PROFITABLE FIELDS OF INVESTIGATION

IN MEDIEVAL HISTORY1

THERE is a striking sentence in the prologue of Froissart's Chronicles, which in the sonorous Tudor translation runs:

It is said of trouth that al buyldynges are masoned and wroughte of dyverse stones, and all great ryvers are gurged and assemblede of divers surges and sprynges of water. In lyke wyse, all sciences are extraught and compiled of diverse clerkes; of that one wryteth, another, paraventure, is ignorant. But by the famous wrytyng of auncient auctours all thyngs is ben knowen in one place or other.

The student of history knows that even if history were not every year in the making and if new archives were not still accumulating, the sources of the past will ever continue to be an inexhaustible repository. The thoughts of men are widened with the process of the suns. The point of view changes from generation to generation, and new interests are accentuated. The amount of new-found source material pertaining to medieval history is relatively slight when compared with the mass of inscriptions, clay tablets, pyramid texts, and papyri which have broadened the horizon of antiquity so greatly in the past fifty years, or the vast collections of modern history still unexamined and even uncatalogued in European archives. And yet there is no field of history which will better reward the investigator than that of the Middle Ages, and there is probably no field in which greater progress is being made.

When the chairman of the programme committee invited me to prepare this paper, he expressed the wish that it should consist of a general view of the field in question in relation to investigation, indicating subjects which have been reasonably well worked out, and the lines along which study can at present most profitably be carried on. With your permission, I will reverse the order of these ideas, and consider some lines along which the study of medieval history can most profitably be carried on, for it were an uninteresting task to undertake that of warning people away from unprofitable subjects.

The dean of American medievalists some years ago, in an article which all doubtless know, but which the student of medieval history may re-read with great benefit, because of its pregnant suggestiveness, has said:2

1 A paper read in a conference of students of medieval history, at the meeting of the American Historical Association in Boston, December 28, 1912.

2 G. B. Adams, "Present Problems of Medieval History", International Congress of Arts and Science, III. 126-128.

There is no other considerable portion of history, ancient or modern, that has been as yet investigated with such minuteness as that which embraces the history of Europe from the beginning of the fifth century to the end of the ninth, and we may add that, as a natural result, regarding all questions of importance in this field there is now a nearly or quite general consensus of opinion among scholars. . . . In view of this condition of things . . . I should like in all earnestness to raise the question whether the time has not now come when the main force of our vigorous and advancing historical effort should be turned into some other portion of the field; whether scholarly work in the first half of medieval history is not likely to find itself more and more shut up to the study of minute facts, which are, it may be, interesting in themselves, but of no essential influence on the real current of affairs. If this is true, and the students of medieval history continue in the future as they have in the past to spend their chief effort in this field, are we not running some risk of that danger which seems to threaten every science at some period of its history, the danger of the development of a more or less barren scholasticism? ... Have we not now reached the point in our study of the first half of the Middle Ages when we should expect and encourage, as the next step in advance, constructive rather than analytical work?

Unless this statement be understood to have reference to the larger things of institutional history, I trust that it will not seem captious to dissent in part from this opinion. Admitting the thoroughness of investigation in the case of early medieval history, can we yet believe that this period is so empty of opportunity to do analytical research, or that there is so completely settled an opinion regarding it? Is there not danger of our historical conclusions becoming too conventionalized and too fixed? The history of the medieval Church is one which has been notoriously conventionalized. It seems to me there is danger lest the great scholarship of men like Waitz, Roth, and Dahn compel too ready an acceptance, and our interpretation of early medieval history become too conventionalized under the great weight of their authority. Much analytical work may yet. frequently be done and with profit in new study of an old subject. The graduate student may not unnaturally think that the greatest immediate progress will be made by the investigation of new and unexplored subjects, but this is not always so. The actual extent of existing information upon a given subject in and of itself is sometimes difficult to find. I have often thought that a valuable proseminar training would be the endeavor to ascertain the present historical status of certain problems and accurately to define that status with a view to further research.

Historical research ought ordinarily to be constructive in its results. I do not mean to imply that there is no room for destructive criticism, for this form of writing is necessary and valuable in its place as a corrective. Yet in the main it is true that historical re

search ought to be constructive, not destructive. To prove a negative is ordinarily profitless.

The genuinely great product of historical investigation is foursquare its length and breadth and height are equal, and it has weight in proportion. Krumbacher's criticism of Drapeyron's L'Empereur Héraclius, "Ein dickes, aber ziemlich luftiges Buch ", is as terse as it is crushing a judgment. The critical review of established conclusions by careful examination of another's method and criticism, or a new interpretation of familiar sources, may be of more proportionate value to the advancement of history than the investigation of an entirely new subject. The door of early medieval history, I believe, is still wide open to modern "high-power" research, if I may so phrase it, to re-examine evidence and make new valuations and new determinations. One who has read that wonderful fourth chapter in Bernheim is likely to rise from it skeptical of even the most accepted interpretation of events. In other words, old subjects may become new in the light of better methods or a new point of view. For the point of view is often of as much importance as the thing seen from it.

Let me illustrate this by an example falling directly within this circumscribed field of medieval history, between the decline of the Roman Empire and the break-up of the Carolingian Empire. The legislation of Charlemagne would seem to be a subject that has been exhaustively studied, and no document more so than the capitulary De Villis. This famous ordinance, from Montesquieu to Inama-Sternegg, has been assumed to have had uniform application to all imperial domains. Kaempfer's Karl der Grosse (Mainz, 1910) which gives special attention to economic conditions, assumes the traditional view. Yet during the present year this assumption has been heavily attacked by a German scholar, Alfons Dopsch. In the course of a searching examination of Inama-Sternegg's classic conclusions, Dopsch denies that the capitulary De Villis was intended to apply to the imperial domains in general. He contends that the capitulary was local in its application, and in all probability was intended to apply to Aquitaine only, and that it was issued in 794 or 795 for the instruction of Frank officials who actually administered Louis the Pious's toy kingdom of Aquitaine. Now, while this most recent conclusion must be accepted with caution, it yet seems to me to show that we cannot accept too unreservedly the view that "regarding all questions of importance in this field there is now a nearly or quite general consensus of opinion among scholars". Krumbacher, Geschichte der Byzantinischen Litteratur, p. 1074 D. Dopsch, Die Wirtschaftsentwicklung der Karolingerzeit, part I. (Weimar, 1912).

5

So fundamental an historical matter as the separation of the East and West in the fourth and fifth centuries is still full of obscurities. It is easy to use broad generalizations and point to the antagonism of culture, institutions, language, and the influence of religious variance. But the actual detail of this slow process of separation is still an unwritten chapter, the constructive writing of which cannot be done until patient preliminary analysis has been made.

If we go back into the history of the Church in the third and fourth centuries, the same state of affairs obtains. Much of our understanding of church history in this period is still unemancipated from tradition, and in many particulars we have not advanced far beyond Ruinart and Tillemont. Even admitting that the erudition of these scholars enabled them to be independent of the lodestone of ecclesiastical tradition, or the coercive influence of church authority, nevertheless their critical apparatus was a clumsy instrument when compared to the edged tool of a Scheffer-Boichorst, a Wattenbach, a Julien Havet, or a Léopold Delisle. Church history in the centuries lying on either side of 300 A.D. still embodies much that is venerable and conventionalized, awaiting new analysis. Let me give a case in point, that of the Edict of Milan. Seeck has assembled strong evidence to show that the so-called "Edict of Milan" was not actually an edict at all, but a letter addressed by Constantine's colleague Licinius to some official in the East enjoining him to see that the Edict of Galerius was enforced."

I refrain from attempting to tabulate a list of the old wines that might be put into new bottles. Such a list would be merely a matter of opinion. But-voicing the opinion of others-as to profitable and unworked subjects of investigation in the early history of the Church, Harnack has mentioned two and Bury one.

1) The technical side of the spread of early Christian literature has not yet been investigated.'

2) Little attempt has yet been made to collect the opinions of Christians as to the personal character and regulations of the various emperors, although ample material lies in the Apologists, Melito, Tertullian, Origen, Lactantius, Eusebius, etc., as well as in the Sibylline Oracles and the Apocryphal Acts.8

Since Harnack indicated this subject, two theses have partially

5 E. g. the diffusion of Latin as the language of administration in the East in the fifth century; see the declaration of the bishops at the Council of Ephesus in 431 (Mansi, IV. 1282) and that of Chalcedon in 451 (Mansi, VII. 54 and 455). "Zeitschrift für Kirchengeschichte, XII. 381 ff. But compare the reply of Görres, Zeitschrift für Wissenschaftliche Theologie, 1892, pp. 282 ff.

Harnack, Mission and Expansion of Christianity, I. 376.

8

Ibid., II. 43, note 3.

covered it, one in French, the other in German, but the whole body of apologetic literature yet remains to be studied.

3) The ecclesiastical policy of Justinian is still a field for research.10

No one needs to be told that some of the richest results in medieval research in the last thirty years have been in the field of economic history. In some subjects, the American medievalist has an advantage over his European confrère, because, if he has imagination, he will discover that there are certain events in his own history that will enable him to visualize the history of the Middle Ages more clearly than they. He ought to have keener historical perception of their nature and operation. In 1893, in his memorable paper upon "The Significance of the Frontier in American History", Professor Turner quoted the words of the Italian economist. Loria: "America has the key to the historical enigma which Europe has sought for centuries in vain."

An admirable illustration of this is to be found in German history of the twelfth and thirteenth centuries. Lamprecht has pointed out that the great deed of the German people in the Middle Ages11 was the expansion of the German race eastward over the Slavonic nations and the making of three-fifths of modern Germany. The significance of the frontier in conditioning the history of Germany in the Middle Ages was little less than the significance of the frontier in shaping American history. But there is no German writer who has perceived it with the vividness with which Professor Turner has set forth the influence of American western expansion. The reason is not hard to find. The European frontier is a fortified line, an artificial barrier, running through densely populated regions. The stages in Germany's eastward expansion and the formative processes which made that expansion have largely become obliterated. In the United States west of the Alleghanies, the history of this process is still intimately associated with family and personal history. Men are yet living whose grandsires settled Ohio, Indiana, and Illinois, whose fathers made Wisconsin, Iowa, Kansas, and Nebraska. To the American the history of the making of the great West is still a vivid personal and family history. To the German scholar the history of the making of the Northeast is an academic question. The German pioneer is seven hundred years removed from the students of Berlin

'Dennery, “Les Sentiments des Chrêtiens à l'égard de l'Empereur d'après les Acta Primorum Martyrum et Selecta de Dom Th. Ruinart", Positions de Thèses de l'Université de Paris (1896); Morawitzky, Die Kaiseridee in den echten und unechten Märtyrerakten der Christenverfolgungen des Decius (Breslau, 1909). 10 Gibbon, Decline and Fall of the Roman Empire (ed. Bury), I. introduction, p. lx.

11 Lamprecht, Deutsche Geschichte, III. 349.