Editor Charles H. Smith's Note: Original pagination indicated within double brackets. Reprinted by permission of the American Journal of Science. Citation: American Journal of Science 242 (1944): 218-231.

    [[p. 218]] A recent article by A. L. du Toit, entitled "Tertiary Mammals and Continental Drift" (1944), was prepared as a rejoinder to an earlier paper, "Mammals and the Nature of Continents," by George Gaylord Simpson (1943). I cannot presume to continue the debate on behalf of Doctor Simpson, since I have no qualifications in mammalian zoölogy and paleontology, and moreover I do not know what his reactions may be to particular points in du Toit's reply. However, Simpson is now serving in the armed forces of the United States, and probably he will have no opportunity to give further attention to this matter until the end of the war. In the meantime it seems desirable, for the good of geological science, to comment on some parts of du Toit's discussion that concern the concept of continental drift in general, and to offer suggestions for employing more comprehensively the type of critical study exemplified by Simpson's paper.

    Simpson's discussion has two clear objectives: (1) to correct a number of gross errors that have appeared in published statements regarding mammalian distribution; (2) to use the established facts of mammalian distribution as a test in comparing the merits of three hypotheses concerning the geologic history of continents, including the concept of continental drift, known also as Wegener's "displacement hypothesis." At the outset Simpson clearly restricts his discussion to the evidence from mammals, with frank recognition that this evidence "is limited both in time and in scope . . . It is not claimed that the mammalian evidence alone is conclusive for the Cenozoic or that if it were, the same conclusions would have to be extended to previous eras." This concentration on data in his special field, with exclusion of other data--however important in themselves--attention to which would obscure rather than clarify the immediate issues, is a highly commendable feature of Simpson's discussion. He is under no illusion that reëxamination of evidence in his limited segment of the problem can "disprove" the hypothesis of continental drift or "prove" any rival [[p. 219]] hypothesis. It should be extremely helpful, however, to have each special aspect of this many-faceted subject examined critically by someone qualified to appraise that aspect. Unfortunately du Toit, in his reply, does not strictly respect this logical limitation of scope. True, he excuses his digressions on the ground that Simpson has failed to present some of his (du Toit's) views correctly, "or has omitted their other vital aspects." There seems to be no warrant, however, for du Toit's defensive plea, recurrent in his discussion, that Simpson "throughout his paper has entirely ignored the vital stratigraphic and tectonic aspects." Under any parliamentary procedure such comments would be ruled out of order, in view of Simpson's self-imposed restrictions in subject matter. Readers will be indulgent because of du Toit's open zeal for the concept of "drift," which he hastens to defend against every appearance of adverse criticism. Nevertheless his failure to restrict debate to subjects blocked out in the original paper serves to befog issues that should be kept clear, and makes his reply difficult to follow as a scientific analysis.

    My good friend du Toit shows commendable spirit in acknowledging certain of his own errors that were pointed out by Simpson, and I am prone to dismiss on the ground of unconsidered phraseology some statements to which, appraised at their face value, one might justifiably take exception. In his introduction du Toit says that Simpson "has set out to prove that the evidence of mammalian distribution . . . is adverse to hypotheses of trans-oceanic or drifting masses, but favorable to current views of stable continents." Surely we are not reduced to the level of a college debating society, or of a court in law, in which each participant is interested only in making the best case possible for the "side" with which he is aligned! Regrettably there are scientists who, whether consciously or not, reveal a stronger interest in advocating chosen viewpoints than in objective appraisal of all pertinent evidence. Those who are familiar with Simpson's cool objectivity in scientific reasoning will only be amused at any suggestion that he is such an advocate. Careful reading of his paper in question brings conviction that he "has set out to" examine and evaluate data that have been cited regarding the distribution of mammals, and to draw such conclusions as these data seem to warrant. Possibly some readers will have decided, on the basis of [[p. 220]] comments up to this point, that I belong to the camp unalterably opposed to "drift," and that I am singling out for criticism items of du Toit's paper that are aside from any main issue. I should like to clear myself of suspicion on both these counts. The Wegener hypothesis has been so stimulating and has such fundamental implications in geology as to merit respectful and sympathetic interest from every geologist. Some striking arguments in his favor have been advanced, and it would be foolhardy indeed to reject any concept that offers a possible key to solution of profound problems in the Earth's history. On the other hand, critical examination and rigorous testing of the concept in all its aspects do not imply unfriendly opposition toward an unwelcome intruder into the realm of "orthodoxy." Intemperate statements have been made on both sides of the question; but these merely reflect weaknesses of human nature. Du Toit seems to sense a strongly intrenched opposition in what he calls "current geology, sublimely unconscious of its impotence." What is this "current geology," which apparently is synonymous with "orthodox geology"? I associate with numerous men in the science, and find them, on the whole, a rather open-minded group, not given to arrogant judgments on the many abstruse problems of the Earth, and emphatically not uniform in their thinking on these problems. They find much in their geologic work to occupy their attention aside from the conflicting hypotheses on the history of continents. However, thanks to recent published discussions most of them know the ideas on continental drift, and are willing to give these ideas a fair hearing. To be sure, most of them are not active protagonists of the hypothesis.

    What should be done to improve the situation in "current geology"--other than to cultivate the open-minded attitude toward hypothetical matters in general and continental drift in particular? Du Toit states that he regards the hypothesis of drift "as essentially established by the Paleozoic and Mesozoic evidence." Does he mean established as fact, and would he have it taught among the established facts of geology? I fear that without more unequivocal evidence than we now can muster there would be many skeptics among the students. Perhaps he would be satisfied if numerous geologists entered into active and sympathetic discussion of the problem, treating it as a live issue in the science. I agree that this would be helpful, [[p. 221]] provided the discussion were governed by rigid scientific standards. The concept of drifting continents will be strengthened only by establishing a body of incontrovertible evidence in its favor; not by reiteration of diffuse and qualitative arguments, some of them based on data that are subject to question. The foregoing statement may be pronounced a truism, but it is worthy of emphasis nevertheless, as Simpson's analysis of mammalian evidence makes amply clear.

    Let us hope, therefore, that specialists in some other fields will emulate the example set by Simpson, by publishing critiques of evidence that comes within the range of their own competence. The result should be elimination of errors and other weaknesses from existing literature on the drift hypothesis, leaving a residue of data that can be accepted as dependable and significant. Simpson mentions certain erroneous statements and misinterpretations regarding reptilian distribution that appear in the literature on "drift." This is a large field, more critical in its bearing on the Wegener hypothesis than is mammalian distribution. Both Wegener (1929) and du Toit (1937) make much of the close resemblance between Triassic reptilian faunas found in South Africa and in South America. Simpson, reducing the available information to a quantitative basis, shows that 43 per cent of families and 8 per cent of genera are common to the two regions, with no identical species (1943). Du Toit replies that "the apparent lack of identical species among the Triassic reptiles of Brazil and South Africa should not strictly be pressed in view of the limited amount of collecting [and] the high ratio of new genera and species so far found . . ." But Simpson is not pressing the lack of identical species--he is merely stating the facts now in hand. Significantly he, a close student of vertebrate faunas, finds in the evidence a resemblance between South America and Africa of such small degree that it "opposes a direct land connection, even a connection by a direct bridge." This verdict is indeed in sharp contrast with that of Wegener, who was neither biologist nor paleontologist; and with that of du Toit who, after naming about a dozen reptilian groups common to certain lands in the southern hemisphere, states: "These lists could be considerably amplified, but should suffice when taken in conjunction with the associated floras and the fresh-water fishes and mollusca, to prove the continuity of the various parts of Gondwana from the [[p. 222]] Permian to the Rhaetic" (1937, p. 86). After studying Simpson's analysis of the reptilian evidence, the cautious reader will wish for equally expert advisers on the plants, the fishes, and the molluscs. When one is confronted with sweeping conclusions in these matters, truly a little learning is a dangerous thing.

    Du Toit (1944) questions the validity of the percentage method for expressing fossil faunal resemblances, as it is used by Simpson, on the ground that "the recorded proportions of determinable genera and species could be very different from their actual frequency in nature . . . The scantiness of such material cannot be overlooked nor the likelihood of unexpected discoveries that would appreciably modify current ideas." True enough; but is there any ground for supposing that a percentage of total forms common to two regions will be increased rather than decreased by future discoveries? The best we can do is to assume that known forms constitute a fair sample, and that proportions will not be radically altered even though the total may be greatly increased. Judgments, however tentative, must be based on evidence actually in hand. Surely expression of resemblances in the form of percentages gives a fairer overall picture of fossil faunas, and a more adequate basis for comparison with present conditions, than does a mere enumeration of genera or families whose distribution seems to harmonize with a given hypothesis of former land connections, to the exclusion of all other forms whose testimony is less favorable.

    Du Toit emphasizes that mammals "have been robbed of much of their value through their late appearance on the scene, well after continental rupturing is deduced to have occurred . . ."; and goes on to reiterate his opinion of several years earlier, that "geological evidence almost entirely must decide the probability of this hypothesis, for those arguments based upon zoo-distribution are incompetent to do so." After an analysis of several inherent weaknesses in the paleontologic data he concludes that "the existing paleontologic evidence can be accepted only with reserve by those favoring drift." Each of these quoted conclusions seems reasonable, and all of them seem consistent among themselves. However, they appear somewhat strange against the background of arguments that are urged without any detectable reserve by all protagonists of "drift," for whom paleontologic and biologic evidence seems to [[p. 223]] have a peculiar fascination. The high value placed by du Toit on the evidence from animals and plants bearing on the former "continuity of the various parts of Gondwana" has been cited on an earlier page. In like manner Wegener (1929, p. 101), agreeing with Stromer and others, tells us ". . . the distribution of the Glossopteris flora, the reptilian family of the Mesosauridae, and many other elements, makes necessary the assumption of a former great land mass uniting the southern continents." Authors of these positive statements do not warn readers that the biologic evidence is in any way equivocal. I find that college students who read the statements ordinarily accept them at face value and become convinced that a former close union of southern continents is demonstrated by the biologic evidence. Simpson has exposed the weakness of arguments based on the reptiles. Consideration of some problems presented by distribution of modern plants should give us pause also in accepting the strong claims based on ancient floras, including the famous Glossopteris flora. One example will serve as a cogent illustration.

    Primitive dogwoods of the genus Cornus, containing about 40 species, and its near allies, are widely distributed in eastern North America, in southeastern Asia, and in groups of islands in the south Pacific (Fig. 1). "Cornus is conspicuously absent from both South America and the region of Australia--a fact which has a bearing in tracing the early migration of the family into the Pacific" (Brown, 1928, p. 3). Cretaceous representatives ranged continuously northward from central North America into the Arctic region (Fig. 1). Aside from the problem presented by the distribution in Asia, the occurrences in oceanic Polynesia are of unusual interest. How were the plants introduced from the probable center of origin in North America across thousands of miles of ocean, not to mention the additional barrier of intervening climatic zones? Brown suggests that during the early history of the dogwoods, when there was no land connection between North and South America, seeds were transported "in masses of buoyant drift such as separate from the delta region of the Mississippi . . . , and float for thousands of miles under the influence of the ocean currents and wind." In this way, aided by the equatorial drift, the dogwoods may have gained a foothold on one or more of the Pacific isles, whence they were further dispersed southward, step by [[p. 224]] step, perhaps in part through the agency of birds. Distances between some of the existing islands are great, but some islands that were important in the dispersal may have disappeared during Cenozoic time. Further discussion of Brown's suggested solution has no place here; but it is worth noting that the distribution of the dogwoods poses greater problems than that of the Glossopteris flora, since it involves greater oceanic distances and more formidable climatic barriers. Moreover, the

Fig. 1. Distribution of primitive dogwoods. Modern forms are found in the black areas (A, B, C, D). Known Cretaceous distribution shown by vertical lining. (Forest B. H. Brown).

hypothesis of continental drift does not help explain the dispersal of dogwoods--rather it increases the difficulties. Obscure ways in which plants and also some animals must have been distributed during long geologic time intervals are suggested by other examples from the vast Pacific region. When these numerous problems are viewed together, emphasis that has been placed on the Glossopteris flora as "compelling evidence" of once-continuous lands seems dangerously near the unscientific procedure of selecting evidence to support a favored theory.

    [[p. 225]] There is no space here to discuss in detail the data from stratigraphy and invertebrate paleontology, although they deserve analysis by expert students. The stratigraphic data are, perhaps inevitably, diffuse and difficult to evaluate. Du Toit's arguments for the "Samfrau" geosyncline, extending from Argentina through South Africa to eastern Australia, are not easy to follow, although he tabulates much of the information in a stratigraphic chart which in his judgment shows an "extraordinarily similar sequence of events" in the regions concerned (1937, p. 62). Stratigraphers will ask what degree of uniformity is to be expected throughout a geosyncline extending at least 110 degrees in length--a question that is pointed by diverse formations of equivalent age in the shorter Appalachian geosyncline. In considering the "striking similarities" between stratigraphic units on opposite sides of the Atlantic, we should keep in mind that Nature has a strange way of producing near-duplicates, either in widely separated regions or in the same region at different times. Parts of the Torridonian sandstone of Scotland might well be mistaken for Old Red sandstone in the same small country if evidence of the stratigraphic sequence were lacking. Du Toit meets the argument that "drift" would require near-identity of facies and faunas on opposed coasts by assuming an original distance of several hundred kilometers between present shorelines of South America and Africa. This device has the twofold effect of avoiding certain difficulties and of admitting that the case for "drift" based on stratigraphic similarities is less convincing than a protagonist might wish.

    The most striking unit in du Toit's "Samfrau" belt consists of late Paleozoic glacial deposits; and without question the eloquent testimony that widespread ice caps reached to low latitudes in the southern continents furnishes the most cogent argument that has been offered in favor of continental drift. The marvelous displays of this evidence, particularly in South Africa, serve to create in the geologist a humble attitude and a feeling of tolerance toward all attempts to explain this great enigma. Students of climatology do not agree on the significance of the evidence, however; G. C. Simpson interprets it in favor of continental drift, but Brooks points out other possibilities (G. C. Simpson, 1930).

    [[p. 226]] With regard to tectonic evidence, on which du Toit lays special emphasis, students of structure are not prepared to agree on any sweeping conclusions. Many of the structural features cited in favor of "drift" are in regions of complicated geology that are known from reconnaissance studies only. Du Toit (1937, Fig. 13) shows structure-lines on opposite sides of the Atlantic that seem to match in most convincing style, until the reader learns that the lines represent approximate axes of broad regional uplifts dated as "post-Triassic"--surely not features that can be correlated with exactness in either space or time. Some of the structural data on which Wegener based plausible arguments were shown to be erroneous (Lake, 1922), but were cited again several years later as if they constituted valid evidence (Wegener, 1929, p. 77). Remarkable similarities are reported between the Cape Ranges of Africa and the Sierras of Buenos Aires in Argentina, and the northern end of the Appalachian belt of folding can be made to fit in striking fashion against the western termination of "Armorican" folds in the British Isles. Definite data of this kind of course arrest the attention of all serious students of tectonics, and establish the "drift" concept among the hypotheses that must serve as equipment in the present nebulous stage of megatectonics. Many of us, however, are not yet prepared to accept literally Wegener's interesting analogy of the torn newspaper as applied to Atlantic coasts, nor to entertain his extravagant suggestion--offered, it is true, with some reservation--that the geologic "controls" make his assumption of continental drift probable by odds of the order of a million to one (1929, p. 79). Structural data must be vastly amplified and much refined before they can provide the basis of any satisfactory comparison between opposed coasts of the Atlantic.

    If I were free to select the next block of subject matter related to continental drift for an expert audit, my choice would be the several redeterminations of geographic coördinates carried out in the effort to detect relative shifts of continental masses that may be now in progress. These projects have special appeal and importance, since they offer the possibility of demonstrating, within the present generation, actual horizontal movements of the kind envisaged in the drift hypothesis. Results of the several projects were reviewed by both Wegener (1929) and du Toit (1937). Data from Greenland and [[p. 227]] vicinity have come from comparison of longitude determinations at several dates in the nineteenth century with more recent determinations at the same stations. The older work used observations of the Moon, whereas some of the later values represent modern methods using stars in combination with radio time-signals. All of the results cited indicate westward movement of Greenland (and of Jan Mayen), at average rates that range from 4 to 25 meters per year. Wegener admits--more freely in the fourth than in the third edition of his book--the possibility of rather large systematic errors in the determinations based on observations of the Moon. How seriously does this factor impair the values on which the apparent movement rests? Du Toit (1937, p. 300) remarks that even if all the measurements referred to above be rejected, we still have two modern determinations at one Greenland station, with an interval of five years, which indicate westward movement at the rate of 36 meters per year, a figure "far in excess of the probable errors." The skeptic with only moderate qualifications in mathematics will answer promptly that a single example cannot be accepted as the basis of a confident conclusion, since conceivably it may involve errors several times the theoretical probable error.

    Wegener emphasized that all of the results indicate westward movement, and that this would imply an extraordinary coincidence of systematic errors in several independent determinations. This argument is weakened by consideration of additional data. Littell and Hammond (1928) published a determination in 1927 of difference in longitude between Paris and Washington, and compared the value with that obtained in 1913-14. According to the figures, the distance between the two stations increased in the 13-year interval by 4.35 m. +/- 1.0 m., or about 0.32 m. yearly. This result came to Wegener's attention while the last edition of his book was in press, and was included in a special appendix (1929, p. 220). Du Toit quotes the figures (1937, p. 300), but does not report a damaging refutation from Sir Frank Dyson, Astronomer Royal at the Greenwich Observatory, who stated that comparison of longitude values at Greenwich and Washington between 1913 and 1926 indicate a decrease of distance by more than 9 m., an average of about 0.7 m. per year (Nature, v. 124, 1929, p. 649). These contradictory results make it appear [[p. 228]] that the possible error of such determinations is at least several meters, at old established stations using the most refined modern methods. Since conditions for observations in Greenland are far less satisfactory at best, and since all but one set of available data involve to some extent the inaccurate lunar method, objective judgment can hardly indorse du Toit's statement, "it must therefore be concluded that a positive shift of crustal matter has been instrumentally observed." Why should we be hasty in reaching conviction in this matter? Modern methods of determining coördinates are closely accurate and will eventually reveal the truth. Jensen's Greenland station of 1922 can be reoccupied after the war, and the interval of more than 20 years should give a far better basis for judgment than any Arctic data now available. Even if future observations in this century should fail to indicate appreciable movement of any land masses, the hypothesis of continental drift would still be tenable, since movements may have been episodic, or at rates too slow to be detected within a human generation. To du Toit, after a review of the instrumental work in Greenland, "The reluctance of so many persons to concede the probability of such movements is hard to understand . . ." (1937, p. 300). I have no personal aversion to westward movement of Greenland--in fact I should be pleasantly excited by the vista of tremendous implications attendant on authentic confirmation of such movement. However, in this matter we are not dealing with probabilities. Astronomers and geodesists will eventually tell us that observations either have or have not demonstrated a shift of Greenland with relation to Europe. Until that time the only objective attitude is one of "wait and see."

    Perhaps it is inevitable that the early stage of testing a revolutionary concept, such as continental drift, begets some harsh critics and also some advocates with partisan zeal. Surely the time has come to treat this subject objectively, and to separate wheat from chaff in the voluminous argumentative literature devoted to it. Du Toit says, reasonably enough, "Critics of Continental Drift are apt to forget that this conception . . . is still being shaped and must experience revisions and modifications during its evolution." On the other hand, friends of the concept must expect that scientists generally will submit all aspects of it to close scientific scrutiny. [[p. 229]] If the concept is fundamentally sound it will survive all such tests; any parts of it that fail under scientific testing are not worthy of survival. It does not help the cause to accuse all its critics of "orthodoxy," with the implication that this state of mind is as unworthy as fascism. Protagonists of "drift" should welcome all searching study of the evidence by competent experts. Moreover, these protagonists would serve their cause by attempting to purge their own contributions of obvious weaknesses, since they have a human audience, endowed with limited time, patience, and objectivity. Soon after the appearance of Wegener's well-known book in the 3rd edition, I heard a prominent geologist who was sympathetic toward the drift hypothesis remark, "Wegener's book is at least 50 per cent dross, but it contains also some pure gold for anyone who looks for it honestly." Other readers, less objective, were repelled by the numerous obvious flaws in Wegener's presentation, and condemned the entire concept out of hand. Particular exception has been taken to one of Wegener's "geologic controls," which to the last he rated equal in value with mountain axes and other major features of the bedrock; namely, the late Pleistocene terminal moraine in Europe and North America, supposedly broken and the parts separated by westward drift of the latter continent. Du Toit rejects this part of Wegener's scheme, on the ground that it involves "an absurdly late date for the main movement under which those continents became separated." Indeed, Wegener appears to have forgotten entirely the Rocky Mountain deformation and other pre-Wisconsin tectonic episodes of the North American Cordillera, which he himself related to westward movement of the continent. Charitable commentators suggest that such inconsistencies may be overlooked on the ground that Wegener was not a geologist. However, his view regarding the terminal moraine is curiously vulnerable from the viewpoint of climatology, which is related to his own subject. He notes that the American moraine now enters the Atlantic fully four and a half degrees south of the moraine in western Europe, and thinks it more logical to have the moraines brought to the same latitude by his reconstruction which moves America northward. However, since at the present time annual isotherms are 10 or 12 degrees farther south in eastern North America than in western Europe, why is it difficult to believe that the ice cap reached farther south on the west side of the Atlantic?

    [[p. 230]] Du Toit has a revised version of the Wegener hypothesis which omits some glaring defects in the original. However, du Toit also is guilty of curious weaknesses which bring his effort into disrepute with some readers. As an example I quote the following passage, which is an attempt to explain certain tectonic features as the consequence of northward migration of the two postulated parental land masses: "Laurasia in moving from its more or less equatorial position towards the North Pole--where the meridians were convergent--became subjected to an E.-W. compression, revealed in its orogenies from the Carboniferous onwards and especially in that of the Urals, whereas Gondwana moving towards the equator--where the meridians were divergent--became put under tension in an east-west direction, which ultimately led to its fracturing and wide dispersal. Such would explain the vital difference, why, in contrast to their similar "equatorial" and peripheral crumplings, Laurasia should display dominantly meridional folding but Gondwana meridional rifting." (1937, p. 305). The reader may well rub his eyes and ask whether the author offered these suggestions seriously. The suggested mechanism could be made credible only by proposing a plausible force, powerful in its operation, which urged every molecule of all land masses, on both sides of the equator, inexorably toward one point near the north geographic pole. Shall we invoke terrestrial magnetism as a possible cause of orogeny? It is true that such lapses from the plane of objective analysis do not affect the merits of the basic concept of "drift." However, an avowed protagonist presumably sets out to win his readers to his own views, and should try to avoid destroying their confidence instead. The case for continental drift deserves more discriminating presentation.

    The frankly critical tone of this brief discussion may brand it as an unfriendly attack in the eyes of proponents of the "drift" concept. Zealous believers commonly follow the motto, "He that is not for us is against us." However, I have devoted time to the discussion only because of a genuine interest in the hypothesis of continental drift. I have an interest also in some other hypotheses designed to explain major features of the earth in terms of its history. No one of these hypotheses has yet won me as a protagonist, and at present it is inconceivable to me that any scientist could adopt one such [[p. 231]] hypothesis to the exclusion of all others. Perhaps a definite choice of creed brings some peace of soul that is denied to the scientific skeptic. However, those who declare unswerving loyalty to any hypothetical concept appear to settle into an "orthodoxy" of their own, which interferes with breadth of scientific vision. In the genetic study of major earth-features I can not believe we have arrived at a stage that permits discarding the method of multiple hypotheses. In this study the several concepts at our disposal are essential tools, which should be sharpened continuously with the abrasive of objective criticism.

WORKS CITED.

Brown, Forest B. H.: 1928, Cornaceae and allies in the Marquesas and neighboring islands. Bernice P. Bishop Museum Bull. 52, Honolulu, T. H.

du Toit, A. L.: 1937, Our wandering continents. Oliver and Boyd, Edinburgh.

_____: Tertiary Mammals and continental drift. Amer. Jour. Sci., Vol. 242, March, 1944.

Lake, Philip: 1922, Wegener's displacement theory. Geol. Mag., Vol. 59, pp. 338-346.

Simpson, G. C., and others: 1930, Discussion on geological climates. Proc. Roy. Soc. London, Vol. 106 (B), pp. 299-317.

Simpson, George Gaylord: 1943, Mammals and the nature of continents. Amer. Jour. Sci., Vol. 241, pp. 1-31.

Wegener, Alfred: 1929, Die Entstehung der Kontinente and Ozeane, vierte umgearbeitete Auflage. Friedr. Vieweg und Sohn, Braunschweig.

DEPT. OF GEOLOGY,
YALE UNIVERSITY,
NEW HAVEN, CONNECTICUT.

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