There is no doubt that this is a perfectly sound postulate. Like all ultimate postulates it is indemonstrable; Mill's derivation of it from Experience did not amount to a demonstration. It is simply an assumption on which we act. If any man cares to deny it, there is no argument that we can turn against him. We can only convict him of practical inconsistency, by showing that he acts upon this assumption himself every minute of his waking day. If we do not believe in the continuance of observed uniformities, why do we turn our eyes to the window expecting to find it in its accustomed order of place? Why do we not look for it in another wall? Why do we dip our pens in ink, and expect the application of them to white paper to be followed by a black mark?

The principle is sound, but is it our only postulate in inference to the unobserved, and does the continuance of empirical laws represent all that Science assumes in its inferences? Mill was not satisfied about this question. He pointed out a difficulty which a mere belief in empirical continuity does not solve. Why do we believe more confidently in some uniformities than in others? Why would a reported breach of one be regarded with more incredulity than that of another? Suppose a traveller to return from a strange country and report that he had met men with heads growing beneath their shoulders, why would this be pronounced more incredible than a report that he had seen a grey crow? All crows hitherto observed have been black, and in all men hitherto observed the heads have been above the shoulders: if the mere continuity of observed uniformities is all that we go upon in our inferences, a breach of the one uniformity should be just as improbable as a breach of the other, neither more nor less. Mill admitted the difficulty, and remarked that whoever could solve it would have solved the problem of Induction. Now it seems to me that this particular difficulty may be solved, and yet leave another behind. It may be solved within the limits of the principle of emperical—meaning by that observational—continuity. The uniform blackness of the crow is an exception within a wider uniformity: the colour of animals is generally variable. Hence we are not so much surprised at the reported appearance of a grey crow: it is in accordance with the more general law. On the other hand, the uniform position of the head relative to other parts of the body is a uniformity as wide as the animal kingdom: it is a coincidence repeated as often as animals have been repeated, and merely on the principle that uniformities continue, it has an absolutely uncontradicted series in its favour.

But is this principle really all that we assume? Do we not also assume that behind the observed fact uniformity, there is a cause for it, a cause that does not appear on the surface of the observation, but must be sought outside of its range? And do not the various degrees of confidence with which we expect a repetition of the coincidence, depend upon the extent of our knowledge of the producing causes and the mode of their operation? At bottom our belief in the continuance of the observed uniformities rests on a belief in the continuance of the producing causes, and till we know what these are our belief has an inferior warrant: there is less reason for our confidence.

To go back to the illustrations with which we started. If we have met a man every day for months at a certain place at a certain hour, it is reasonable to expect to meet him there to-morrow, even if our knowledge does not go beyond the observed facts of repeated coincidence. But if we know also what brings him there, and that this cause continues, we have a stronger reason for our expectation. And so with the case of poles at regular intervals on a road. If we know why they are placed there, and the range of the purpose, we expect their recurrence more confidently within the limits of that purpose. This further knowledge is a warrant for stronger confidence, because if we know the producing causes, we are in a better position for knowing whether anything is likely to defeat the coincidence. A uniformity is said to be explained when its cause is known, and an inference from an explained uniformity is always more certain than an inference from a uniformity that is merely empirical in the sense of being simply observed.

Now, the special work of Science is to explain, in the sense of discovering the causes at work beneath what lies open to observation. In so doing it follows a certain method, and obeys certain conditions of satisfactory explanation. Its explanations are inferences from facts, inasmuch as it is conformity with observed facts, with outward signs of underlying causal nexus, that is the justification of them. But they are not inferences from facts in the sense above described as empirical inference. In its explanations also Science postulates a principle that may be called the Uniformity of Nature. But this principle is not merely that observed uniformities continue. It may be expressed rather as an assumption that the underlying causes are uniform in their operation, that as they have acted beneath the recorded experiences of mankind, so they have acted before and will continue to act.

The foregoing considerations indicate a plan for a roughly systematic arrangement of the methods of Induction. Seeing that all inference from the data of experience presupposes causal connexion among the data from which we infer, all efforts at establishing sound bases of inference, or rational ground for expectation fall, broadly speaking, under two heads: (1) Methods of ascertaining causal connexion among phenomena as a matter of fact, that is, Methods of Observation; and (2) Methods of ascertaining what the causal connexion is, that is, Methods of Explanation.

These constitute the body of Inductive Logic. But there is a preliminary and a pendant. Without raising the question of causal connexion, we are liable to certain errors in ascertaining in what sequence and with what circumstances events really occurred. These tendencies to error deserve to be pointed out by way of warning, and this I shall attempt in a separate chapter on observation of facts of simple sequence. This is preliminary to the special methods of observing causal sequence. Then, by way of pendant, I shall consider two modes of empirical inference from data in which the causal connexion has not been ascertained or explained—Inference from approximate generalisations to particular cases, and Inference from Analogy.

Most of these methods in one form or another were included by Mill in his system of Inductive Logic, and the great merit of his work was that he did include them, though at some sacrifice of consistency with his introductory theory. With regard to the kind of empirical inference which that theory, following the lead of Whately, took as the type of all inference, Logic has really little to say. It was this probably that was in Mill's mind when he said that there is no Logic of Observation, ignoring the fact that the Experimental Methods are really methods of observation, as well as the Methods of Eliminating Chance by calculation of Probability. There is no method of observing uniformities except simply observing them. Nor indeed is there any "method" of inferring from them: we can only point out that in every particular inference from them we assume or postulate their continuance generally. As regards their observation, we may point out further that a special fallacy is incident to it, the fallacy of ignoring exceptions. If we are prepossessed or prejudiced in favour of a uniformity, we are apt to observe only the favourable instances, and to be blind to cases where the supposed invariable coincidence does not occur. Thus, as Bacon remarked among his Idola, we are apt to remember when our dreams come true, and to forget when they do not. Suppose we take up the notion that a new moon on a Saturday is invariably followed by twenty days of unsettled weather, one or two or a few cases in which this notably holds good are apt to be borne in mind, while cases where the weather is neither conspicuously good nor bad are apt to be overlooked. But when a warning has been given against this besetting fallacy, Logic has nothing further to say about empirical uniformities, except that we may infer from them with some degree of reasonable probability, and that if we want ground for a more certain inference we should try to explain them.

Chapter II.

ASCERTAINMENT OF SIMPLE FACTS IN THEIR ORDER.—PERSONAL OBSERVATION.—HEARSAY EVIDENCE—METHOD OF TESTING TRADITIONAL EVIDENCE.

All beliefs as to simple matter of fact must rest ultimately on observation. But, of course, we believe many things to have happened that we have never seen. As Chaucer says:—

For the great bulk of matters of fact that we believe we are necessarily dependent on the observations of others. And if we are to apply scientific method to the ascertainment of this, we must know what errors we are liable to in our recollections of what we have ourselves witnessed, and what errors are apt to arise in the tradition of what purports to be the evidence of eye-witnesses.

I.—Personal Observation.

It is hard to convince anybody that he cannot trust implicitly to his memory of what he has himself seen. We are ready enough to believe that others may be deceived: but not our own senses. Seeing is believing. It is well, however, that we should realise that all observation is fallible, even our own.

Three great besetting fallacies or tendencies to error may be specified:—

1. Liability to have the attention fastened on special incidents, and so diverted from other parts of the occurrence.

2. Liability to confuse and transpose the sequence of events.

3. Liability to substitute inference for fact.

It is upon the first of these weaknesses in man as an observing machine that jugglers chiefly depend on working their marvels. Sleight of hand counts for much, but diverting the spectator's eyes for a good deal more. That is why they have music played and patter incessantly as they operate. Their patter is not purposeless: it is calculated to turn our eyes away from the movements of their nimble hands.

It must be borne in mind that in any field of vision there are many objects, and that in any rapid succession of incidents much more passes before the eyes than the memory can retain in its exact order. It is of course in moments of excitement and hurry, when our observation is distracted, that we are most subject to fallacious illusions of memory. Unconsciously we make a coherent picture of what we have seen, and very often it happens that the sequence of events is not what actually passed, but what we were prejudiced in favour of seeing. Hence the unlikelihood of finding exact agreement among the witnesses of any exciting occurrence, a quarrel, a railway accident, a collision at sea, the incidents of a battle.

"It commonly happens," says Mr. Kinglake,¹ "that incidents occurring in a battle are told by the most truthful bystanders with differences more or less wide." In the attack on the Great Redoubt in the Battle of the Alma, a young officer, Anstruther, rushed forward and planted the colours of the Royal Welsh—but where? Some distinctly remembered seeing him dig the butt-end of the flagstaff into the parapet: others as distinctly remembered seeing him fall several paces before he reached it. Similarly with the incidents of the death of the Prince Imperial near the Italezi Hills in the Zulu War. He was out as a volunteer with a reconnoitring party. They had off-saddled at a kraal and were resting, when a band of Zulus crept up through the long grass, and suddenly opened fire and made a rush forward. Our scouts at once took horse, as a reconnoitring party was bound to do, and scampered off, but the Prince was overtaken and killed. At the Court-Martial which ensued, the five troopers gave the most conflicting accounts of particulars which an unskilled investigator would think could not possibly have been mistaken by eye-witnesses of the same event. One said that the Prince had given the order to mount before the Zulus fired: another that he gave the order directly after: a third was positive that he never gave the order at all, but that it was given after the surprise by the officer in command. One said that he saw the Prince vault into the saddle as he gave the order: another that his horse bolted as he laid hold of the saddle, and that he ran alongside trying to get up.

The evidence before any Court of Inquiry into an exciting occurrence is almost certain to reveal similar discrepancies. But what we find it hard to realise is that we ourselves can possibly be mistaken in what we have a distinct and positive recollection of having seen. It once happened to myself in a London street to see a drunken woman thrown under a cab by her husband. Two cabs were running along, a four-wheeler and a hansom: the woman staggered almost under the first, and was thrown under the second. As it happened the case never got beyond the police station to which the parties were conveyed after fierce opposition from some neighbours, who sympathised entirely with the man. The woman herself, when her wounds were dressed, acknowledged the justice of her punishment, and refused to charge her husband. I was all the more willing to acquiesce in this because I found that while I had the most distinct impression of having seen the four-wheeler run over the woman's body, and should have been obliged to swear accordingly, there could be no doubt that it was really the hansom that had done so. This was not only the evidence of the neighbours, which I suspected at the time of being a trick, but of the cabdriver, who had stopped at the moment to abide the results of the accident. I afterwards had the curiosity to ask an eminent police magistrate, Sir John Bridge, whether this illusion of memory on my part—which I can only account for by supposing that my eyes had been fixed on the sufferer and that I had unconsciously referred her injuries to the heavier vehicle—would have entirely discredited my testimony in his Court. His answer was that it would not; that he was constantly meeting with such errors, and that if he found a number of witnesses of the same occurrence exactly agreed in every particular, he would suspect that they had talked the matter over and agreed upon what they were to say. This was the opinion of an experienced judge, a skilled critic of the defects of personal observation. An Old Bailey counsel for the defence, who is equally acquainted with the weakness of human memory, takes advantage of the fact that it is not generally understood by a Jury, and makes the fallacious assumption that glaring discrepancies are irreconcilable with the good faith of the witnesses who differ.²

II.—Tradition.—Hearsay Evidence.

Next in value to personal observation, we must place the report, oral or written, of an eye-witness. This is the best evidence we can get if we have not witnessed an occurrence ourselves. Yet Courts of Law, which in consideration of the defects of personal observation require more than one witness to establish the truth, exclude hearsay evidence altogether in certain cases, and not without reason.

In hearing a report we are in the position of observers of a series of significant sounds, and we are subject to all the fallacies of observation already mentioned. In an aggravated degree, for words are harder to observe than visible things. Our attention is apt to be more listless than in presence of the actual events. Our minds dwell upon parts of the narrative to the neglect of other parts, and in the coherent story or description that we retain in our memories, sequences are apt to be altered and missing links supplied in accordance with what we were predisposed to hear. Thus hearsay evidence is subject to all the imperfections of the original observer, in addition to the still more insidious imperfections of the second observer.

How quickly in the course of a few such transmissions hearsay loses all evidentiary value is simply illustrated by the game known as Russian Scandal. One of a company, A, writes down a short tale or sketch, and reads it to B. B repeats it to C, C to D, and so on. When it has thus gone the round of the company, the last hearer writes down his version, and it is compared with the original. With every willingness to play fair, the changes are generally considerable and significant.

Sometimes it is possible to compare an oral tradition with a contemporary written record. In one of Mr. Hayward's Essays—"The Pearls and Mock Pearls of History"—there are some examples of this disenchanting process. There is, for instance, a pretty story of an exchange of courtesies between the leaders of the French and English Guards at the battle of Fontenoy. The tradition runs that Lord Charles Hay stepped in front of his men and invited the French Guards to fire, to which M. d'Auteroche with no less chivalry responded: "Monsieur, we never fire first; you fire". What really passed we learn from a letter from Lord Charles Hay to his mother, which happens to have been preserved. "I advanced before our regiment, and drank to the Frenchmen, and told them we were the English Guards, and hoped they would stand till we came, and not swim the Scheldt as they did the Maine at Dettingen." Tradition has changed this lively piece of buffoonery into an act of stately and romantic courtesy. The change was probably made quite unconsciously by some tenth or hundredth transmitter, who remembered only part of the story, and dressed the remainder to suit his own fancy.

The question has been raised, For how long can oral tradition be trusted? Newton was of opinion that it might be trusted for eighty years after the event. Others have named forty years. But if this means that we may believe a story that we find in circulation forty years after the alleged events, it is wildly extravagant. It does injustice to the Mythopoeic Faculty of man. The period of time that suffices for the creation of a full-blown myth, must be measured by hours rather than by years. I will give an instance from my own observation, if that has not been entirely discredited by my previous confessions. The bazaars of the East are generally supposed to be the peculiar home of myth, hotbeds in which myths grow with the most amazing speed, but the locality of my myth is Aberdeen. In the summer of 1887 our town set up in one of its steeples a very fine carillon of Belgian bells. There was much public excitement over the event: the descriptions of enthusiastic promoters had prepared us to hear silvery music floating all over the town and filling the whole air. On the day fixed for the inauguration, four hours after the time announced for the first ceremonial peal, not having heard the bells, I was in a shop and asked if anything had happened to put off the ceremony. "Yes," I was told; "there had been an accident; they had not been properly hung, and when the wife of the Lord Provost had taken hold of a string to give the first pull, the whole machinery had come down." As a matter of fact all that had happened was that the sound of the bells was faint, barely audible a hundred yards from the belfry, and not at all like what had been expected. There were hundreds of people in the streets, and the myth had originated somehow among those who had not heard what they went out to hear. The shop where it was repeated circumstantially to me was in the main street, not more than a quarter of a mile from where the carillon had been played in the hearing of a large but disappointed crowd. I could not help reflecting that if I had been a mediÆval chronicler, I should have gone home and recorded the story, which continued to circulate for some days in spite of the newspapers: and two hundred years hence no historian would have ventured to challenge the truth of the contemporary evidence.

III.—Method of Testing Traditional Evidence.

It is obvious that the tests applied to descriptive testimony in Courts of Law cannot be applied to the assertions of History. It is a supreme canon of historical evidence that only the statements of contemporaries can be admitted: but most even of their statements must rest on hearsay, and even when the historian professes to have been an eye-witness, the range of his observation is necessarily limited, and he cannot be put into the witness-box and cross-examined. Is there then no way of ascertaining historical fact? Must we reject history as altogether unworthy of credit?

The rational conclusion only is that very few facts can be established by descriptive testimony such as would satisfy a Court of Law. Those who look for such ascertainment are on a wrong track, and are doomed to disappointment. It is told of Sir Walter Raleigh that when he was writing his History of the World, he heard from his prison in the Tower a quarrel outside, tried to find out the rights and the wrongs and the course of it, and failing to satisfy himself after careful inquiry, asked in despair how he could pretend to write the history of the world when he could not find out the truth about what occurred under his own windows. But this was really to set up an impossible standard of historical evidence.

The method of testing historical evidence follows rather the lines of the Newtonian method of Explanation, which we shall afterwards describe. We must treat any historical record as being itself in the first place a fact to be explained. The statement at least is extant: our first question is, What is the most rational way of accounting for it? Can it be accounted for most probably by supposing the event stated to have really occurred with all the circumstances alleged? Or is it a more probable hypothesis that it was the result of an illusion of memory on the part of the original observer, if it professes to be the record of an eye-witness, or on the part of some intermediate transmitter, if it is the record of a tradition? To qualify ourselves to answer the latter kind of question with reasonable probability we must acquaint ourselves with the various tendencies to error in personal observation and in tradition, and examine how far any of them are likely to have operated in the given case. We must study the operation of these tendencies within our experience, and apply the knowledge thus gained. We must learn from actual observation of facts what the Mythopoeic Faculty is capable of in the way of creation and transmutation, and what feats are beyond its powers, and then determine with as near a probability as we can how far it has been active in the particular case before us.

Footnote 1: The Invasion of the Crimea, iii. 124

Footnote 2: The truth is, that we see much less than is commonly supposed. Not every impression is attended to that is made on the retina, and unless we do attend we cannot, properly speaking, be said to see. Walking across to college one day, I was startled by seeing on the face of a clock in my way that it was ten minutes to twelve, whereas I generally passed that spot about twenty minutes to twelve. I hurried on, fearing to be late, and on my arrival found myself in very good time. On my way back, passing the clock again, I looked up to see how much it was fast. It marked ten minutes to eight. It had stopped at that time. When I passed before I had really seen only the minute hand. The whole dial must have been on my retina, but I had looked at or attended to only what I was in doubt about, taking the hour for granted. I am bound to add that my business friends hint that it is only absorbed students that are capable of such mistakes, and that alert men of business are more circumspect. That can only be because they are more alive to the danger of error.

Chapter III.

ASCERTAINMENT OF FACTS OF CAUSATION.

I.—Post Hoc ergo Propter Hoc.

One of the chief contributions of the Old Logic to Inductive Method was a name for a whole important class of misobservations. The fallacy entitled Post Hoc ergo Propter Hoc—"After, therefore, Because of"—consisted in alleging mere sequence as a proof of consequence or causal sequence. The sophist appeals to experience, to observed facts: the sequence which he alleges has been observed. But the appeal is fallacious: the observation on which he relies amounts only to this, that the one event has followed upon the other. This much must be observable in all cases of causal sequence, but it is not enough for proof. Post hoc ergo propter hoc may be taken as a generic name for imperfect proof of causation from observed facts of succession.

The standard example of the fallacy is the old Kentish peasant's argument that Tenterden Steeple was the cause of Goodwin Sands. Sir Thomas More (as Latimer tells the story in one of his Sermons to ridicule incautious inference) had been sent down into Kent as a commissioner to inquire into the cause of the silting up of Sandwich Haven. Among those who came to his court was the oldest inhabitant, and thinking that he from his great age must at least have seen more than anybody else, More asked him what he had to say as to the cause of the sands. "Forsooth, sir," was the greybeard's answer, "I am an old man: I think that Tenterden Steeple is the cause of Goodwin Sands. For I am an old man, and I may remember the building of Tenterden Steeple, and I may remember when there was no steeple at all there. And before that Tenterden Steeple was in building, there was no manner of speaking of any flats or sands that stopped the haven; and, therefore, I think that Tenterden Steeple is the cause of the destroying and decaying of Sandwich Haven."

This must be taken as Latimer meant it to be, as a ridiculous example of a purely imbecile argument from observation, but the appeal to experience may have more show of reason and yet be equally fallacious. The believers in Kenelm Digby's "Ointment of Honour" appealed to experience in support of its efficacy. The treatment was to apply the ointment, not to the wound, but to the sword that had inflicted it, to dress this carefully at regular intervals, and, meantime, having bound up the wound, to leave it alone for seven days. It was observed that many cures followed upon this treatment. But those who inferred that the cure was due to the bandaging of the sword, failed to observe that there was another circumstance that might have been instrumental, namely, the exclusion of the air and the leaving of the wound undisturbed while the natural healing processes went on. And it was found upon further observation that binding up the wound alone answered the purpose equally well whether the sword was dressed or not.

In cases where post hoc is mistaken for propter hoc, simple sequence for causal sequence, there is commonly some bias of prejudice or custom which fixes observation on some one antecedent and diverts attention from other circumstances and from what may be observed to follow in other cases. In the minds of Digby and his followers there was probably a veneration for the sword as the weapon of honour, and a superstitious belief in some secret sympathy between the sword and its owner. So when the practice of poisoning was common, and suspicion was flurried by panic fear, observation was often at fault. Pope Clement VIII. was said to have been killed by the fumes of a poisoned candle which was placed in his bedroom. Undoubtedly candles were there, but those who attributed the Pope's death to them took no notice of the fact that a brazier of burning charcoal was at the same time in the apartment with no sufficient outlet for its fumes. Prince Eugene is said to have received a poisoned letter, which he suspected and immediately threw from him. To ascertain whether his suspicions were well founded the letter was administered to a dog, which, to make assurance doubly sure, was fortified by an antidote. The dog died, but no inquiry seems to have been made into the character of the antidote.

Hotspur's retort to Glendower showed a sound sense of the true value to be attached to mere priority.

We all admit at once that the retort was just. What principle of sound conclusion was involved in it? It is the business of Inductive Logic to make such principles explicit.

Taking Post Hoc ergo Propter Hoc as a generic name for fallacious arguments of causation based on observed facts, for the fallacious proof of causation from experience, the question for Logic is, What more than mere sequence is required to prove consequence? When do observations of Post Hoc warrant the conclusion Propter Hoc?

II.—Meaning of "Cause".—Methods of Observation—Mill's Experimental Methods.

The methods formulated by Mill under the name of Experimental Methods are methods actually practised by men of science with satisfactory results, and are perfectly sound in principle. They were, indeed, in substance, taken by him from the practice of the scientific laboratory and study as generalised by Herschel. In effect what Mill did was to restate them and fit them into a system. But the controversies into which he was tempted in so doing have somewhat obscured their exact function in scientific inquiry. Hostile critics, finding that they did not serve the ends that he seemed to claim for them, have jumped to the conclusion that they are altogether illusory and serve no purpose at all.

First, we must dismiss the notion, encouraged by Mill's general theory of Inference, that the Experimental Methods have anything special to do with the observation and inferential extension of uniformities such as that death is common to all organised beings. One of the Methods, as we shall see, that named by Mill the Method of Agreement, does incidentally and collaterally establish empirical laws in the course of its observations, and this probably accounts for the prominence given to it in Mill's system. But this is not its end and aim, and the leading Method, that named by him the Method of Difference, establishes as fact only a particular case of causal coincidence. It is with the proof of theories of causation that the Experimental Methods are concerned: they are methods of observing with a view to such proof.¹

The next point to be made clear is that the facts of causation with which the Methods are concerned are observable facts, relations among phenomena, but that the causal relations or conditions of which they are the proof are not phenomena, in the meaning of being manifest to the senses, but rather noumena, inasmuch as they are reached by reasoning from what is manifest.

Take, for example, what is known as the quaquaversus principle in Hydrostatics, that pressure upon a liquid is propagated equally in all directions. We cannot observe this extension of pressure among the liquid particles directly. It cannot be traced among the particles by any of our senses. But we can assume that it is so, consider what ought to be visible if it is so, and then observe whether the visible facts are in accordance with the hypothesis. A box can be made, filled with water, and so fitted with pistons on top and bottom and on each of its four sides that they will indicate the amount of pressure on them from within. Let pressure then be applied through a hole in the top, and the pistons show that it has been communicated to them equally. The application of the pressure and the yielding of the pistons are observable facts, facts in causal sequence: what happens among the particles of the liquid is not observed but reasonably conjectured, is not phenomenal but noumenal.

This distinction, necessary to an understanding of the scope of the Methods, was somewhat obscured by Mill in his preliminary discussion of the meaning of "cause". Very rightly, though somewhat inconsistently with his first theory of Induction, he insists that "the notion of Cause being the root of the whole theory of Induction, it is indispensable that this idea should at the very outset of our inquiry be, with the utmost practicable degree of precision, fixed and determined". But in this determination, not content with simply recognising that it is with phenomena that the Experimental Methods primarily deal, it being indeed only phenomena that can be the subjects of experimental management and observation, he starts by declaring that science has not to do with any causes except such as are phenomenal—"when I speak of the cause of any phenomenon, I do not mean a cause which is not itself a phenomenon"—and goes on to define as the only correct meaning of cause "the sum total of conditions," including among them conditions which are not phenomenal, in the sense of being directly open to observation.

When Mill protested that he had regard only to phenomenal causes, he spoke as the partisan of a philosophical tradition. It would have been well if he had acted upon his own remark that the proper understanding of the scientific method of investigating cause is independent of metaphysical analysis of what cause means. Curiously enough, this remark is the preface to an analysis of cause which has but slight relevance to science, and is really the continuation of a dispute begun by Hume. This is the key to his use of the word phenomenon: it must be interpreted with reference to this: when he spoke of causes as phenomenal, he opposed the word to "occult" in some supposed metaphysical sense.² And this irrelevant discussion, into the vortex of which he allowed himself to be carried, obscured the fact, elsewhere fully recognised by Mill himself, that science does attempt to get beyond phenomena at ultimate laws which are not themselves phenomena though they bind phenomena together. The "colligation" of the facts, to use Whewell's phrase, is not a phenomenon, but a noumenon.

The truth is that a very simple analysis of "cause" is sufficient for the purposes of scientific inquiry. It is enough to make sure that causal sequence or consequence shall not be confounded with simple sequence. Causal sequence is simple sequence and something more, that something more being expressed by calling it causal. What we call a cause is not merely antecedent or prior in time to what we call its effect: it is so related to the effect that if it or an equivalent event had not happened the effect would not have happened. Anything in the absence of which a phenomenon would not have come to pass as it did come to pass is a cause in the ordinary sense. We may describe it as an indispensable antecedent, with this reservation (which will be more fully understood afterwards), that if we speak of a general effect, such as death, the antecedents must be taken with corresponding generality.

It is misleading to suggest, as Mill does, by defining cause as "the sum total of conditions"—a definition given to back up his conception of cause as phenomenal—that science uses the word cause in a different meaning from that of ordinary speech. It is quite true that "the cause, philosophically speaking, is the sum total of the conditions, positive and negative, taken together: the whole of the contingencies of every description, which being realised, the consequent invariably follows". But this does not imply any discrepancy between the scientific or philosophical meaning and the ordinary meaning. It is only another way of saying that the business of science or philosophy is to furnish a complete explanation of an event, an account of all its indispensable antecedents. The plain man would not refuse the name of cause to anything that science or philosophy could prove to be an indispensable antecedent, but his interest in explanation is more limited. It is confined to what he wants to know for the purpose he has in hand. Nor could the man of science consistently refuse the name of cause to what the plain man applies it to, if it really was something in consequence of which the event took place. Only his interest in explanation is different. The indispensable antecedents that he wants to know may not be the same. Science or philosophy applies itself to the satisfaction of a wider curiosity: it wants to know all the causes, the whole why, the sum total of conditions. To that end the various departments of science interest themselves in various species of conditions. But all understand the word cause in the ordinary sense.

We must not conclude from accidental differences in explanation or statement of cause, dependent on the purpose in view, that the word Cause is used in different senses. In answering a question as to the cause of anything, we limit ourselves to what we suppose our interrogator to be ignorant of and desirous of knowing. If asked why the bells are ringing, we mention a royal marriage, or a victory, or a church meeting, or a factory dinner hour, or whatever the occasion may be. We do not consider it necessary to mention that the bells are struck by a clapper. Our hearer understands this without our mentioning it. Nor do we consider it necessary to mention the acoustic condition, that the vibration of the bells is communicated to our ears through the air, or the physiological condition, that the vibrations in the drums of our ears are conveyed by a certain mechanism of bone and tissue to the nerves. Our hearer may not care to know this, though quite prepared to admit that these conditions are indispensable antecedents. Similarly, a physiographer, in stating the cause of the periodical inundation of the Nile, would consider it enough to mention the melting of snow on the mountains in the interior of Africa, without saying anything of such conditions as the laws of gravity or the laws of liquefaction by heat, though he knows that these conditions are also indispensable. Death is explained by the doctor when referred to a gunshot wound, or a poison, or a virulent disease. The Pathologist may inquire further, and the Moral Philosopher further still. But all inquiries into indispensable conditions are inquiries into cause. And all alike have to be on their guard against mistaking simple sequence for consequence.

To speak of the sum total of conditions, as the Cause in a distinctively scientific sense, is misleading in another direction. It rather encourages the idea that science investigates conditions in the lump, merely observing the visible relations between sets of antecedents and their consequents. Now this is the very thing that science must avoid in order to make progress. It analyses the antecedent situation, tries to separate the various coefficients, and finds out what they are capable of singly. It must recognise that some of the antecedents of which it is in search are not open to observation. It is these, indeed, for the most part that constitute the special subject-matter of the sciences in Molar as well as in Molecular Physics. For practical every-day purposes, it is chiefly the visible succession of phenomena that concerns us, and we are interested in the latent conditions only in as far as they provide safer ground for inference regarding such visible succession. But to reach the latent conditions is the main work of science.

It is, however, only through observation of what is open to the senses that science can reach the underlying conditions, and, therefore, to understand its methods we must consider generally what is open to observation in causal succession. What can be observed when phenomena follow one another as cause and effect, that is, when the one happens in consequence of the happening of the other? In Hume's theory, which Mill formally adopted with a modification,³ there is nothing observable but the constancy or invariability of the connexion. When we say that Fire burns, there is nothing to be observed except that a certain sensation invariably follows upon close proximity to fire. But this holds good only if our observation is arbitrarily limited to the facts enounced in the expression. If this theory were sound, science would be confined to the observation of empirical laws. But that there is something wrong with it becomes apparent when we reflect that it has been ascertained beyond doubt that in many observed changes, and presumably in all, there is a transference of energy from one form to another. The paralogism really lies in the assumption from which Hume deduced his theory, namely, that every idea is a copy of some impression. As a matter of fact, we have ideas that are not copies of any one impression, but a binding together, colligation, or intellection of several impressions. Psychological analysis shows us that even when we say that things exist with certain qualities, we are expressing not single impressions or mental phenomena, but supposed causes and conditions of such, noumena in short, which connect our recollections of many separate impressions and expectations of more.

The Experimental Methods proceed on the assumption that there is other outward and visible evidence of causal connexion than invariability of sequence. In the leading Method it is assumed that when events may be observed to follow one another in a certain way, they are in causal sequence. If we can make sure that an antecedent change is the only change that has occurred in an antecedent situation, we have proof positive that any immediately subsequent change in the situation is a consequent, that the successive changes are in causal sequence. Thus when Pascal's barometer was carried to the top of Puy le Dome, and the mercury in it fell, the experimenters argued that the fall of the mercury was causally connected with the change of elevation, all the other circumstances remaining the same. This is the foundation of the so-called Method of Difference. To determine that the latent condition was a difference in the weight of the atmosphere, needed other observations, calculations and inferences; but if it could be shown that the elevation was the only antecedent changed in a single instance, causal connexion was established between this and the phenomenon of the fall of the barometer.

It is obvious that in coming to this conclusion we assume what cannot be demonstrated but must simply be taken as a working principle to be confirmed by its accordance with experience, that nothing comes into being without some change in the antecedent circumstances. This is the assumption known as the Law of Causation—ex nihilo nihil fit.

Again, certain observable facts are taken as evidence that there is no causal connexion. On the assumption that any antecedent in whose absence a phenomenon takes place is not causally connected with it, we set aside or eliminate various antecedents as fortuitous or non-causal. This negative principle, as we shall see, is the foundation of what Mill called the Method of Agreement.

Be it remarked, once for all, that before coming to a conclusion on the Positive Method or Method of Difference, we may often have to make many observations on the Negative Method. Thus Pascal's experimenters, before concluding that the change of altitude was the only influential change, tried the barometer in exposed positions and in sheltered, when the wind blew and when it was calm, in rain and in fog, in order to prove that these circumstances were indifferent. We must expound and illustrate the methods separately, but every method known to science may have in practice to be employed in arriving at a single conclusion.

Footnote 1: This is implied, as I have already remarked, in the word Experimental. An experiment is a proof or trial: of what? Of a theory, a conjecture.

Footnote 2: If we remember, as becomes apparent on exact psychological analysis, that things and their qualities are as much noumena and not, strictly speaking, phenomena as the attraction of gravity or the quaquaversus principle in liquid pressure, the prejudice against occultism is mitigated.

Footnote 3: The modification was that causation is not only "invariable" but also "unconditional" sequence. This addition of unconditionality as part of the meaning of cause, after defining cause as the sum total of the conditions, is very much like arguing in a circle. After all, the only point recognised in the theory as observable is the invariability of the sequence. But this is less important than the fact that in his canons of the Experimental Methods Mill recognised that more is observable.

Chapter IV.

METHODS OF OBSERVATION.—SINGLE DIFFERENCE.

I.—The Principle of Single Difference.— Mill's "Canon".

On what principle do we decide, in watching a succession of phenomena, that they are connected as cause and effect, that one happened in consequence of the happening of another? It may be worded as follows:—

When the addition of an agent is followed by the appearance or its subtraction by the disappearance of a certain effect, no other influential circumstance having been added or subtracted at the same time or in the meantime, and no change having occurred among the original circumstances, that agent is a cause of the effect.

On this principle we would justify our belief in the causal properties of common things—that fire burns, that food appeases hunger, that water quenches thirst, that a spark ignites gunpowder, that taking off a tight shoe relieves a pinched foot. We have observed the effect following when there was no other change in the antecedent circumstances, when the circumstance to which we refer it was simply added to or subtracted from the prior situation.

Suppose we doubt whether a given agent is or is not capable of producing a certain effect in certain circumstances, how do we put it to the proof? We add it singly or subtract it singly, taking care that everything else remains as before, and watch the result. If we wish to know whether a spoonful of sugar can sweeten a cup of tea, we taste the tea without the sugar, then add the sugar, and taste again. The isolated introduction of the agent is the proof, the experiment. If we wish to know whether a pain in the foot is due to a tight lacing, we relax the lacing and make no other change: if the pain then disappears, we refer it to the lacing as the cause. The proof is the disappearance of the pain on the subtraction of the single antecedent.

The principle on which we decide that there is causal connexion is the same whether we make the experimental changes ourselves or merely watch them as they occur—the only course open to us with the great forces of nature which are beyond the power of human manipulation. In any case we have proof of causation when we can make sure that there was only one difference in the antecedent circumstances corresponding to the difference of result.

Mill's statement of this principle, which he calls the Canon of the Method of Difference, is somewhat more abstract, but the proof relied upon is substantially the same.

If an instance in which the phenomenon under investigation occurs, and an instance in which it does not occur, have every circumstance in common save one, that one occurring only in the former, the circumstance in which alone the two instances differ is [the effect, or]¹ the cause, or an indispensable part of the cause, of the phenomenon.

Mill's statement has the merit of exactness, but besides being too abstract to be easy of application, the canon is apt to mislead in one respect. The wording of it suggests that the two instances required must be two separate sets of circumstances, such as may be put side by side and compared, one exhibiting the phenomenon and the other not. Now in practice it is commonly one set of circumstances that we observe with a special circumstance introduced or withdrawn: the two instances, the data of observation, are furnished by the scene before and the scene after the experimental interference. In the case, for example, of a man shot in the head and falling dead, death being the phenomenon in question, the instance where it does not occur is the man's condition before he received the wound, and the instance where it does occur is his condition after, the single circumstance of difference being the wound, a difference produced by the addition or introduction of a new circumstance. Again, take the common coin and feather experiment, contrived to show that the resistance of the air is the cause of the feather's falling to the ground more slowly than the coin. The phenomenon under investigation is the retardation of the feather. When the two are dropped simultaneously in the receiver of an air-pump, the air being left in, the feather flutters to the ground after the coin. This is the instance where the phenomenon occurs. Then the air is pumped out of the receiver, and the coin and the feather being dropped at the same instant reach the ground together. This is the instance where the phenomenon does not occur. The single circumstances of difference is the presence of air in the former instance, a difference produced by the subtraction of a circumstance.

Mill's Canon is framed so as to suit equally whether the significant difference is produced by addition to or subtraction from an existing sum of circumstances. But that is misleading in so far as it suggests that the two instances must be separate sets of circumstances, is shown by the fact that it misled himself when he spoke of the application of the method in social investigations, such as the effect of Protection on national wealth. "In order," he says, "to apply to the case the most perfect of the methods of experimental inquiry, the Method of Difference, we require to find two instances which tally in every particular except the one which is the subject of inquiry. We must have two nations alike in all natural advantages and disadvantages; resembling each other in every quality physical and moral; habits, usages, laws, and institutions, and differing only in the circumstance that the one has a prohibitory tariff and the other has not." It being impossible ever to find two such instances, he concluded that the Method of Difference could not be applied in social inquiries. But really it is not necessary in order to have two instances that we should have two different nations: the same nation before and after a new law or institution fulfils that requirement. The real difficulty, as we shall see, is to satisfy the paramount condition that the two instances shall differ in a single circumstance. Every new enactment would be an experiment after the Method of Difference, if all circumstances but it remained the same till its results appeared. It is because this seldom or never occurs that decisive observation is difficult or impossible, and the simple method of difference has to be supplemented by other means.

To introduce or remove a circumstance singly is the typical application of the principle; but it may be employed also to compare the effects of different agents, each added alone to exactly similar circumstances. A simple example is seen in Mr. Jamieson's agricultural experiments to determine the effects of different manures, such as coprolite and superphosphate, on the growth of crops. Care is taken to have all the antecedent circumstances as exactly alike as possible, except as regards the agency whose effects are to be observed. A field is chosen of uniform soil and even exposure and divided into plots: it is equally drained so as to have the same degree of moisture throughout; the seed is carefully selected for the whole sowing. Between the sowing and the maturing of the crop all parts of the field are open to the same weather. Each plot may thus be regarded as practically composing the same set of conditions, and any difference in the product may with reasonable probability be ascribed to the single difference in the antecedents, the manures which it is desired to compare.

II.—Application of the Principle.

The principle of referring a phenomenon to the only immediately preceding change in antecedent circumstances that could possibly have affected it, is so simple and so often employed by everybody every day, that at first we do not see how there can be any difficulty about it or any possibility of error. And once we understand how many difficulties there are in reaching exact knowledge even on this simple principle, and what care has to be taken, we are apt to overrate its value, and to imagine that it carries us further than it really does. The scientific expert must know how to apply this principle, and a single application of it with the proper precautions may take him days or weeks, and yet all that can be made good by it may carry but a little way towards the knowledge of which he is in search.

When the circumstances are simple and the effect follows at once, as when hot water scalds, or a blow with a stick breaks a pane of glass, there can be no doubt of the causal connexion so far, though plenty of room for further inquiry into the why. But the mere succession of phenomena may be obscure. We may introduce more than one agent without knowing it, and if some time elapses between the experimental interference and the appearance of the effect, other agents may come in without our knowledge.

We must know exactly what it is that we introduce and all the circumstances into which we introduce it. We are apt to ignore the presence of antecedents that are really influential in the result. A man heated by work in the harvest field hastily swallows a glass of water, and drops down dead. There is no doubt that the drinking of the water was a causal antecedent, but the influential circumstance may not have been the quantity or the quality of the liquid but its temperature, and this was introduced into the situation as well as a certain amount of the liquid components. In making tea we put in so much tea and so much boiling water. But the temperature of the pot is also an influential circumstance in the resulting infusion. So in chemical experiments, where one might expect the result to depend only upon the proportions of the ingredients, it is found that the quantity is also influential, the degree of heat evolved entering as a factor into the result. Before we can apply the principle of single difference, we must make sure that there is really only a single difference between the instances that we bring into comparison.

The air-pump was invented shortly before the foundation of the Royal Society, and its members made many experiments with this new means of isolating an agent and thus discovering its potentialities. For example, live animals were put into the receiver, and the air exhausted, with the result that they quickly died. The absence of the air being the sole difference, it was thus proved to be indispensable to life. But air is a composite agent, and when means were contrived of separating its components, the effects of oxygen alone and of carbonic acid alone were experimentally determined.

A good example of the difficulty of excluding agencies other than those we are observing, of making sure that none such intrude, is found in the experiments that have been made in connexion with spontaneous generation. The question to be decided is whether life ever comes into existence without the antecedent presence of living germs. And the method of determining this is to exclude all germs rigorously from a compound of inorganic matter, and observe whether life ever appears. If we could make sure in any one case that no germs were antecedently present, we should have proved that in that case at least life was spontaneously generated.

The difficulty here arises from the subtlety of the agent under observation. The notion that maggots are spontaneously generated in putrid meat, was comparatively easy to explode. It was found that when flies were excluded by fine wire-gauze, the maggots did not appear. But in the case of microscopic organisms proof is not so easy. The germs are invisible, and it is difficult to make certain of their exclusion. A French experimenter, Pouchet, thought he had obtained indubitable cases of spontaneous generation. He took infusions of vegetable matter, boiled them to a pitch sufficient to destroy all germs of life, and hermetically sealed up the liquid in glass flasks. After an interval, micro-organisms appeared. Doubts as to the conclusion that they had been spontaneously generated turned upon two questions: whether all germs in the liquid had been destroyed by the preliminary boiling, and whether germs could have found access in the course of the interval before life appeared. At a certain stage in Pouchet's process he had occasion to dip the mouths of the flasks in mercury. It occurred to Pasteur in repeating the experiments that germs might have found their way in from the atmospheric dust on the surface of this mercury. That this was so was rendered probable by his finding that when he carefully cleansed the surface of the mercury no life appeared afterwards in his flasks.

The application of the principle in human affairs is rendered uncertain by the immense complication of the phenomena, the difficulty of experiment, and the special liability of our judgments to prejudice. That men and communities of men are influenced by circumstances is not to be denied, and the influence of circumstances, if it is to be traced at all, must be traced through observed facts. Observation of the succession of phenomena must be part at least of any method of tracing cause and effect. We must watch what follows upon the addition of new agencies to a previously existing sum. But we can seldom or never get a decisive observation from one pair of instances, a clear case of difference of result preceded by a single difference in the antecedents. The simple Method of Experimental Addition or Subtraction is practically inapplicable. We can do nothing with a man analogous to putting him into a hermetically sealed retort. Any man or any community that is the subject of our observations must be under manifold influences. Each of them probably works some fraction of the total change observable, but how are they to be disentangled? Consider, for example, how impossible it would be to prove in an individual case, on the strict principle of Single Difference, that Evil communications corrupt good manners. Moral deterioration may be observed following upon the introduction of an evil companion, but how can we make sure that no other degrading influence has operated, and that no original depravity has developed itself in the interval? Yet such propositions of moral causation can be proved from experience with reasonable probability. Only it must be by more extended observations than the strict Method of Difference takes into account. The method is to observe repeated coincidences between evil companionship and moral deterioration, and to account for this in accordance with still wider observations of the interaction of human personalities.

For equally obvious reasons the simple Method of Difference is inapplicable to tracing cause and effect in communities. Every new law or repeal of an old law is the introduction of a new agency, but the effects of it are intermixed with the effects of other agencies that operate at the same time. Thus Professor Cairnes remarks, concerning the introduction of a high Protective Tariff into the United States in 1861, that before its results could appear in the trade and manufacture of the States, there occurred (1) The great Civil War, attended with enormous destruction of capital; (2) Consequent upon this the creation of a huge national debt, and a great increase of taxation; (3) The issue of an inconvertible paper currency, deranging prices and wages; (4) The discovery of great mineral resources and oil-springs; (5) A great extension of railway enterprise. Obviously in such circumstances other methods than the Method of Difference must be brought into play before there can be any satisfactory reasoning on the facts observed. Still what investigators aim at is the isolation of the results of single agencies.

Footnote 1: Prof. Bain, who adopts Mill's Canon, silently drops the words within brackets. They seem to be an inadvertence. The "circumstance," in all the examples that Mill gives, is an antecedent circumstance. Herschel's statement, of which Mill's is an adaptation, runs as follows: "If we can either find produced by nature, or produce designedly for ourselves, two instances which agree exactly in all but one particular and differ in that one, its influence in producing the phenomenon, if it have any, must thereby be rendered apparent".

Chapter V.

METHODS OF OBSERVATION.—ELIMINATION.—SINGLE AGREEMENT.

I.—The Principle of Elimination.

The essence of what Mill calls the Method of Agreement is really the elimination¹ of accidental, casual, or fortuitous antecedents. It is a method employed when we are given an effect and set to work to discover the cause. It is from the effect that we start and work back. We make a preliminary analysis of the antecedents; call the roll, as it were, of all circumstances present before the effect appeared. Then we proceed to examine other instances of the same effect, and other instances of the occurrence of the various antecedents, and bring to bear the principle that any antecedent in the absence of which the effect has appeared or on the presence of which it has not appeared may be set aside as fortuitous, as being not an indispensable antecedent. This is really the guiding principle of the method as a method of observation.

Let the inquiry, for example, be into the cause of Endemic Goitre. Instances of the disease have been collected from the medical observations of all countries over many years. Why is it endemic in some localities and not in others? We proceed on the assumption that the cause, whatever it is, must be some circumstance common to all localities where it is endemic. If any such circumstance is obvious at once, we may conclude on the mere principle of repeated coincidence that there is causal connexion between it and the disease, and continue our inquiry into the nature of the connexion. But if no such circumstance is obvious, then in the course of our search for it we eliminate, as fortuitous, conditions that are present in some cases but absent in others. One of the earliest theories was that endemic goitre was connected with the altitude and configuration of the ground, some notorious centres of it being deeply cleft mountain valleys, with little air and wind and damp marshy soil. But wider observation found it in many valleys neither narrower nor deeper than others that were exempt, and also in wide exposed valleys such as the Aar. Was it due to the geological formation? This also had to be abandoned, for the disease is often incident within very narrow limits, occurring in some villages and sparing others though the geological formation is absolutely the same. Was it due to the character of the drinking-water? Especially to the presence of lime or magnesia? This theory was held strongly, and certain springs characterised as goitre-springs. But the springs in some goitre centres show not a trace of magnesia. The comparative immunity of coast regions suggested that it might be owing to a deficiency of iodine in the drinking-water and the air, and many instances were adduced in favour of this. But further inquiries made out the presence of iodine in considerable quantities, in the air, the water, and the vegetation of districts where goitre was widely prevalent; while in Cuba it is said that not a trace of iodine is discoverable either in the air or the water, and yet it is quite free from goitre. After a huge multiplication of instances, resulting in the elimination of every local condition that had been suggested as a possible cause, Hirsch came to the conclusion that the true cause must be a morbid poison, and that endemic goitre has to be reckoned among the infectious diseases.²

On this negative principle, that if a circumstance comes and goes without bringing the phenomenon in its train, the phenomenon is causally independent of it, common-sense is always at work disconnecting events that are occasionally coincident in time. A bird sings at our window, for example, and the clock ticks on the mantelpiece. But the clock does not begin to tick when the bird begins to sing, nor cease to tick when the bird flies away. Accordingly, if the clock should stop at any time, and we wished to inquire into the cause, and anybody were to suggest that the stoppage of the clock was caused by the stoppage of a bird's song outside, we should dismiss the suggestion at once. We should eliminate this circumstance from our inquiry, on the ground that from other observations we knew it to be a casual or fortuitous concomitant. Hotspur's retort to Glendover (p. 297) was based on this principle. When poetic sentiment or superstition rejects a verdict of common-sense or science, it is because it imagines a causal connexion to exist that is not open to observation, as in the case of the grandfather's clock which stopped short never to go again when the old man died.

The procedure in Mill's "Method of Agreement" consists in thus eliminating fortuitous antecedents or concomitants till only one remains. We see the nature of the proof relied upon when we ask, How far must elimination be carried in order to attain proof of causal connexion? The answer is that we must go on till we have eliminated all but one. We must multiply instances of the phenomenon, till we have settled of each of the antecedents except one that it is not the cause. We must have taken account of all the antecedents, and we must have found in our observations that all but one have been only occasionally present.

When all the antecedents of an effect except one can be absent without the disappearance of the effect, that one is causally connected with the effect, due precautions being taken that no other circumstances have been present besides those taken account of.

Mill's Canon of the Method of Agreement is substantially identical with this:—

When two or more instances of the phenomenon under investigation have only one circumstance in common, the circumstance in which alone all the instances agree is the cause (or effect) of the given phenomenon.

Herschel's statement, on which this canon is founded, runs as follows: "Any circumstance in which all the facts without exception agree, may be the cause in question, or if not, at least a collateral effect of the same cause: if there be but one such point of agreement, the possibility becomes a certainty".

All the instances examined must agree in one circumstance—hence the title Method of Agreement. But it is not in the agreement merely that the proof consists, but the agreement in one circumstance combined with difference in all the other circumstances, when we are certain that every circumstance has come within our observation. It is the singleness of the agreement that constitutes the proof just as it is the singleness of the difference in the Method of Difference.³

It has been said that Mill's Method of Agreement amounts after all only to an uncontradicted Inductio per enumerationem simplicem, which he himself stigmatised as Induction improperly so called. But this is not strictly correct. It is a misunderstanding probably caused by calling the method that of agreement simply, instead of calling it the Method of Single Agreement, so as to lay stress upon the process of elimination by which the singleness is established. It is true that in the course of our observations we do perform an induction by simple enumeration. In eliminating, we at the same time generalise. That is to say, in multiplying instances for the elimination of non-causes, we necessarily at the same time multiply instances where the true causal antecedent, if there is only one possible, is present. An antecedent containing the true cause must always be there when the phenomenon appears, and thus we may establish by our eliminating observations a uniformity of connexion between two facts.

Take, for example, Roger Bacon's inquiry into the cause of the colours of the rainbow. His first notion seems to have been to connect the phenomenon with the substance crystal, probably from his thinking of the crystal firmament then supposed to encircle the universe. He found the rainbow colours produced by the passage of light through hexagonal crystals. But on extending his observations, he found that the passage of light through other transparent mediums was also attended by the phenomenon. He found it in dewdrops, in the spray of waterfalls, in drops shaken from the oar in rowing. He thus eliminated the substance crystal, and at the same time established the empirical law that the passage of light through transparent mediums of a globular or prismatic shape was a causal antecedent of the rainbow colours.⁴

Ascertainment of invariable antecedents may thus proceed side by side with that of variable antecedents, the use of the elimination being simply to narrow the scope of the inquiry. But the proof set forth in Mill's Canon does not depend merely on one antecedent or concomitant being invariably present, but also on the assumption that all the influential circumstances have been within our observation. Then only can we be sure that the instances have only one circumstance in common.

The truth is that owing to the difficulty of fulfilling this condition, proof of causation in accordance with Mill's Canon is practically all but impossible. It is not attained in any of the examples commonly given. The want of conclusiveness is disguised by the fact that both elimination and positive observation of mere agreement or uniform concomitance are useful and suggestive in the search for causes, though they do not amount to complete proof such as the Canon describes. Thus in the inquiry into the cause of goitre, the elimination serves some purpose though the result is purely negative. When the inquirer is satisfied that goitre is not originated by any directly observable local conditions, altitude, temperature, climate, soil, water, social circumstances, habits of exertion, his search is profitably limited. And mere frequency, much more constancy of concomitance, raises a presumption of causal connexion, and looking out for it is valuable as a mode of reconnoitring. The first thing that an inquirer naturally asks when confronted by numerous instances of a phenomenon is, What have they in common? And if he finds that they have some one circumstance invariably or even frequently present, although he cannot prove that they have no other circumstance in common as the Cannon of Single Agreement requires, the presumption of causal connexion is strong enough to furnish good ground for further inquiry. If an inquirer finds an illness with marked symptoms in a number of different households, and finds also that all the households get their milk supply from the same source, this is not conclusive proof of causation, but it is a sufficient presumption to warrant him in examining whether there is any virulent ingredient in the milk.

Thus varying the circumstances so as to bring out a common antecedent, though it does not end in exact proof, may indicate causal connexion though it does not prove what the nature of the connexion is. Roger Bacon's observations indicated that the production of rainbow colours was connected with the passage of light through a transparent globe or prism. It was reserved for Newton to prove by other methods that white light was composed of rays, and that those rays were differently refracted in passing through the transparent medium. We have another example of how far mere agreement, revealed by varying the circumstances, carries us towards discovery of the cause, in Wells's investigation of the cause of dew. Comparing the numerous instances of dew appearing without visible fall of moisture, Wells found that they all agreed in the comparative coldness of the surface dewed. This was all the agreement that he established by observation; he did not carry observation to the point of determining that there was absolutely no other common circumstance: when he had simply discovered dewed surfaces, he tried next to show by reasoning from other knows facts how the coldness of the surface affected the aqueous vapour of the neighbouring air. He did not establish his Theory of Dew by the Method of Agreement: but the observation of an agreement or common feature in a number of instances was a stage in the process by which he reached his theory.

III.—Mill's "Joint Method of Agreement and Difference".

After examining a variety of instances in which an effect appears, and finding that they all agree in the antecedent presence of some one circumstance, we may proceed to examine instances otherwise similar (in pari materia, as Prof. Fowler puts it) where the effect does not appear. If these all agree in the absence of the circumstance that is uniformly present with the effect, we have corroborative evidence that there is causal connexion between this circumstance and the effect.

The principle of this method seems to have been suggested to Mill by Wells's investigations into Dew. Wells exposed a number of polished surfaces of various substances, and compared those in which there was a copious deposit of dew with those in which there was little or none. If he could have got two surfaces, one dewed and the other not, identical in every concomitant but one, he would have attained complete proof on the principle of Single Difference. But this being impracticable, he followed a course which approximated to the method of eliminating every circumstance but one from instances of dew, and every circumstance but one in the instances of no-dew. Mill sums up as follows the results of his experiments: "It appears that the instances in which much dew is deposited, which are very various, agree in this, and, so far as we are able to observe, in this only, that they either radiate heat rapidly or conduct it slowly: qualities between which there is no other circumstance of agreement than that by virtue of either, the body tends to lose heat from the surface more rapidly than it can be restored from within. The instances, on the contrary, in which no dew, or but a small quantity of it, is formed, and which are also extremely various, agree (as far as we can observe) in nothing except in not having this same property. We seem therefore to have detected the characteristic difference between the substances on which the dew is produced, and those on which it is not produced. And thus have been realised the requisitions of what we have termed the Indirect Method of Difference, or the Joint Method of Agreement and Difference." The Canon of this Method is accordingly stated by Mill as follows:—

If two or more instances in which the phenomenon occurs have only one circumstance in common, while two or more instances in which it does not occur have nothing in common save the absence of that circumstance; the circumstance in which alone the two sets of instances differ, is the effect, or the cause, or an indispensable part of the cause, of the phenomenon.

In practice, however, this theoretical standard of proof is never attained. What investigators really proceed upon is the presumption afforded, to use Prof. Bain's terms, by Agreement in Presence combined with Agreement in Absence. When it is found that all substances which have a strong smell agree in being readily oxidisable, and that the marsh gas or carbonetted hydrogen which has no smell is not oxidisable at common temperatures, the presumption that oxidation is one of the causal circumstances in smell is strengthened, even though we have not succeeded in eliminating every circumstance but this one from either the positive or the negative instances. So in the following examples given by Prof. Fowler there is not really a compliance with the theoretical requirements of Mill's Method: there is only an increased presumption from the double agreement. "The Joint Method of Agreement and Difference (or the Indirect Method of Difference, or, as I should prefer to call it, the Double Method of Agreement) is being continually employed by us in the ordinary affairs of life. If when I take a particular kind of food, I find that I invariably suffer from some particular form of illness, whereas, when I leave it off, I cease to suffer, I entertain a double assurance that the food is the cause of my illness. I have observed that a certain plant is invariably plentiful on a particular soil; if, with a wide experience, I fail to find it growing on any other soil, I feel confirmed in my belief that there is in this particular soil some chemical constituent, or some peculiar combination of chemical constituents, which is highly favourable, if not essential, to the growth of the plant."

Footnote 1: Elimination, or setting aside as being of no concern, must not be confounded with the exclusion of agents practised in applying the Method of Difference. We use the word in its ordinary sense of putting outside the sphere of an argument. By a curious slip, Professor Bain follows Mill in applying the word sometimes to the process of singling out or disentangling a causal circumstance. This is an inadvertent departure from the ordinary usage, according to which elimination means discarding from consideration as being non-essential.

Footnote 2: Hirsch's Geographical and Historical Pathology, Creighton's translation, vol. ii. pp. 121-202.

Footnote 3: The bare titles Difference and Agreement, though they have the advantage of simplicity, are apt to puzzle beginners inasmuch as in the Method of Difference the agreement among the instances is at a maximum, and the difference at a minimum, and vice vers in the Method of Agreement. In both Methods it is really the isolation of the connexion between antecedent and sequent that constitutes the proof.

Footnote 4: That rainbows in the sky are produced by the passage of light through minute drops in the clouds was an inference from this observed uniformity.

Chapter VI.

METHODS OF OBSERVATION.—MINOR METHODS.

I.—Concomitant Variations.

Whatever phenomenon varies in any manner whenever another phenomenon varies in some particular manner, is either a cause or an effect of that phenomenon, or is connected with it through some fact of causation.

This simple principle is constantly applied by us in connecting and disconnecting phenomena. If we hear a sound which waxes and wanes with the rise and fall of the wind, we at once connect the two phenomena. We may not know what the causal connexion is, but if they uniformly vary together, there is at once a presumption that the one is causally dependent on the other, or that both are effects of the same cause.

This principle was employed by Wells in his researches into Dew. Some bodies are worse conductors of heat than others, and rough surfaces radiate heat more rapidly than smooth. Wells made observations on conductors and radiators of various degrees, and found that the amount of dew deposited was greater or less according as the objects conducted heat slowly or radiated heat rapidly. He thus established what Herschel called a "scale of intensity" between the conducting and radiating properties of the bodies bedewed, and the amount of the dew deposit. The explanation was that in bad conductors the surface cools more quickly than in good conductors because heat is more slowly supplied from within. Similarly in rough surfaces there is a more rapid cooling because heat is given off more quickly. But whatever the explanation might be, the mere concomitant variation of the dew deposit with these properties showed that there was some causal connexion between them.

It must be remembered that the mere fact of concomitant variation is only an index that some causal connexion exists. The nature of the connexion must be ascertained by other means, and may remain a problem, one of the uses of such observed facts being indeed to suggest problems, for inquiry. Thus a remarkable concomitance has been observed between spots on the sun, displays of Aurora Borealis, and magnetic storms. The probability is that they are causally connected, but science has not yet discovered how. Similarly in the various sciences properties are arranged in scales of intensity, and any correspondence between two scales becomes a subject for investigation on the assumption that it points to a causal connexion. We shall see afterwards how in social investigations concomitant variations in averages furnish material for reasoning.

When two variants can be precisely measured, the ratio of the variation may be ascertained by the Method of Single Difference. We may change an antecedent in degree, and watch the corresponding change in the effect, taking care that no other agent influences the effect in the meantime. Often when we cannot remove an agent altogether, we may remove it in a measurable amount, and observe the result. We cannot remove friction altogether, but the more it is diminished, the further will a body travel under the impulse of the same force.

Until a concomitant variation has been fully explained, it is merely an empirical law, and any inference that it extends at the same rate beyond the limits of observation must be made with due caution. "Parallel variation," says Professor Bain, "is sometimes interrupted by critical points, as in the expansion of bodies by heat, which suffers a reverse near the point of cooling. Again, the energy of a solution does not always follow the strength; very dilute solutions occasionally exercise a specific power not possessed in any degree by stronger. So, in the animal body, food and stimulants operate proportionally up to a certain point, at which their further operation is checked by the peculiarities in the structure of the living organs.... We cannot always reason from a few steps in a series to the whole series, partly because of the occurrence of critical points, and partly from the development at the extremes of new and unsuspected powers. Sir John Herschel remarks that until very recently 'the formulÆ empirically deduced for the elasticity of steam, those for the resistance of fluids, and on other similar subjects, have almost invariably failed to support the theoretical structures that have been erected upon them'."¹

II.—Single Residue.

Subduct from any phenomenon such part as previous induction has shown to be the effect of certain antecedents, and the residue of the phenomenon is the effect of the remaining antecedents.

"Complicated phenomena, in which several causes concurring, opposing, or quite independent of each other, operate at once, so as to produce a compound effect, may be simplified by subducting the effect of all the known causes, as well as the nature of the case permits, either by deductive reasoning or by appeal to experience, and thus leaving as it were a residual phenomenon to be explained. It is by this process, in fact, that science, in its present advanced state, is chiefly promoted. Most of the phenomena which nature presents are very complicated; and when the effects of all known causes are estimated with exactness, and subducted, the residual facts are constantly appearing in the form of phenomena altogether new, and leading to the most important conclusions."²

It is obvious that this is not a primary method of observation, but a method that may be employed with great effect to guide observation when a considerable advance has been made in accurate knowledge of agents and their mode of operation. The greatest triumph of the method, the discovery of the planet Neptune, was won some years after the above passage from Herschel's Discourse was written. Certain perturbations were observed in the movements of the planet Uranus: that is to say, its orbit was found not to correspond exactly with what it should be when calculated according to the known influences of the bodies then known to astronomers. These perturbations were a residual phenomenon. It was supposed that they might be due to the action of an unknown planet, and two astronomers, Adams and Le Verrier, simultaneously calculated the position of a body such as would account for the observed deviations. When telescopes were directed to the spot thus indicated, the planet Neptune was discovered. This was in September, 1846: before its actual discovery, Sir John Herschel exulted in the prospect of it in language that strikingly expresses the power of the method. "We see it," he said, "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."³

Many of the new elements in Chemistry have been discovered in this way. For example, when distinctive spectrums had been observed for all known substances, then on the assumption that every substance has a distinctive spectrum, the appearance of lines not referable to any known substance indicated the existence of hitherto undiscovered substances and directed search for them. Thus Bunsen in 1860 discovered two new alkaline metals, CÆsium and Rubidium. He was examining alkalies left from the evaporation of a large quantity of mineral water from Durkheim. On applying the spectroscope to the flame which this particular salt or mixture of salts gave off, he found that some bright lines were visible which he had never observed before, and which he knew were not produced either by potash or soda. He then set to work to analyse the mixture, and ultimately succeeded in separating two new alkaline substances. When he had succeeded in getting them separate, it was of course by the Method of Difference that he ascertained them to be capable of producing the lines that had excited his curiosity.

Footnote 1: Bain's Logic, vol. ii. p. 64.

Footnote 2: Herschel's Discourse, § 158.

Footnote 3: De Morgan's Budget of Paradoxes, p. 237.

Chapter VII.

THE METHOD OF EXPLANATION.

Given perplexity as to the cause of any phenomenon, what is our natural first step? We may describe it as searching for a clue: we look carefully at the circumstances with a view to finding some means of assimilating what perplexes us to what is already within our knowledge. Our next step is to make a guess, or conjecture, or, in scientific language, a hypothesis. We exercise our Reason or Nous, or Imagination, or whatever we choose to call the faculty, and try to conceive some cause that strikes us as sufficient to account for the phenomenon. If it is not at once manifest that this cause has really operated, our third step is to consider what appearances ought to present themselves if it did operate. We then return to the facts in question, and observe whether those appearances do present themselves. If they do, and if there is no other way of accounting for the effect in all its circumstances, we conclude that our guess is correct, that our hypothesis is proved, that we have reached a satisfactory explanation.

These four steps or stages may be distinguished in most protracted inquiries into cause. They correspond to the four stages of what Mr. Jevons calls the Inductive Method par excellence, Preliminary Observation, Hypothesis, Deduction and Verification. Seeing that the word Induction is already an overloaded drudge, perhaps it would be better to call these four stages the Method of Explanation. The word Induction, if we keep near its original and most established meaning, would apply strictly only to the fourth stage, the Verification, the bringing in of the facts to confirm our hypothesis. We might call the method the Newtonian method, for all four stages are marked in the prolonged process by which he made good his theory of Gravitation.

To give the name of Inductive Method simply to all the four stages of an orderly procedure from doubt to a sufficient explanation is to encourage a widespread misapprehension. There could be no greater error than to suppose that only the senses are used in scientific investigation. There is no error that men of science are so apt to resent in the mouths of the non-scientific. Yet they have partly brought it on themselves by their loose use of the word Induction, which they follow Bacon in wresting from the traditional meaning of Induction, using it to cover both Induction or the bringing in of facts—an affair mainly of Observation—and Reasoning, the exercise of Nous, the process of constructing satisfactory hypotheses. In reaction against the popular misconception which Bacon encouraged, it is fashionable now to speak of the use of Imagination in Science. This is well enough polemically. Imagination as commonly understood is akin to the constructive faculty in Science, and it is legitimate warfare to employ the familiar word of high repute to force general recognition of the truth. But in common usage Imagination is appropriated to creative genius in the Fine Arts, and to speak of Imagination in Science is to suggest that Science deals in fictions, and has discarded Newton's declaration Hypotheses non fingo. In a fight for popular respect, men of science may be right to claim for themselves Imagination; but in the interests of clear understanding, the logician must deplore that they should defend themselves from a charge due to their abuse of one word by making an equally unwarrantable and confusing extension of another.

Call it what we will, the faculty of likely guessing, of making probable hypotheses, of conceiving in all its circumstances the past situation or the latent and supramicroscopical situation out of which a phenomenon has emerged, is one of the most important of the scientific man's special gifts. It is by virtue of it that the greatest advancements of knowledge have been achieved, the cardinal discoveries in Molar and Molecular Physics, Biology, Geology, and all departments of Science. We must not push the idea of stages in explanatory method too far: the right explanation may be reached in a flash. The idea of stages is really useful mainly in trying to make clear the various difficulties in investigation, and the fact that different men of genius may show different powers in overcoming them. The right hypothesis may occur in a moment, as if by simple intuition, but it may be tedious to prove, and the gifts that tell in proof, such as Newton's immense mathematical power in calculating what a hypothesis implies, Darwin's patience in verifying, Faraday's ingenuity in devising experiments, are all great gifts, and may be serviceable at different stages. But without originality and fertility in probable hypothesis, nothing can be done.

The dispute between Mill and Whewell as to the place and value of hypotheses in science was in the main a dispute about words. Mill did not really undervalue hypothesis, and he gave a most luminous and accurate account of the conditions of proof. But here and there he incautiously spoke of the "hypothetical method" (by which he meant what we have called the method of Explanation) as if it were a defective kind of proof, a method resorted to by science when the "experimental methods" could not be applied. Whether his language fairly bore this construction is not worth arguing, but this was manifestly the construction that Whewell had in his mind when he retorted, as if in defence of hypotheses, that "the inductive process consists in framing successive hypotheses, the comparison of these with the ascertained facts of nature, and the introduction into them of such modifications as the comparison may render necessary". This is a very fair description of the whole method of explanation. There is nothing really inconsistent with it in Mill's account of his "hypothetical method"; only he erred himself or was the cause of error in others in suggesting, intentionally or unintentionally, that the Experimental Methods were different methods of proof. The "hypothetical method," as he described it, consisting of Induction, Ratiocination, and Verification, really comprehends the principles of all modes of observation, whether naturally or artificially experimental. We see this at once when we ask how the previous knowledge is got in accordance with which hypotheses are framed. The answer must be, by Observation. However profound the calculations, it must be from observed laws, or supposed analogues of them, that we start. And it is always by Observation that the results of these calculations are verified.

Both Mill and Whewell, however, confined themselves too exclusively to the great hypotheses of the Sciences, such as Gravitation and the Undulatory Theory of Light. In the consideration of scientific method, it is a mistake to confine our attention to these great questions, which from the multitude of facts embraced can only be verified by prolonged and intricate inquiry. Attempts at the explanation of the smallest phenomena proceed on the same plan, and the verification of conjectures about them is subject to the same conditions, and the methods of investigation and the conditions of verification can be studied most simply in the smaller cases. Further, I venture to think it a mistake to confine ourselves to scientific inquiry in the narrow sense, meaning thereby inquiry conducted within the pale of the exact sciences. For not merely the exact sciences but all men in the ordinary affairs of life must follow the same methods or at least observe the same principles and conditions, in any satisfactory attempt to explain.

Tares appear among the wheat. Good seed was sown: whence, then, come the tares? "An enemy has done this." If an enemy has actually been observed sowing the tares, his agency can be proved by descriptive testimony. But if he has not been seen in the act, we must resort to what is known in Courts of Law as circumstantial evidence. This is the "hypothetical method" of science. That the tares are the work of an enemy is a hypothesis: we examine all the circumstances of the case in order to prove, by inference from our knowledge of similar cases, that thus, and thus only, can those circumstances be accounted for. Similarly, when a question is raised as to the authorship of an anonymous book. We first search for a clue by carefully noting the diction, the structure of the sentences, the character and sources of the illustration, the special tracks of thought. We proceed upon the knowledge that every author has characteristic turns of phrase and imagery and favourite veins of thought, and we look out for such internal evidence of authorship in the work before us. Special knowledge and acumen may enable us to detect the authorship at once from the general resemblance to known work. But if we would have clear proof, we must show that the resemblance extends to all the details of phrase, structure and imagery: we must show that our hypothesis of the authorship of XYZ explains all the circumstances. And even this is not sufficient, as many erroneous guesses from internal evidence may convince us. We must establish further that there is no other reasonable way of accounting for the matter and manner of the book; for example, that it is not the work of an imitator. An imitator may reproduce all the superficial peculiarities of an author with such fidelity that the imitation can hardly be distinguished from the original: thus few can distinguish between Fenton's work and Pope's in the translation of the Odyssey. We must take such known facts into account in deciding a hypothesis of authorship. Such hypotheses can seldom be decided on internal evidence alone: other circumstantial evidence—other circumstances that ought to be discoverable if the hypothesis is correct—must be searched for.

The operation of causes that are manifest only in their effects must be proved by the same method as the operation of past causes that have left only their effects behind them. Whether light is caused by a projection of particles from a luminous body or by an agitation communicated through an intervening medium cannot be directly observed. The only proof open is to calculate what should occur on either hypothesis, and observe whether this does occur. In such a case there is room for the utmost calculating power and experimental ingenuity. The mere making of the general hypothesis or guess is simple enough, both modes of transmitting influence, the projection of moving matter and the travelling of an undulation or wave movement, being familiar facts. But it is not so easy to calculate exactly how a given impulse would travel, and what phenomena of ray and shadow, of reflection, refraction and diffraction ought to be visible in its progress. Still, no matter how intricate the calculation, its correspondence with what can be observed is the only legitimate proof of the hypothesis.

II.—Obstacles to Explanation.—Plurality of Causes and Intermixture of Effects.

There are two main ways in which explanation may be baffled. There may exist more than one cause singly capable of producing the effect in question, and we may have no means of determining which of the equally sufficient causes has actually been at work. For all that appears the tares in our wheat may be the effect of accident or of malicious design: an anonymous book may be the work of an original author or of an imitator. Again, an effect may be the joint result of several co-operating causes, and it may be impossible to determine their several potencies. The bitter article in the Quarterly may have helped to kill John Keats, but it co-operated with an enfeebled constitution and a naturally over-sensitive temperament, and we cannot assign its exact weight to each of these coefficients. Death may be the result of a combination of causes; organic disease co-operating with exposure, over-fatigue co-operating with the enfeeblement of the system by disease.

The technical names for these difficulties, Plurality of Causes and Intermixture of Effects, are apt to confuse without some clearing up. In both kinds of difficulty more causes than one are involved: but in the one kind of case there is a plurality of possible or equally probable causes, and we are at a loss to decide which: in the other kind of case there is a plurality of co-operating causes; the effect is the result or product of several causes working conjointly, and we are unable to assign to each its due share.

It is with a view to overcoming these difficulties that Science endeavours to isolate agencies and ascertain what each is capable of singly. Mill and Bain treat Plurality of Causes and Intermixture of Effects in connexion with the Experimental Methods. It is better, perhaps, to regard them simply as obstacles to explanation, and the Experimental Methods as methods of overcoming those obstacles. The whole purpose of the Experimental Methods is to isolate agencies and effects: unless they can be isolated, the Methods are inapplicable. In situations where the effects observable may be referred with equal probability to more than one cause, you cannot eliminate so as to obtain a single agreement. The Method of Agreement is frustrated. And an investigator can get no light from mixed effects, unless he knows enough of the causes at work to be able to apply the Method of Residues. If he does not, he must simply look out for or devise instances where the agencies are at work separately, and apply the principle of Single Difference.

Great, however, as the difficulties are, the theory of Plurality and Intermixture baldly stated makes them appear greater than they are in practice. There is a consideration that mitigates the complication, and renders the task of unravelling it not altogether hopeless. This is that different causes have distinctive ways of operating, and leave behind them marks of their presence by which their agency in a given case may be recognised.

An explosion, for example, occurs. There are several explosive agencies, capable of causing as much destruction as meets the eye at the first glance. The agent in the case before us may be gunpowder or it may be dynamite. But the two agents are not so alike in their mode of operation as to produce results identical in every circumstance. The expert inquirer knows by previous observation that when gunpowder acts the objects in the neighbourhood are blackened; and that an explosion of dynamite tears and shatters in a way peculiar to itself. He is thus able to interpret the traces, to make and prove a hypothesis.

A man's body is found dead in water. It may be a question whether death came by drowning or by previous violence. He may have been suffocated and afterwards thrown into the water. But the circumstances will tell the true story. Death by drowning has distinctive symptoms. If drowning was the cause, water will be found in the stomach and froth in the trachea.

Thus, though there may be a plurality of possible causes, the causation in the given case may be brought home to one by distinctive accompaniments, and it is the business of the scientific inquirer to study these. What is known as the "ripple-mark" in sandstone surfaces may be produced in various ways. The most familiar way is by the action of the tides on the sand of the sea-shore, and the interpreter who knows this way only would ascribe the marks at once to this agency. But ripple-marks are produced also by the winds on drifting sands, by currents of water where no tidal influence is felt, and in fact by any body of water in a state of oscillation. Is it, then, impossible to decide between these alternative possibilities of causation? No: wind-ripples and current-ripples and tidal-ripples have each their own special character and accompanying conditions, and the hypothesis of one rather than another may be made good by means of these. "In rock-formations," Mr. Page says,¹ "there are many things which at first sight seem similar, and yet on more minute examination, differences are detected and conditions discovered which render it impossible that these appearances can have arisen from the same causation."

The truth is that generally when we speak of plurality of causes, of alternative possibilities of causation, we are not thinking of the effect in its individual entirety, but only of some general or abstract aspect of it. When we say, e.g., that death may be produced by a great many different causes, poison, gunshot wounds, disease of this or that organ, we are thinking of death in the abstract, not of the particular case under consideration, which as an individual case, has characters so distinctive that only one combination of causes is possible.

The effort of science is to become less and less abstract in this sense, by observing agencies or combinations of agencies apart and studying the special characters of their effects. That knowledge is then applied, on the assumption that where those characters are present, the agent or combination of agencies has been at work. Given an effect to be explained, it is brought home to one out of several possible alternatives by circumstantial evidence.

Bacon's phrase, Instantia Crucis,² or Finger-post Instance, might be conveniently appropriated as a technical name for a circumstance that is decisive between rival hypotheses. This was, in effect, proposed by Sir John Herschel,³ who drew attention to the importance of these crucial instances, and gave the following example: "A curious example is given by M. Fresnel, as decisive, in his mind, of the question between the two great opinions on the nature of light, which, since the time of Newton and Huyghens, have divided philosophers. When two very clean glasses are laid one on the other, if they be not perfectly flat, but one or both in an almost imperceptible degree convex or prominent, beautiful and vivid colours will be seen between them; and if these be viewed through a red glass, their appearance will be that of alternate dark and bright stripes.... Now, the coloured stripes thus produced are explicable on both theories, and are appealed to by both as strong confirmatory facts; but there is a difference in one circumstance according as one or the other theory is employed to explain them. In the case of the Huyghenian doctrine, the intervals between the bright stripes ought to appear absolutely black; in the other, half bright, when viewed [in a particular manner] through a prism. This curious case of difference was tried as soon as the opposing consequences of the two theories were noted by M. Fresnel, and the result is stated by him to be decisive in favour of that theory which makes light to consist in the vibrations of an elastic medium."

III.—The Proof of a Hypothesis.

The completest proof of a hypothesis is when that which has been hypothetically assumed to exist as a means of accounting for certain phenomena is afterwards actually observed to exist or is proved by descriptive testimony to have existed. Our argument, for example, from internal evidence that Mill in writing his Logic aimed at furnishing a method for social investigations is confirmed by a letter to Miss Caroline Fox, in which he distinctly avowed that object.

The most striking example of this crowning verification in Science is the discovery of the planet Neptune, in which case an agent hypothetically assumed was actually brought under the telescope as calculated. Examples almost equally striking have occurred in the history of the Evolution doctrine. Hypothetical ancestors with certain peculiarities of structure have been assumed as links between living species, and in some cases their fossils have actually been found in the geological register.

Such triumphs of verification are necessarily rare. For the most part the hypothetical method is applied to cases where proof by actual observation is impossible, such as prehistoric conditions of the earth or of life upon the earth, or conditions in the ultimate constitution of matter that are beyond the reach of the strongest microscope. Indeed, some would confine the word hypothesis to cases of this kind. This, in fact, was done by Mill: hypothesis, as he defined it, was a conjecture not completely proved, but with a large amount of evidence in its favour. But seeing that the procedure of investigation is the same, namely, conjecture, calculation and comparison of facts with the calculated results, whether the agency assumed can be brought to the test of direct observation or not, it seems better not to restrict the word hypothesis to incompletely proved conjectures, but to apply it simply to a conjecture made at a certain stage in whatever way it may afterwards be verified.

In the absence of direct verification, the proof of a hypothesis is exclusive sufficiency to explain the circumstances. The hypothesis must account for all the circumstances, and there must be no other way of accounting for them. Another requirement was mentioned by Newton in a phrase about the exact meaning of which there has been some contention. The first of his RegulÆ Philosophandi laid down that the cause assumed must be a vera causa. "We are not," the Rule runs, "to admit other causes of natural things than such as both are true, and suffice for explaining their phenomena."⁴

It has been argued that the requirement of "verity" is superfluous; that it is really included in the requirement of sufficiency; that if a cause is sufficient to explain the phenomena it must ipso facto be the true cause. This may be technically arguable, given a sufficient latitude to the word sufficiency: nevertheless, it is convenient to distinguish between mere sufficiency to explain the phenomena in question, and the proof otherwise that the cause assigned really exists in rerum natura, or that it operated in the given case. The frequency with which the expression vera causa has been used since Newton's time shows that a need is felt for it, though it may be hard to define "verity" precisely as something apart from "sufficiency". If we examine the common usage of the expression we shall probably find that what is meant by insisting on a vera causa is that we must have some evidence for the cause assigned outside the phenomena in question. In seeking for verification of a hypothesis we must extend our range beyond the limited facts that have engaged our curiosity and that demand explanation.

There can be little doubt that Newton himself aimed his rule at the Cartesian hypothesis of Vortices. This was an attempt to explain the solar system on the hypothesis that cosmic space is filled with a fluid in which the planets are carried round as chips of wood in a whirlpool, or leaves or dust in a whirlwind. Now this is so far a vera causa that the action of fluid vortices is a familiar one: we have only to stir a cup of tea with a bit of stalk in it to get an instance. The agency supposed is sufficient also to account for the revolution of a planet round the sun, given sufficient strength in the fluid to buoy up the planet. But if there were such a fluid in space there would be other phenomena: and in the absence of these other phenomena the hypothesis must be dismissed as imaginary. The fact that comets pass into and out of spaces where the vortices must be assumed to be in action without exhibiting any perturbation is an instantia crucis against the hypothesis.

If by the requirement of a vera causa were meant that the cause assigned must be one directly open to observation, this would undoubtedly be too narrow a limit. It would exclude such causes as the ether which is assumed to fill interstellar space as a medium for the propagation of light. The only evidence for such a medium and its various properties is sufficiency to explain the phenomena. Like suppositions as to the ultimate constitution of bodies, it is of the nature of what Professor Bain calls a "Representative Fiction": the only condition is that it must explain all the phenomena, and that there must be no other way of explaining all. When it is proved that light travels with a finite velocity, we are confined to two alternative ways of conceiving its transmission, a projection of matter from the luminous body and the transference of vibrations through an intervening medium. Either hypothesis would explain many of the facts: our choice must rest with that which best explains all. But supposing that all the phenomena of light were explained by attributing certain properties to this intervening medium, it would probably be held that the hypothesis of an ether had not been fully verified till other phenomena than those of light had been shown to be incapable of explanation on any other hypothesis. If the properties ascribed to it to explain the phenomena of light sufficed at the same time to explain otherwise inexplicable phenomena connected with Heat, Electricity, or Gravity, the evidence of its reality would be greatly strengthened.

Not only must the circumstances in hand be explained, but other circumstances must be found to be such as we should expect if the cause assigned really operated. Take, for example, the case of Erratic blocks or boulders, huge fragments of rock found at a distance from their parent strata. The lowlands of England, Scotland, and Ireland, and the great central plain of Northern Europe contain many such fragments. Their composition shows indubitably that they once formed part of hills to the northward of their present site. They must somehow have been detached and transported to where we now find them. How? One old explanation is that they were carried by witches, or that they were themselves witches accidentally dropped and turned into stone. Any such explanation by supernatural means can neither be proved nor disproved. Some logicians would exclude such hypotheses altogether on the ground that they cannot be rendered either more or less probable by subsequent examination.⁵ The proper scientific limit, however, is not to the making of hypotheses, but to the proof of them. The more hypotheses the merrier: only if such an agency as witchcraft is suggested, we should expect to find other evidence of its existence in other phenomena that could not otherwise be explained. Again, it has been suggested that the erratic boulders may have been transported by water. Water is so far a vera causa that currents are known to be capable of washing huge blocks to a great distance. But blocks transported in this way have the edges worn off by the friction of their passage: and, besides, currents strong enough to dislodge and force along for miles blocks as big as cottages must have left other marks of their presence. The explanation now received is that glaciers and icebergs were the means of transport. But this explanation was not accepted till multitudes of circumstances were examined all tending to show that glaciers had once been present in the regions where the erratic blocks are found. The minute habits of glaciers have been studied where they still exist: how they slowly move down carrying fragments of rock; how icebergs break off when they reach water, float off with their load, and drop it when they melt; how they grind and smooth the surfaces of rocks over which they pass or that are frozen into them: how they undercut and mark the faces of precipices past which they move; how moraines are formed at the melting ends of them, and so forth. When a district exhibits all the circumstances that are now observed to attend the action of glaciers the proof of the hypothesis that glaciers were once there is complete.

Footnote 1: Page's Philosophy of Geology, p. 38.

Footnote 2: Crux in this phrase means a cross erected at the parting of ways, with arms to tell whither each way leads.

Footnote 3: Discourse, § 218.

Footnote 4: Causas rerum naturalium non plures admitti debere quam quÆ et veriÆ sint et carum phenomenis explicandis sufficiant.

Footnote 5: See Prof. Fowler on the Conditions of Hypotheses, Inductive Logic, pp. 100-115.

Chapter VIII.

SUPPLEMENTARY METHODS OF INVESTIGATION.

I.—The Maintenance of Averages.—Supplement to the Method of Difference.

A certain amount of law obtains among events that are usually spoken of as matters of chance or accident in the individual case. Every kind of accident recurs with a certain uniformity. If we take a succession of periods, and divide the total number of any kind of event by the number of periods, we get what is called the average for that period: and it is observed that such averages are maintained from period to period. Over a series of years there is a fixed proportion between good harvests and bad, between wet days and dry: every year nearly the same number of suicides takes place, the same number of crimes, of accidents to life and limb, even of suicides, crimes, or injuries by particular means: every year in a town nearly the same number of children stray from their parents and are restored by the police: every year nearly the same number of persons post letters without putting an address on them.

This maintenance of averages is simple matter of observation, a datum of experience, an empirical law. Once an average for any kind of event has been noted, we may count upon its continuance as we count upon the continuance of any other kind of observed uniformity. Insurance companies proceed upon such empirical laws of average in length of life and immunity from injurious accidents by sea or land: their prosperity is a practical proof of the correctness and completeness of the observed facts and the soundness of their inference to the continuance of the average.

The constancy of averages is thus a guide in practice. But in reasoning upon them in investigations of cause, we make a further assumption than continued uniformity. We assume that the maintenance of the average is due to the permanence of the producing causes. We regard the average as the result of the operation of a limited sum of forces and conditions, incalculable as regards their particular incidence, but always pressing into action, and thus likely to operate a certain number of times within a limited period.

Assuming the correctness of this explanation, it would follow that any change in the average is due to some change in the producing conditions; and this derivative law is applied as a help in the observation and explanation of social facts. Statistics are collected and classified: averages are struck: and changes in the average are referred to changes in the concomitant conditions.

With the help of this law, we may make a near approach to the precision of the Method of Difference. A multitude of unknown or unmeasured agents may be at work on a situation, but we may accept the average as the result of their joint operation. If then a new agency is introduced or one of the known agents is changed in degree, and this is at once followed by a change in the average, we may with fair probability refer the change in the result to the change in the antecedents.

The difficulty is to find a situation where only one antecedent has been changed before the appearance of the effect. This difficulty may be diminished in practice by eliminating changes that we have reason to know could not have affected the circumstances in question. Suppose, for example, our question is whether the Education Act of 1872 had an influence in the decrease of juvenile crime. Such a decrease took place post hoc; was it propter hoc? We may at once eliminate or put out of account the abolition of Purchase in the Army or the extension of the Franchise as not having possibly exercised any influence on juvenile crime. But with all such eliminations, there may still remain other possible influences, such as an improvement in the organisation of the Police, or an expansion or contraction in employment. "Can you tell me in the face of chronology," a leading statesman once asked, "that the Crimes Act of 1887 did not diminish disorder in Ireland?" But chronological sequence alone is not a proof of causation as long as there are other contemporaneous changes of condition that may also have been influential.

The great source of fallacy is our proneness to eliminate or isolate in accordance with our prejudices. This has led to the gibe that anything can be proved by statistics. Undoubtedly statistics may be made to prove anything if you have a sufficiently low standard of proof and ignore the facts that make against your conclusion. But averages and variations in them are instructive enough if handled with due caution. The remedy for rash conclusions from statistics is not no statistics, but more of them and a sound knowledge of the conditions of reasonable proof.

II.—The Presumption from Extra-Casual Coincidence.

We have seen that repeated coincidence raises a presumption of causal connexion between the coinciding events. If we find two events going repeatedly together, either abreast or in sequence, we infer that the two are somehow connected in the way of causation, that there is a reason for the coincidence in the manner of their production. It may not be that the one produces the other, or even that their causes are in any way connected: but at least, if they are independent one of the other, both are tied down to happen at the same place and time,—the coincidence of both with time and place is somehow fixed.

But though this is true in the main, it is not true without qualification. We expect a certain amount of repeated coincidence without supposing causal connexion. If certain events are repeated very often within our experience, if they have great positive frequency, we may observe them happening together more than once without concluding that the coincidence is more than fortuitous.

For example, if we live in a neighbourhood possessed of many black cats, and sally forth to our daily business in the morning, a misfortune in the course of the day might more than once follow upon our meeting a black cat as we went out without raising in our minds any presumption that the one event was the result of the other.

Certain planets are above the horizon at certain periods of the year and below the horizon at certain other periods. All through the year men and women are born who afterwards achieve distinction in various walks of life, in love, in war, in business, at the bar, in the pulpit. We perceive a certain number of coincidences between the ascendancy of certain planets and the birth of distinguished individuals without suspecting that planetary influence was concerned in their superiority.

Marriages take place on all days of the year: the sun shines on a good many days at the ordinary time for such ceremonies; some marriages are happy, some unhappy; but though in the case of many happy marriages the sun has shone upon the bride, we regard the coincidence as merely accidental.

Men often dream of calamities and often suffer calamities in real life: we should expect the coincidence of a dream of calamity followed by a reality to occur more than once as a result of chance. There are thousands of men of different nationalities in business in London, and many fortunes are made: we should expect more than one man of any nationality represented there to make a fortune without arguing any connexion between his nationality and his success.

We allow, then, for a certain amount of repeated coincidence without presuming causal connexion: can any rule be laid down for determining the exact amount?

Prof. Bain has formulated the following rule: "Consider the positive frequency of the phenomena themselves, how great frequency of coincidence must follow from that, supposing there is neither connexion nor repugnance. If there be greater frequency, there is connexion; if less, repugnance."

I do not know that we can go further definite in precept. The number of casual coincidences bears a certain proportion to the positive frequency of the coinciding phenomena: that proportion is to be determined by common-sense in each case. It may be possible, however, to bring out more clearly the principle on which common-sense proceeds in deciding what chance will and will not account for, although our exposition amounts only to making more clear what it is that we mean by chance as distinguished from assignable reason. I would suggest that in deciding what chance will not account for, we make regressive application of a principle which may be called the principle of Equal and Unequal Alternatives, and which may be worded as follows:—

Of a given number of possible alternatives, all equally possible, one of which is bound to occur at a given time, we expect each to have its turn an equal number of times in the long run. If several of the alternatives are of the same kind, we expect an alternative of that kind to recur with a frequency proportioned to their greater number. If any of the alternatives has an advantage, it will recur with a frequency proportioned to the strength of that advantage.

Situations in which alternatives are absolutely equal are rare in nature, but they are artificially created for games "of chance," as in tossing a coin, throwing dice, drawing lots, shuffling and dealing a pack of cards. The essence of all games of chance is to construct a number of equal alternatives, making them as nearly equal as possible, and to make no prearrangement which of the number shall come off. We then say that this is determined by chance. If we ask why we believe that when we go on bringing off one alternative at a time, each will have its turn, part of the answer undoubtedly is that given by De Morgan, namely, that we know no reason why one should be chosen rather than another. This, however, is probably not the whole reason for our belief. The rational belief in the matter is that it is only in the long run or on the average that each of the equal alternatives will have its turn, and this is probably founded on the experience of actual trial. The mere equality of the alternatives, supposing them to be perfectly equal, would justify us as much in expecting that each would have its turn in a single revolution of the series, in one complete cycle of the alternatives. This, indeed, may be described as the natural and primitive expectation which is corrected by experience. Put six balls in a wicker bottle, shake them up, and roll one out: return this one, and repeat the operation: at the end of six draws we might expect each ball to have had its turn of being drawn if we went merely on the abstract equality of the alternatives. But experience shows us that in six successive draws the same ball may come out twice or even three or four times, although when thousands of drawings are made each comes out nearly an equal number of times. So in tossing a coin, heads may turn up ten or twelve times in succession, though in thousands of tosses heads and tails are nearly equal. Runs of luck are thus within the rational doctrine of chances: it is only in the long run that luck is equalised supposing that the events are pure matter of chance, that is, supposing the fundamental alternatives to be equal.

If three out of six balls are of the same colour, we expect a ball of that colour to come out three times as often as any other colour on the average of a long succession of tries. This illustrates the second clause of our principle. The third is illustrated by a loaded coin or die.

By making regressive application of the principle thus ascertained by experience, we often obtain a clue to special causal connexion. We are at least enabled to isolate a problem for investigation. If we find one of a number of alternatives recurring more frequently than the others, we are entitled to presume that they are not equally possible, that there is some inequality in their conditions.

The inequality may simply lie in the greater possible frequency of one of the coinciding events, as when there are three black balls in a bottle of six. We must therefore discount the positive frequency before looking for any other cause. Suppose, for example, we find that the ascendancy of Jupiter coincides more frequently with the birth of men afterwards distinguished in business than with the birth of men otherwise distinguished, say in war, or at the bar, or in scholarship. We are not at liberty to conclude planetary influence till we have compared the positive frequency of the different modes of distinction. The explanation of the more frequently repeated coincidence may simply be that more men altogether are successful in business than in war or law or scholarship. If so, we say that chance accounts for the coincidence, that is to say, that the coincidence is casual as far as planetary influence is concerned.

So in epidemics of fever, if we find on taking a long average that more cases occur in some streets of a town than in others, we are not warranted in concluding that the cause lies in the sanitary conditions of those streets or in any special liability to infection without first taking into account the number of families in the different streets. If one street showed on the average ten times as many cases as another, the coincidence might still be judged casual if there were ten times as many families in it.

Apart from the fallacy of overlooking the positive frequency, certain other fallacies or liabilities to error in applying this doctrine of chances may be specified.

1. We are apt, under the influence of prepossession or prejudice, to remember certain coincidences better than others, and so to imagine extra-casual coincidence where none exists. This bias works in confirming all kinds of established beliefs, superstitious and other, beliefs in dreams, omens, retributions, telepathic communications, and so forth. Many people believe that nobody who thwarts them ever comes to good, and can produce numerous instances from experience in support of this belief.

2. We are apt, after proving that there is a residuum beyond what chance will account for on due allowance made for positive frequency, to take for granted that we have proved some particular cause for this residuum. Now we have not really explained the residuum by the application of the principle of chances: we have only isolated a problem for explanation. There may be more than chance will account for: yet the cause may not be the cause that we assign off-hand. Take, for example, the coincidence that has been remarked between race and different forms of Christianity in Europe. If the distribution of religious systems were entirely independent of race, it might be said that you would expect one system to coincide equally often with different races in proportion to the positive number of their communities. But the Greek system is found almost solely among Slavonic peoples, the Roman among Celtic, and the Protestant among Teutonic. The coincidence is greater than chance will account for. Is the explanation then to be found in some special adaptability of the religious system to the character of the people? This may be the right explanation, but we have not proved it by merely discounting chance. To prove this we must show that there was no other cause at work, that character was the only operative condition in the choice of system, that political combinations, for example, had nothing to do with it. The presumption from extra-casual coincidence is only that there is a special cause: in determining what that is we must conform to the ordinary conditions of explanation.

So coincidence between membership of the Government and a classical education may be greater than chance would account for, and yet the circumstance of having been taught Latin and Greek at school may have had no special influence in qualifying the members for their duties. The proportion of classically educated in the Government may be greater than the proportion of them in the House of Commons, and yet their eminence may be in no way due to their education. Men of a certain social position have an advantage in the competition for office, and all those men have been taught Latin and Greek as a matter of course. Technically speaking, the coinciding phenomena may be independent effects of the same cause.

3. Where the alternative possibilities are very numerous, we are apt not to make due allowance for the number, sometimes overrating it, sometimes underrating it.

The fallacy of underrating the number is often seen in games of chance, where the object is to create a vast number of alternatives, all equally possible, equally open to the player, without his being able to affect the advent of one more than another. In whist, for example, there are some six billions of possible hands. Yet it is a common impression that, one night with another, in the course of a year, a player will have dealt to him about an equal number of good and bad hands. This is a fallacy. A very much longer time is required to exhaust the possible combinations. Suppose a player to have 2000 hands in the course of a year: this is only one "set," one combination, out of thousands of millions of such sets possible. Among those millions of sets, if there is nothing but chance in the matter, there ought to be all proportions of good and bad, some sets all good, some all bad, as well as some equally divided between good and bad.¹

Sometimes, however, the number of possible alternatives is overrated. Thus, visitors to London often remark that they never go there without meeting somebody from their own locality, and they are surprised at this as if they had the same chance of meeting their fellow-visitors and any other of the four millions of the metropolis. But really the possible alternatives of rencounter are far less numerous. The places frequented by visitors to London are filled by much more limited numbers: the possible rencounters are to be counted by thousands rather than by millions.

Footnote 1: See De Morgan's Essay on Probabilities, c. vi., "On Common Notions of Probability".

Undoubtedly there are degrees of probability. Not only do we expect some events with more confidence than others: we may do so, and our confidence may be misplaced: but we have reason to expect some with more confidence than others. There are different degrees of rational expectation. Can those degrees be measured numerically?

The question has come into Logic from the mathematicians. The calculation of Probabilities is a branch of Mathematics. We have seen how it may be applied to guide investigation by eliminating what is due to chance, and it has been vaguely conceived by logicians that what is called the calculus of probabilities might be found useful also in determining by exact numerical measurement the probability of single events. Dr. Venn, who has written a separate treatise on the Logic of Chance, mentions "accurate quantitative apportionment of our belief" as one of the goals which Logic should strive to attain. The following passage will show his drift.¹

A man in good health would doubtless like to know whether he will be alive this time next year. The fact will be settled one way or the other in due time, if he can afford to wait, but if he wants a present decision, Statistics and the Theory of Probability can alone give him any information. He learns that the odds are, say five to one that he will survive, and this is an answer to his question as far as any answer can be given. Statisticians are gradually accumulating a vast mass of data of this general character. What they may be said to aim at is to place us in the position of being able to say, in any given time or place, what are the odds for or against any at present indeterminable fact which belongs to a class admitting of statistical treatment.

Again, outside the regions of statistics proper—which deal, broadly speaking, with events which can be numbered or measured, and which occur with some frequency—there is still a large field as to which some better approach to a reasoned intensity of belief can be acquired. What will be the issue of a coming war? Which party will win in the next election? Will a patient in the crisis of a given disease recover or not? That statistics are lying here in the background, and are thus indirectly efficient in producing and graduating our belief, I fully hold; but there is such a large intermediate process of estimating, and such scope for the exercise of a practised judgment, that no direct appeal to statistics in the common sense can directly help us. In sketching out therefore the claims of an Ideal condition of knowledge, we ought clearly to include a due apportionment of belief to every event of such a class as this. It is an obvious defect that one man should regard as almost certain what another man regards as almost impossible. Short, therefore, of certain prevision of the future, we want complete agreement as to the degree of probability of every future event: and for that matter of every past event as well.

Technically speaking, if we extend the name Modality (see p. 78) to any qualification of the certainty of a statement of belief, what Dr. Venn here desiderates, as he has himself suggested, is a more exact measurement of the Modality of propositions. We speak of things as being certain, possible, impossible, probable, extremely probable, faintly probable, and so forth: taking certainty as the highest degree of probability² shading gradually down to the zero of the impossible, can we obtain an exact numerical measure for the gradations of assurance?

To examine the principles of all the cases in which chances for and against an occurrence have been calculated from real or hypothetical data, would be to trespass into the province of Mathematics, but a few simple cases will serve to show what it is that the calculus attempts to measure, and what is the practical value of the measurement as applied to the probability of a single event.

Suppose there are 100 balls in a box, 30 white and 70 black, all being alike except in respect of colour, we say that the chances of drawing a black ball as against a white are as 7 to 3, and the probability of drawing black is measured by the fraction ⁷/₁₀. In believing this we proceed on the principle already explained (p. 356) of Proportional Chances. We do not know for certain whether black or white will emerge, but knowing the antecedent situation we expect black rather than white with a degree of assurance corresponding to the proportions of the two in the box. It is our degree of rational assurance that we measure by this fraction, and the rationality of it depends on the objective condition of the facts, and is the same for all men, however much their actual degree of confidence may vary with individual temperament. That black will be drawn seven times out of every ten on an average if we go on drawing to infinity, is as certain as any empirical law: it is the probability of a single draw that we measure by the fraction ⁷/₁₀.

When we build expectations of single events on statistics of observed proportions of events of that kind, it is ultimately on the same principle that rational expectation rests. That the proportion will obtain on the average we regard as certain: the ratio of favourable cases to the whole number of possible alternatives is the measure of rational expectation or probability in regard to a particular occurrence. If every year five per cent. of the children of a town stray from their guardians, the probability of this or that child's going astray is ¹/₂₀. The ratio is a correct measure only on the assumption that the average is maintained from year to year.

Without going into the combination of probabilities, we are now in a position to see the practical value of such a calculus as applied to particular cases. There has been some misunderstanding among logicians on the point. Mr. Jevons rebuked Mill for speaking disrespectfully of the calculus, eulogised it as one of the noblest creations of the human intellect, and quoted Butler's saying that "Probability is the guide of life". But when Butler uttered this famous saying he was probably not thinking of the mathematical calculus of probabilities as applied to particular cases, and it was this special application to which Mill attached comparatively little value.

The truth is that we seldom calculate or have any occasion to calculate individual chances except as a matter of curiosity. It is true that insurance offices calculate probabilities, but it is not the probability of this or that man dying at a particular age. The precise shade of probability for the individual, in so far as this depends on vital statistics, is a matter of indifference to the company as long as the average is maintained. Our expectations about any individual life cannot be measured by a calculation of the chances because a variety of other elements affect those expectations. We form beliefs about individual cases, but we try to get surer grounds for them than the chances as calculable from statistical data. Suppose a person were to institute a home for lost dogs, he would doubtless try to ascertain how many dogs were likely to go astray, and in so doing would be guided by statistics. But in judging of the probability of the straying of a particular dog, he would pay little heed to statistics as determining the chances, but would proceed upon empirical knowledge of the character of the dog and his master. Even in betting on the field against a particular horse, the bookmaker does not calculate from numerical data such as the number of horses entered or the number of times the favourite has been beaten: he tries to get at the pedigree and previous performances of the various horses in the running. We proceed by calculation of chances only when we cannot do better.

Footnote 1: Empirical Logic, p. 556.

Footnote 2: Mr. Jevons held that all inference is merely probable and that no inference is certain. But this is a purposeless repudiation of common meaning, which he cannot himself consistently adhere to. We find him saying that if a penny is tossed into the air it will certainly come down on one side or the other, on which side being a matter of probability. In common speech probability is applied to a degree of belief short of certainty, but to say that certainty is the highest degree of probability does no violence to the common meaning.

Chapter X.

INFERENCE FROM ANALOGY.

The word Analogy was appropriated by Mill, in accordance with the usage of the eighteenth century, to designate a ground of inference distinct from that on which we proceed in extending a law, empirical or scientific, to a new case. But it is used in various other senses, more or less similar, and in order to make clear the exact logical sense, it is well to specify some of these. The original word ??a????a, as employed by Aristotle, corresponds to the word Proportion in Arithmetic: it signified an equality of ratios, ?s?t?? ?????: two compared with four is analogous to four compared with eight. There is something of the same meaning in the technical use of the word in Physiology, where it is used to signify similarity of function as distinguished from similarity of structure, which is called homology: thus the tail of a whale is analogous to the tail of a fish, inasmuch as it is similarly used for motion, but it is homologous with the hind legs of a quadruped; a man's arms are homologous with a horse's fore legs, but they are not analogous inasmuch as they are not used for progression. Apart from these technical employments, the word is loosely used in common speech for any kind of resemblance. Thus De Quincey speaks of the "analogical" power in memory, meaning thereby the power of recalling things by their inherent likeness as distinguished from their casual connexions or their order in a series. But even in common speech, there is a trace of the original meaning: generally when we speak of analogy we have in our minds more than one pair of things, and what we call the analogy is some resemblance between the different pairs. This is probably what Whately had in view when he defined analogy as "resemblance of relations".

In a strict logical sense, however, as defined by Mill, sanctioned by the previous usage of Butler and Kant, analogy means more than a resemblance of relations. It means a preponderating resemblance between two things such as to warrant us in inferring that the resemblance extends further. This is a species of argument distinct from the extension of an empirical law. In the extension of an empirical law, the ground of inference is a coincidence frequently repeated within our experience, and the inference is that it has occurred or will occur beyond that experience: in the argument from analogy, the ground of inference is the resemblance between two individual objects or kinds of objects in a certain number of points, and the inference is that they resemble one another in some other point, known to belong to the one, but not known to belong to the other. "Two things go together in many cases, therefore in all, including this one," is the argument in extending a generalisation: "Two things agree in many respects, therefore in this other," is the argument from analogy.

The example given by Reid in his Intellectual Powers has become the standard illustration of the peculiar argument from analogy.

We may observe a very great similitude between this earth which we inhabit, and the other planets, Saturn, Jupiter, Mars, Venus and Mercury. They all revolve round the sun, as the earth does, although at different distances and in different periods. They borrow all their light from the sun, as the earth does. Several of them are known to revolve round their axis like the earth, and by that means have like succession of day and night. Some of them have moons, that serve to give them light in the absence of the sun, as our moon does to us. They are all, in their motions, subject to the same law of gravitation as the earth is. From all this similitude it is not unreasonable to think that these planets may, like our earth, be the habitation of various orders of living creatures. There is some probability in this conclusion from analogy.¹

The argument from analogy is sometimes said to range through all degrees of probability from certainty to zero. But this is true only if we take the word analogy in its loosest sense for any kind of resemblance. If we do this, we may call any kind of argument an argument from analogy, for all inferences turn upon resemblance. I believe that if I throw my pen in the air it will come down again, because it is like other ponderable bodies. But if we use the word in its limited logical sense, the degree of probability is much nearer zero than certainty. This is apparent from the conditions that logicians have formulated of a strict argument from analogy.

1. The resemblance must be preponderating. In estimating the value of an argument from analogy, we must reckon the points of difference as counting against the conclusion, and also the points in regard to which we do not know whether the two objects agree or differ. The numerical measure of value is the ratio of the points of resemblance to the points of difference plus the unknown points. Thus, in the argument that the planets are inhabited because they resemble the earth in some respects and the earth is inhabited, the force of the analogy is weakened by the fact that we know very little about the surface of the planets.

2. In a numerical estimate all circumstances that hang together as effects of one cause must be reckoned as one. Otherwise, we might make a fallaciously imposing array of points of resemblance. Thus in Reid's enumeration of the agreements between the earth and the planets, their revolution round the sun and their obedience to the law of gravitation should count as one point of resemblance. If two objects agree in a, b, c, d, e, but b follows from a, and d and e from c, the five points count only as two.

3. If the object to which we infer is known to possess some property incompatible with the property inferred, the general resemblance counts for nothing. The moon has no atmosphere, and we know that air is an indispensable condition of life. Hence, however much the moon may resemble the earth, we are debarred from concluding that there are living creatures on the moon such as we know to exist on the earth. We know also that life such as it is on the earth is possible only within certain limits of temperature, and that Mercury is too hot for life, and Saturn too cold, no matter how great the resemblance to the earth in other respects.

4. If the property inferred is known or presumed to be a concomitant of one or more of the points of resemblance, any argument from analogy is superfluous. This is, in effect, to say that we have no occasion to argue from general resemblance when we have reason to believe that a property follows from something that an object is known to possess. If we knew that any one of the planets possessed all the conditions, positive and negative, of life, we should not require to reckon up all the respects in which it resembles the earth in order to create a presumption that it is inhabited. We should be able to draw the conclusion on other grounds than those of analogy. Newton's famous inference that the diamond is combustible is sometimes quoted as an argument from analogy. But, technically speaking, it was rather, as Professor Bain has pointed out, of the nature of an extended generalisation. Comparing bodies in respect of their densities and refracting powers, he observed that combustible bodies refract more than others of the same density; and observing the exceptionally high refracting power of the diamond, he inferred from this that it was combustible, an inference afterwards confirmed by experiment. "The concurrence of high refracting power with inflammability was an empirical law; and Newton, perceiving the law, extended it to the adjacent case of the diamond. The remark is made by Brewster that had Newton known the refractive powers of the minerals greenockite and octohedrite, he would have extended the inference to them, and would have been mistaken."²

From these conditions it will be seen that we cannot conclude with any high degree of probability from analogy alone. This is not to deny, as Mr. Jevons seems to suppose, that analogies, in the sense of general resemblances, are often useful in directing investigation. When we find two things very much alike, and ascertain that one of them possesses a certain property, the presumption that the other has the same is strong enough to make it worth while trying whether as a matter of fact it has. It is said that a general resemblance of the hills near Ballarat in Australia to the Californian hills where gold had been found suggested the idea of digging for gold at Ballarat. This was a lucky issue to an argument from analogy, but doubtless many have dug for gold on similar general resemblances without finding that the resemblance extended to that particular. Similarly, many of the extensions of the Pharmacopeia have proceeded upon general resemblances, the fact that one drug resembles another in certain properties being a sufficient reason for trying whether the resemblance goes further. The lucky guesses of what is known as natural sagacity are often analogical. A man of wide experience in any subject-matter such as the weather, or the conduct of men in war, in business, or in politics, may conclude to the case in hand from some previous case that bears a general resemblance to it, and very often his conclusions may be perfectly sound though he has not made a numerical estimate of the data.

The chief source of fallacy in analogical argument is ignoring the number of points of difference. It often happens that an amount of resemblance only sufficient for a rhetorical simile is made to do duty as a solid argument. Thus the resemblance between a living body and the body politic is sometimes used to support inferences from successful therapeutic treatment to State policy. The advocates of annual Parliaments in the time of the Commonwealth based their case on the serpent's habit of annually casting its skin.

Carlyle's saying that a ship could never be taken round Cape Horn if the crew were consulted every time the captain proposed to alter the course, if taken seriously as an analogical argument against Representative Government, is open to the objection that the differences between a ship and a State are too great for any argument from one to the other to be of value. It was such fallacious analogies as these that Heine had in view in his humorous prayer, "Heaven defend us from the Evil One and from metaphors".

Footnote 1: Hamilton's Reid, p. 236.

Footnote 2: Bain's Logic, ii. 145.

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Transcriber's Note If your computer doesn't read Greek, or if you would like the transliteration, run your mouse over the Greek words (????????? ???e??) to see the approximation in Latin font. *p. 113: "(??e? s?p?????)" corrected to "(??e? s?p?????)". Aristotle wrote: "??? ?e?????? t? ?? ?at? s?p????? ???eta?, t? d? ??e? s?p????? ... " (~Categoriae 1a16-17) "... t? d? ??e? s?p?????, ???? ?????p??, ???, t???e?, ????." (~Categoriae 1a18-19) " ...p??ta d? t? e?????a ??e? s?p????? ???eta?."(~Categoriae: same document as above) but the book scans give the following: "He (Aristotle) explains that by "out of syntax" (??e? s?p?????) he means without reference to truth or falsehood:...." ... "??e?" would appear to be an error.