangements to some extent; as, for instance, if a station is much below the range of sight, the observations then require to be nearly all taken from it, since one very accurate centreing of the theodolite, by cross-transiting with an auxiliary theodolite, would suffice, instead of occupying time by setting up a signal with similar accuracy on several different days. In many other ways the irregularity of the field alters the arrangement of the observations, though the distribution of accuracy allotted to each remains unchanged.
Appendix 2. The Rejection of Discordant Observations. 182. [p. 226] This subject has been so warmly argued, and is at the same time looked on with so much disfavour by some workers, that it may seem presumptuous to discuss it in brief here. But some common-sense considerations seem to have been overlooked, while results were being deduced by more elaborate methods. And, as Airy says, "The calculus (of probabilities) is, after all, a mere tool, by which the decisions of the mind are worked out with accuracy, but which must be directed by the mind."1 In the first place, errors are of two classes: (1) Continual, i.e., present in every observation of a series; and (2) Occasional, i.e., only present in a few observations. Both these classes presumably, from theory and experience, follow the law of the distribution of error, well known as the Probability Curve. But, further, to take the continual errors first: this curve of the continual errors is in reality a curve of the sums of the errors due to various independent causes; for instance, the probable error of judgment in reading a circle might be .5"; of judgment in bisecting the object, another .5"; of judgment in placing the signal, =.3 "; of judgment in placing the theodolite, =.2 "; of flickering of the air, .6 "; making a probable error on the complete observation equal to But the occasional errors are those which need not occur, and which, occuring but seldom, may be to a large extent eliminated from the observations. They doubtless follow the same law of probability as the continual errors; but owing to their rarity, and the many causes of different extents and different varieties which give rise to them, their regular distribution is not seen. Among these [p. 227] causes are (1) absolute mistakes in reading, generally integral amounts, but sometimes of complements; (2) mistakes in identifying the signal, and mistakes due to irregular background and illumination of it; (3) instrumental defects of accidental character, bruises, expansions, &c.; (4) shifting of the instrument, or of the clamping; (5) constant lateral refraction in one line of sight, due to a column of heated air from a black stone, a wall face, &c. There is no place for these occasional errors in the usual classification, except with the continual errors before mentioned.
183. Now the recognition of the difference between these two classes of error will clear away a confusion which has arisen; one writer claiming that discordant observations should be rejected, while another says that errors of extraordinary extent are recognised by theory as possible, and therefore should never be rejected. In reality, both views are right; for though discordant observations should be rejected, if due to occasional errors, yet in continual errors any extent of error has some small amount of probability, decreasing with a diminution of the number of observations. How, then, are occasional errors to be detected? Solely by the application of the law of distribution of errors. We have no other guide. If among observations varying only a few seconds, one occurs differing by many minutes or degrees from all the others, no computer could be found to include it in a general mean; and yet it is rejected solely on account of its improbability, notwithstanding that extraordinary errors are recognised by theory as possible. What theory does not recognise, is an erratic distribution of errors; and it is precisely that which makes a computer throw out such a case as the above, by intuition. But the occasional errors, as I have said, most likely follow the law of probability, because in all cases in which a smaller error is more likely than a larger (as in all the causes of occasional error noted above), it is plain that the distribution will be like that due to continual errors. The real distinction between the two classes being that (practically) only a small portion of the observations are affected by occasional errors, and the greater part are absolutely free from them. If, then, the occasional errors follow the law of probability, they will (as being generally of much larger amount than the continual errors) be distributed over the whole range of continual errors, and far beyond that as well, But we can only eliminate the affected observations when they lie beyond the range of continual errors; and we cannot reject them when they lie within those limits. Hence, as they are more evenly and widely distributed than the continual errors (their Probability Curve being much wider), they will, on the whole, raise the probable error and its functions, which are deduced from the observations, even after the apparently discordant observations are omitted; in fact, they broaden the Probability Curve of the whole. Hence the true probable error of the [p. 228] continual errors alone is really less than it appears, even after so-called discordances are removed; and it is therefore proper to reject observations as being discordant to the full extent of this criterion, and not to save any cases that are near the boundary of acceptance.
184. We should note parenthetically in this section, a system which has been strongly advocated for the treatment of observations. This is by weighting them according to their distance from the simple mean of them all; and then employing the mean thus found as a fresh starting point for weighting, and so on ad infinitum, until a practically stable result is reached. This is so clearly fallacious when worked, that it is strange that it was ever proposed. The impossibility which it involves is seen thus:— Any increase of weight of one observation over another, dependent upon its distance from the mean, must result in displacing the calculated probable error and all its functions in the curve of distribution of the set of observations in question, bringing the probable error much nearer to the centre; this is at once a denial of the truth of the law of probabilities, and a contradiction of terms which it is useless to discuss further. Beside this, the practical result of weighting observations inversely as their distances from the mean, is that if the number of observations be even, the mean is eventually thrown in a position anywhere between the two central observations; as its position is indifferent, provided it only have any equal number of observations on each side of it. Or, if the number is odd, the final mean is immovably fixed to the central observation. If otherwise the weighting is inversely according to square of the distance of the observation from the mean, the successive means are attracted more and more to whatever observation is nearest to the first mean, and the final result sticks to this observation; like a south pole of a rnagnet, which has taken its choice of a lot of north poles. Thus, both in theory and practice, the idea of any weighting dependent on the distance from a mean is inadmissible.
185. The best practical way of applying the law of probabilities to a group of observations, for the elimination of the occasional errors, will now be considered. A usual method is to extract the probable error, and then (knowing the number of observations) to find from a table what multiple of the probable error the largest variation should be, and reject all beyond that. Of course, this process requires repeating until constant results are obtained, as the first probable error is increased by the discordant observations which are afterwards rejected. The defect of this method is that as the distribution of the most divergent observations is very irregular, owing to their rarity, it is therefore not suitable to regard their extent so much as their number in relation to the whole. On looking at the Probability Curve, it is seen that the point in which its [p. 229] range is best defined (i.e., in the direction of the magnitude of errors) is, of course, at the point of maximum inclination. And this point is identical practically (if not also theoretically) with the square root of the sum of the squares of the differences, divided by the As the various functions have received rather different names, it will be as well to state them here, to avoid confusion. A, refers to Airy in "Errors of Observations;"2 D, to De Morgan in "Essay on Probabilities;" and M, to Merriman, in "Method of Least Squares." The notation adopted is Συ = sum of differences from mean; Συ  [ * See footnote 2. ] These formulae of course refer to the functions for a single observation, and must be ÷ The maximum inclination of the curve being, then, at the error of mean square, the most accurate method of testing observations is to extract this error of mean square from them by the formula; and then (by the tables of the Probability Curve) .682 of the number of observations, or a little over 2/3 of all, should have their differences from the mean less than this amount. Or it is nearly as satisfactory to take the simple average of the differences, and then (by the tables) .575 of the observations, or 4/7 of all, should differ from the mean less than this function. If on testing the observation thus, by either method, it is found that more than the due proportion of all are within the limit stated, it shows that the limit is too wide; and hence that the most divergent observations should be rejected, and a fresh limit computed from the remainder, until the proper proportion of all the observations is within the limit of the function calculated. This system of weeding may thus be done by using any function of the curve; but the error of mean square is the most accurate in results, occurring at maximum inclination; and the average error is the most easy to work.
186. [p. 230] To take a practical example, the following are the angular differences between the observations and the mean stations, on distances between 10,000 and 20,000 inches, in the survey around the Great Pyramid. The limits of distance are necessary, as the relation of lineal to angular error is otherwise too variable, and so affects the character of the distribution; the differences requiring treating in groups according to the distances involved. The following is the largest group, and thus best exhibits the method of weeding. 
Here all the earlier differences are certainly within the range of continuous errors, and it is not until within the last 8 observations that there is any need to search for the limit of rejection. Accordingly, the sum of the squares is only taken after each of the last 8 observations; i.e., each horizontal line of figures of "Working" and "Result" shows what the result would be if all the observations below that line were cut off and ignored. We see, on looking to the last two columns, what the results are: that up to within four observations from the end, the theoretical (or normal) and the actual number of observations, within the limit of " error of mean square," are closely in accordance; the actual being rather too few in the first two, shows that some regular or continuous observations have been cut off. Then, after that, the actual and normal numbers agree within less than one number on three successive lines, showing that the [p. 231] limit of continuous observations is nearly reached. After this point, if any more observations are included, the limit rapidly becomes too large, and includes too many observations in the actual series. For instance, including all the observations, the error of mean square is 3'40", and looking in the series of differences in the column of " Data," it is seen that 28 of the differences are less than that amount; whereas rather fewer than 24 differences should exceed it by the regular law of errors (i.e., .682 of the total number of 35 differences), and this proves that the limit given by the mean square is unduly increased by reason of including some discordant observations, affected by occasional errors. Thus in the above example we see that 4 out of 35 observations are affected by occasional errors, and are detected by their lying beyond the range of the distribution of continual errors. These four are accordingly to be rejected, as being influenced by some of the various occasional causes of error indicated before; and as nearly all of the quantities to which these differences belong, are the mean of several observations repeated at intervals, it shows that the causes are probably those not affected by the instrument or observer, but arising from local conditions of refraction, deceptive view of signal, &c. In the whole of the mean observations, on 108 sides of triangles around the Great Pyramid, only 9 are rejected by the above criterion, as being vitiated by occasional errors.
187. A difficulty which has been raised against the universal application of the law of distribution of errors (or Probability Curve) is that + and - errors cannot be equally likely in certain cases. This may possibly be true in some peculiarly conditioned cases of physical impossibility; but the objection was applied to a class of cases which really present no such difficulty. The type which has been discussed is that of guessing the area of a field; the truth being, say, 2 acres, it was objected that a man might guess 4 or 6, but could not guess 0 or - 2. But this difficulty is due to a wrong statement of probable error. It is true that in general, for convenience (and the probable error being but a small fraction of the whole quantity), we usually denote it as + or – ; but in reality it should be written x or ÷. It is a factor, and not a term. For instance, a probable error of a tenth of the whole is not ± .1, but is really This true expression of probable error becomes of great importance where the probable error is large in relation to the whole. Suppose we write the angular width of an object as 2" ± 1", the limits then are 1" and 3"; but if we state its distance in terms of its lineal breadth, we write 100,000 ± 50,000, which implies limits of 50,000 and 150,000, or angularly of 1 It is clear, then, that probable errors must be really multiples of the quantity; and therefore they can only be expressed by + and - when using the logarithm of the quantity.3 Similarly the factor
188. One class of cases might be supposed to illustrate the impossibility of both + and - errors occurring; namely, that of soundings, or measurements with a flexible measure, and the adjustment of one object to fit within another. Here it might seem as if errors could only exist in one direction. But, to take the case of soundings, if we merely suppose the - half of the Probability Curve abolished, we must expect by theory to find the greatest number of observations nearest to the truth, no matter how slack the line, or how strong [p. 233] the current; whereas it is manifest that in practice we shall always have some deflection of the line, never getting it quite straight, and seldom even nearly straight. Hence there must be some amount of error which we are more likely to make than none at all; i.e., the curve of observations has not its maximum at 0 difference. The explanation is, that what we really measure is not one quantity, but two combined. The length of the line is equal to the invariable distance measured, + the shortening of the line due to deflection. This last quantity is the variable; and its mean amount depends on the tension of the line, the length, area, and friction of the line, and the strength of the currents. And we have no reason to suppose that the variations, from this mean amount of deflection, do not follow the law of probabilities. For instance, if in sounding to a certain depth, the mean shortening of the line is 100 feet, then a variation of x or of ÷ 5 is equally unlikely; i.e., a shortening of only 20 feet, or of 500 feet, is equally rare. We can see instantly that the amount of shortening can never become 0 nor
189. In stating the probable error of our knowledge of a quantity, we really state the exact unlikelihood of the quantity exceeding or falling short of a certain amount; we introduce a second quantity to define the uncertainty of the first. And this second quantity is liable to be in error, just like the first quantity; its exact amount, or the chance of the truth exceeding certain limits, is only a fallible statement derived from a series of observations; and it may, therefore, be incorrect. In short, the probable error itself has a probable error, and this secondary probable error has a tertiary probable error; so that the series of probable errors is infinite, though rapidly diminishing. In the following discussion, which is limited to secondary probable errors, p.e. I denotes the primary probable error of the datum; and p.e. II the secondary probable error, or probable error of p.e. I, its limits being rigorously stated as a multiple of p.e. I. [p. 234] Now looking at the p.e. I of a single observation (deduced from the divergencies between the observations), it is plain that it will be known more and more accurately the greater be the number of observations; i.e., there will be a diminution of the p.e. II of a single observation, by increasing the number of observations, exactly as there is a diminution of the p.e. I of the mean by increasing the observations. Hence log. p.e. II of one observation varies as The arithmetical method for determining the value of p.e. II is precisely like that for working out p.e. I. When the observations are all the same, i.e., when the first differences vanish, p.e. I vanishes; similarly, when the first differences are all the same (irrespective of sign), i.e., when the second differences vanish, p.e. II vanishes. To practically exemplify these two statements, we take two examples. The observations on the position of rest of a pendulum will be all the same, and there will be no probable error, apart from mechanical irregularities: in this case first differences have vanished, and p.e. I vanishes. With a coin tossed up, its mean position when at rest again will be on edge (since heads and tails are equally likely), and the difference from its mean position will be constant, 90º : in this case, first differences being all equal (i.e., 90º), the second differences have vanished, and p.e. II vanishes. This result we can see to be true, since there is no uncertainty about p.e. I, but it is absolutely known that the chance of heads or tails is exactly 1/2, and can never be anything else: hence there is no p.e. II; it has vanished, as theory shows us. From this it follows that as there is a normal distribution of errors (the Probability Curve), so there must also be a normal p.e. II. And this normal p.e. II, thus deduced, is = p.e. I Now this theory is open to actual test thus: take a large series of observations casually arranged, and break it into groups, each containing an equal number of observations, say 5, 10, or 25 in a group; then take the probable error of the mean value of each group, this is its p.e. I. So far the process is usual enough; but now compare these probable errors of the equal groups together, see how much they vary, and take the mean p.e. I for each method of division; the amount of variation from the mean p.e. I shows the uncertainty of the p.e. I in each method of division; and from this we can calculate the p.e. II, just as we calculate the p.e. I from any other set of differences from a mean. In this way the theory can be checked; and on working out five complete cases of this check, [p. 235] consisting of from 4 to 10 groups in each case, the p.e. II was practically found to average = p.e. I This is such a satisfactory approach in practice to the theoretical value p.e. I
190. The practical result of the recognition of the secondary probable error is, that it is needless to employ rigorous formulae, or to spend any extra time, in order to obtain the exact value of the primary probable error of the determination in question: and, that the fewer the observations the more useless is an accurate formula, since the probable error has a much larger uncertainty inherent in it. This fact is so far contrary to usual views that it is needful to point it out; one treatise, when mentioning the less rigorous formulae for probable error says: "For values of n less than 24 it is best to hold fast to the more exact formula;" and then, half recognising the increased uncertainty of the probable error with fewer observations, it continues, "and even that cannot for such cases be expected to give precise results, since the hypothesis of its development supposes that enough observations have been taken to exhibit the several errors in proportion to their respective probabilities" (Merriman's "Least Squares," p.189). Now of the approximate formulae sometimes employed for probable error, one of the simplest and most useful is that formed by the mean difference, instead of the error of mean square. By the law of distribution this mean difference x .845 = probable error; i.e., in a normal distribution of errors, the one value above and below which are an equal number of errors, will be .845 x the mean of all the errors. The variation of the result by this formula from that by the formula on the error of mean square, will seldom be of any importance in view of the secondary probable error; for if there be much difference between the two results it shows an irrationality of distribution, which implies a large secondary probable error. Therefore time would be better spent in carefully searching for "occasional" errors, rather than in taking the squares of the quantities, in order to obtain a statement of probable error, with a fallacious appearance of accuracy. In fact, the usually pretentious regard for rigorous formulae of probable error, while ignoring altogether the secondary probable error, is only another form of the old fallacy of stating a mean result to an absurdly long row of figures, regardless of the primary probable error. While showing due honour to the system of observing the probability of the main result, computers have fallen into just the same fallacy over the probable error [p. 236] itself, through sinking the common-sense of the work in an unthinking regard for rigorous methods. Beside the formulae for probable error from mean square and from mean difference, there is also the simplest formula of all, i.e., selecting such a value as shall have half of the differences larger and half of them smaller than the amount of probable error. This definition is the fundamental meaning of the expression; and as a formula it has the advantage over all the others, that it does not depend mainly on the amounts of the largest and most variable of all the observations, but it gives equal value to every observation in the formation of the result. It is true this method does not turn out a neat value to three places of figures, but on the contrary faces the computer with the naked uncertainty which there is in the amount of the probable error; the fewer the observations, the more doubt he must feel as to the exact value. But this is rather an advantage than otherwise, as no man can shut his eyes to the secondary probable error when he has the vagueness of the primary error so plainly before him.
191. One other point of practice may be noted. It is usual, if a series of differences are to be compared with the law of distribution, or Probability Curve, to require that the total number shall be very large; and to compare them by taking the sums of all between certain successive limits. Or, graphically speaking, to draw the curve of the heap of observations, and see how that coincides with the normal curve But a more satisfactory method — which does away with the irregularity of successive steps, and which may be applied to any number of observations — is that of forming a table of the value of each difference (in terms of probable error of one observation = unity) according to the normal distribution. Thus suppose it is wished to test 8 observations by the law of distribution. Dividing the whole area of the curve in 8 equal parts, take the difference due to the middle of each part: at .0625 area (middle of 1st 1/8th) difference is .116 x p.e.; and so on to .9375 area (middle of 8th 1/8th), when difference is 2.76 x p.e.  Such a table, for any given number of observations, may be readily constructed from a curve formed by the number of observations (or area of Probability Curve) as one ordinate, and the multiple of the probable error as the other ordinate. By such normal tables occasional errors can be readily searched for; [p. 237] as, if a few of the more discordant observations ought to be rejected, it will be found that the final entries in the normal table agree with the observed differences a few lines higher up. In this Appendix some exception may be taken by the reader to the consideration of every question by means of its practical applications; and to the absence of proofs deduced from the more elaborate processes of algebraical deductions from the fundamental theories. But since these fundamental theories have never been completely demonstrated, apart from all practical experience; so there is nothing unsuitable in referring directly to the practical working of a method. With respect to the fundamental law of probability, Merriman writes: "In the demonstration of this law of error ... there are two defects ... and they cannot be bridged over or avoided, but will always exist in this mathematical development of the law of probability of error" ("Method of Least Squares," p. 196-7). Airy writes, of the same law, "Whatever may be thought of the process by which this formula has been obtained, it will scarcely be doubted by any one that the result is entirely in accordance with our general ideas of the frequency of errors" ("Errors of Observation," p. 15). And after giving at the end of the same book, a practical example of the distribution of errors in the N.P.D. of Polaris, he concludes thus, "the validity of every investigation in this Treatise is thereby established" (p. 119). After these appeals to the ultimate dependence on experience, it can hardly be thought objectionable to take the shortest road to the practical demonstration of each question.
Appendix 3. The Graphic Reduction of Triangulation. 192. [p. 238] In the foregoing Appendix, on the Rejection of Discordant Observations, the method for eliminating those observations affected by occasional errors, has been pointed out. It is needless to enlarge on the importance of some correct and universal rule for the discrimination of errors which may lie beyond those of the normal distribution; extreme cases are always rejected arbitrarily by every computer, and the question where to draw the line of selection should be determined by some law, rather than by caprice, or even intuition. But in the reduction of triangulation by least squares, when once the equations are formed, the whole process is in a mill; and the computer turns the handle, and grinds out the result, without the chance of seeing anything until it is finished. When completed, and the differences of the observations from the mean azimuths are worked out, then if some of the differences are seen to be due to occasional errors (or "discordant observations") they ought to be rejected, as certainly vitiating the result. Yet this implies a re-working of the whole calculation, a matter perhaps of weeks; and this would probably need to be done several times, until the differences conformed to the normal distribution. Yet unless some search is made for occasional errors, the apparent accuracy of the results cannot be trusted for a moment; and a few observations — which if varying as much in a simple set of unentangled observations would be summarily rejected by probabilities — will render useless the elaborate care spent on the reduction of the whole. What is needed, then, is some way of knowing how the results are going during the working; and above all some way of quickly seeing what difference will be made by the rejection of some one discordant observation, and whether omitting it will enable all the others to be easily reconciled. As no possible clue to this can be obtained in the course of equational reduction, some graphical method is the only apparatus which will suffice. Whether, then, we finally adopt a rigorous equational reduction, or no, still a graphic reduction is needed in all cases to point out the locality of the larger errors, and their approximate amounts.
193. [p. 239] Graphic reduction, as generally understood, means simply drawing the results of the observations on sheets, and fitting them together. In the case of angular observations, the angles are drawn radiating from a theodolite centre on each sheet; and then these sheets can be superposed, and moved in the unknown elements of azimuth and position, i.e., shifted about in rotation and translation, until the observations fit together with the least divergences. Now though this is a very rude method in general, it contains the principle of a method which is capable of being worked with any amount of accuracy. The rudeness of it only results from the necessarily small size of the sheets, in relation to the whole extent of the survey; since this makes the errors of the graphic drawing on the sheets far greater than the errors of the observations in any accurate work. If then we could have sheets, each as large as the whole ground of the survey, — a furlong, a mile, or a hundred miles across, — and draw on each sheet radii corresponding to the observed mean azimuths, or the traces of the observations, around some one station; and then if these sheets were superposed, and shifted in translation and rotation, until the traces coincided as nearly as possible one with another, and with the theodolite centre, at each point; then we should have the most probable system of resulting stations, and differences of observations from these stations. Now, if instead of the sheets covering the full size of the ground (which would be physically impossible to realize), they are reduced to a fraction of that size, and all the distances of the stations apart are similarly reduced, it is plain that rotation or translation of a sheet (within a small angle), will affect all the traces as before; only if the reduction is, say, to 1/60th of the lineal distances, then a rotation of I° of the sheet, will shift the traces lineally as much as a rotation of I' on the full scale on the ground.
194. The practical method, then, for graphic reduction on any scale, is to assume a provisional place for each station, and calculate by co-ordinates the differences of the observations from the assumed places, exactly as in the first step of the reduction by least squares. It is generally best to adopt a scale of 1/3600th (or some simple multiple of that) for plotting the sheet with the provisional places of the stations.6 Then, with this reduction, if the angular differences are plotted with a protractor, reading 1° on it for every 1" of actual difference, the traces will be drawn on the same scale as they are on the actual ground. [p. 240] Thus the traces of the mean of the observations of each of the azimuths around one station, are all plotted on one sheet (marking also the place of the central station, i.e., of the theodolite); all the azimuths around another station, on another sheet, and so on, using as many separate sheets as there are theodolite stations in the survey. These sheets being then all superposed, all the traces to any one station are seen crossing one another; and the theodolite centre of each station will be seen on the sheet of that station, among the traces which are drawn on the other sheets. Practically the traces are drawn on some transparent substance (as mica), in order to see through a large number of sheets together. Then the actual work of reduction consists in shifting these sheets in translation and rotation, until the most probable adjustment of all the traces is reached. This is a work taking some hours or days; but it is the equivalent of some days or months of work in the reduction of simultaneous equations. Many hypotheses have to be tried; each sheet is shifted about in turn, and any apparently erratic observation is disregarded for the time, and a fresh trial of adjustment is made; if no great improvement ensues in the adjustments, the observation is taken into the general mass again; also the likelihood of various eccentricities of the theodolite setting over each station, can be investigated. In short, the causes of all apparently abnormal discordances, can be felt for in different directions; and they can thus be generally tracked down to some one observation, the elimination of which reconciles many others. Some hesitation may be felt at such a rejection of observations; but it must be remembered that the omission of the most discordant of; say eight, really normal observations, would not diminish the mean divergence of them by more than 1/5;7 an amount not very striking, and making a difference which would certainly not lead the adjuster to reject one observation in eight. If an average improvement of the adjustment greater than 1/5 (or, say, 1/4), can be made by omitting 1 in 8 of the observations, then the computer is bound to omit it by the laws of probabilities, as being due to some occasional error. Having thus adjusted these sheets to apparently the most probable arrangement, the mean stations to be adopted from the traces should be marked; and the difference of this, from the provisional places of the same stations, is then read off. Applying these corrections to the co-ordinates of the provisional places, we have the finally adjusted co-ordinates. The sheet of provisional places of the stations may be applied in any position to the adjusted points of the traces, for reading off the corrections; its position is of no consequence, as it affects all stations alike. [p. 241] Finally, the differences of the observations from the adjusted positions of the stations should be calculated; just as at first they were calculated from the provisional stations. Then these differences may be plotted all on one sheet, and they represent the variations of the traces as finally adjusted, from the finally adopted places of the stations.8 If, then, the graphic adjustment has not been satisfactory, or if an error has been made in any part of the computations, it will be shown by the position of the station not being in the midst of the plotted traces.
195. Such a delineation of the traces may be seen, for the most important part of the present survey, in the diagram of "Traces of the Actual Observations," Pl. xvi. To have included all the stations of the survey, would have made the sheet unmanageably large to print; hence, only those around the Great Pyramid are here shown. But beside the traces themselves, their probable errors must also be considered; for it is needless to shift a sheet so as to bring one trace nearer another, if the probable errors of the two traces already overlap, while perhaps the shifting separates still further two traces, whose probable errors are already far apart. Accordingly, instead of drawing lines to represent the traces on the adjustment sheets, bands should always be drawn, extending in their widths to the limits of the probable error; and the distances of the traces apart should always be regarded in terms of their probable errors. These bands of probable error are represented as they cross at station U, on Pl. xvi; only in actual working they are a thin transparent wash of ink, through which other bands can be easily seen; and which is made thinner the wider it is, and the less the observation is worth. At W, here, only the halves of these bands are drawn, to avoid confusion. And at all the other stations the half traces, without probable error bands, are drawn, as the diagram would be otherwise too crowded to be intelligible. Another change in this diagram, from the actual appearance of the working sheets of reduction, is that instead of a spot representing the position of the theodolite at each centre, here the reflex traces are marked; these are the lines in which the theodolite should lie, in order that the direct trace from it should coincide with the adopted station. These reflex traces are dotted; and it should be remembered when looking at the diagram, that the theodolite station is the mean of the dotted traces on any station; and in so far as this does. not coincide with the mean of the direct traces, it shows an error of observing the eccentricity of the theodolite position.
196. This diagram (Pl. xvi) shows practically how nearly the observations of a survey may be adjusted, by a single process of graphic reduction. No alteration in any respect has been made from the results obtained by the first [p. 242] graphic working (in which all corrections for levelling, eccentricities, &c., were duly made), except that the ultra-discordant observations, due to occasional errors, are here omitted; as, owing to their great divergence, they would become confused with the wrong stations; but the 154 traces which agree to the law of errors are all shown here. In no case could any improvement be suggested in the adopted places of the stations, beyond the limits of their probable errors. But in Z and a some change may be still needed, by a second process of graphic reduction; a going further north, and Z further south, and somewhat west. This has not, however, been altered here, as the westing of Z is the only change of importance, and it would diminish the base of survey by about .08 (or .09 inch on Pyramid base length); and a re-comparison of the standard tape used for the measurement of the survey-base, shows a similar change of distance = .12; these errors therefore balance one another, far within the limits of probable errors. Hence no notice has been taken of these insignificant amounts in stating the results. The base of survey was measured on three different days independently; each length in each operation being read four or five times. The probable error of the final value of the base, is shown by the breadth of the black terminal band at Z, with an arrow at the end of it; and the actual differences between the 'three days' results are shown by the three short lines above the terminal band. It will be seen that the uncertainty of lineal measure is not much less than that of angular position; this is as it should be, for in all surveys the error of the length of the base should be nearly of the same amount as the errors of observing on it in triangulation; otherwise either lineal or else angular accuracy is wasted. The probable errors of the positions of the stations, as deduced from the adjusted traces, is here shown by the radius of a small circle around each station. It was calculated from the divergences of the traces; and though this is not entirely a rigorous method, yet it gives results quite as near as is necessary, if we neglect the ellipticity of the probable errors. Strictly the probable error limits of all stations in planes are elliptic, and cannot be expressed by fewer than three elements; describing it in the two co-ordinates being insufficient, unless another element is added. The formula for probable error in two dimensions differs, of course, from that for ordinary probable error in one dimension. Instead of n we must take 2n, as only half the traces on an average are available in any one direction; and for n - 1 we must take n - 2, as two traces are needed to fix a point. The general results of the differences of the traces from the mean stations adopted, in the diagram here given, are as follow. The mean of the differences in the various groups being:— [p. 243]
Hence it may be generally said that there was an average error of 1/12 inch lineally in the azimuths; and in distances over 1/4 mile this error was exceeded by the average angular error of .8".
197. Such, then, is the method of graphic reduction, as applied to observations on plane surfaces; adaptable to any scale of representation, and to showing any amount of accuracy. If meridian observations be taken, they may be marked as lines (or ends of lines) on the sheets; and one element of the adjustment will then be the parallelism of these lines, or rather of their probable error bands. For observations on a sphere, the same method of reduction is equally applicable to co-ordinates of latitude and longitude, plotted on a suitable projection; provided the curvature is not extensive enough to modify the distances, so that a rotational shift does not affect the various stations proportionally. This error could not occur in terrestrial observations, and so the method is applicable to all geodetic surveys. It should be observed that the graphic reduction is equivalent, not merely to the usual system of reduction by least squares, from equations of shift of the points; but it is equivalent to a system of equations which allows not only of lateral shift of the points, but of rotational shift of all the observations around each centre, and also of disseverance of the centreing of the theodolite over a station, from all the other observations to that station; beside this, it takes account of the probable errors of all the observations. Thus it is equivalent to the determination of five unknown quantities for each point; i.e., the two station co-ordinates, the two theodolite co-ordinates, and the zero of azimuth of the circle. And any system of reduction which does not include all of these five unknowns is defective, and cannot impartially render the truest results. Hence the graphic reduction of a network of a dozen stations, which is easily performed, is equivalent to the elaborate formation and solution of 60 normal simultaneous equations, with cognizance of all the probable errors of the observations; and equivalent not only to doing that once, but to doing it many times over, until all occasional errors have been weeded out. In short, a few days' work with graphic reduction will master a mass of observations and unknown quantities, so complex that its solution by least squares would only be attempted for such an object as a national survey. In any case it is desirable to employ the graphic method; as, if the method of least squares should eventually be used, still the [p. 244] graphic work takes but a small fraction of the labour; and it is invaluable for showing the places of occasional errors, which would otherwise vitiate the result from the least squares. And it is almost certain that in all cases the graphic results (especially by a repeated process), are well within the probable errors of the most accurate determination obtainable; and thus practically as accurate as any result that can be procured Hence the graphic method will in most cases obviate the necessity for far longer processes; and also bring the adjustment of check observations within the range of practical work, to a far larger extent than is the case at present. |
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(.5
+.5
1.1.
" and 4". Thus it is impossible, writing + or - , that the limits shall be the same in stating a quantity, and in stating its reciprocal. Hence our notation, + and - , must be defective. If; on the other hand, we write 2" 
since that would be the same result as 
and it will thus be Mean 
; and (in the absence of experiments) our intuitive judgment would certainly not rebel at the idea of a mean shortening of 100 being as unlikely to vary up to 1,000, as to be diminished to only 10 feet, by the run of casual circumstances. Precisely the same principle applies to one object inside another. If, on an average, a shake of 1/100 inch is made (say, in filing a nut-spanner), anyone accustomed to do delicate mechanical work will allow that a fit to 1/500 inch is as unlikely to occur as a misfit of 1/20 inch.
But log. p.e. I of the mean also varies as 
in relation to the whole quantity.