Copyright © 1992 American Institute of Physics
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The analysis is based on 165 interviews on 19 high-energy physics experiments approved 1973-1984 at Brook haven National Laboratory, Fermi National Accelerator Laboratory, and Stanford Linear Accelerator Center. In most cases, interviews were conducted by project staff in the interviewee's office using standardized question sets for each interviewee category: physicists, graduate students, and engineers and technicians.
GENERAL ORGANIZATION AND MANAGEMENT
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Origins of Collaborations
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The period covered by our sample began two years after Fermilab became operational, one year after the SPEAR storage ring at SLAC became operational, and included the inauguration of the Fermilab tevatron, the Cornell Electron Storage Ring, and the PEP storage ring at SLAC. The impact of these accelerator developments on the formation of collaborations was dramatic. Five of the seven collaborations that performed the Fermilab experiments in our sample came together to design experiments for Fermilab's opening; a sixth was a response to the tevatron. Three of the six collaborations that performed SLAC experiments came together to plan PEP experiments. And the CLEO collaboration formed to build a detector for the Cornell storage ring. Even among the experiments not linked to a major accelerator innovation, there were two whose collaborations formed to take advantage of innovations in beamline or targets. While it would be an oversimplification to label the formation of collaborations as "accelerator driven," because some of these experiments also aimed to produce novel detector designs, to test particular theories, or to resolve experimental controversies, the implication of this sample is that the construction of a new accelerator is a sure way to stimulate a shake-up in the pattern of working relations among high-energy physicists.
Experimenters discovered their common interests, or at least the willingness to work together in a collaboration, through a number of channels. Friendships, not surprisingly, were often important to collaboration organizers, and there is evidence of people who met as far back as college trying to find their way into doing an experiment together. But between the sheer number of people needed to mount even the smaller experiments in our sample, the vagaries of individuals' schedules and commitments, and the need to tap particular forms of expertise, only two collaborations were successfully assembled entirely out of the pre-existing professional relationships and personal contacts among the organizing collaborators. The rest required organizers to go beyond their circle of physics friends. The organizers of an under-staffed proto-collaboration sought others through their grapevines and by buttonholing colleagues at conferences or seminars, but other, more formal means were also employed. There are two instances in our sample of collaboration organizers approaching physicists they had never met on the strength of those physicists' published accomplishments. Summer studies to discuss possible PEP experiments spawned both PEP and SPEAR experiments. Three proto-collaborations held open meetings where potentially interested physicists could come to discuss the proposed experiment and meet the organizers. And five experiments were performed by "shot-gun marriages"—collaborations that laboratory administrators had brokered after receiving multiple proposals to use or build similar apparatus.
Interviewees were reluctant to talk about the reasons experimenters do not join collaborations, even when not required to identify the individuals or institutions involved. But two factors that blocked consummation of a collaboration were apparent. First was the perception that a physicist or his institution were over-extended and unwilling to cut back on other activities; no proponent of an experiment wanted its fate to depend on the contribution of someone whose best efforts were going elsewhere. Second was the difficulty an experiment's proponent could have within his home institution. There was one instance in our sample of a university physicist being unable to participate in an experiment he helped to design, because he could not convince his departmental colleagues, who administered the research funds, that support of his experiment made sense from a departmental perspective.
There is no apparent formula for picking collaborators successfully. Our sample included one collaboration where a falling-out between long-standing friends infected physics discussions involving their students; the members of that collaboration have not tried to work together again. The sample also included two instances of strangers becoming fast friends and long-standing collaborators. It does seem generally to be the case that brokered collaborations did not endure beyond the experiment that brought the collaborators together. That does not mean that brokering was a bad practice. If an experiment was attractive enough for multiple proto-collaborations to propose it, but the proposers were either unable to find each other on their own or unreasonably optimistic about their abilities to perform the experiment on their own, a brokered collaboration was the only way to get the experiment done. Rather, the simplest criterion for an experiment's social success—did the experimenters continue to work together?—should be modified for brokered collaborations.
Size and Composition of Collaborations
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The organizers of experiments understood that they needed to attract a vaguely-defined critical mass of physicists to an experiment in order to appear credible to administrators whose duty it was to assess the feasibility and desirability of a proposal. And a collaboration's leaders then had to deploy their resources so as to succeed in building, running, and analyzing data from the proposed experiment. These necessities pressed physicists to form collaborations to match the scale of their experiments rather than the norms previous experimentation; one experiment organizer intended to create an experiment for five to ten physicists but saw "the physics necessity" drive the experiment up to 40 collaborators. However, these necessities did not induce physicists to "pad" proposals in order to have a margin of safety should some part of the experiment prove unexpectedly taxing. To the contrary, interviewees usually described experiments as understaffed, shoestring operations, even when the collaboration seemed unusually large. For example, one interviewee, a post-doc on the experiment being studied, recalled feeling shocked that this experiment had nearly three times as many physicists as his thesis experiment, yet he then found himself terribly overworked during the experiment's construction.
Such individual impressions appear to have a collective reality: in five of the experiments in our sample, collaborations had to add institutions after the proposal had been approved in order to carry through the experiment; in three others, which were second or higher in a string of experiments, the collaboration added one or more new groups prior to the proposal in recognition of the difficulty in carrying on with their current complement; and in only one of the five brokered collaborations did the merging of proposals require the collaborating institutions to pare down their personnel.
Competition for the field's limited funds and personnel was an obvious factor in keeping collaborations lean in relation to the tasks they undertook. Our sample included one experiment that was successfully redesigned to require less material and people in response to the need to be competitive with other proposals vying for an empty experiment site at the accelerator laboratory. A quantitative study analyzing, over time, the number of proposals, the level of funding, the number of high-energy physics groups, and the availability of experiment sites could perhaps assess the importance of competition in keeping down the size of collaborations. However, the overall, qualitative impression from the interviews was that the understaffing of experiments was a cultural norm that many American physicists liked. This impression is strengthened by the dearth of similar impressions in the interviews of European physicists.
Understaffing had at least four advantages. First, it reduced resistance to tapping the knowledge and experience of those outside the collaboration (the "not-invented-here" syndrome). For example, our study of subcontracting indicates that LeCroy Electronics has successfully made a business of producing electronics modules that could be sold to many different experiments, and in one of the experiments in our sample, a physicist and engineer canvassed manufacturers to "learn what was available" for the processing of plastics that had desirable properties for the experiment.
Second, understaffing made it easy for every collaborating institution to be responsible for an important construction project and preempted worries about whether an experiment would address enough physics issues to satisfy the collaborators' needs for distinctive accomplishments. Almost absent from the interviews are stories of "turf disputes" with respect to either apparatus building or data analysis. There was only one experiment where the need for more personnel to build the apparatus induced among the graduate students a fear that there would be an inadequate number of thesis topics; here, a collaboration retreat for physics discussions yielded more than double the number of possible topics for the existing population of students.
Third, understaffing inhibited collaborators from hiding or underestimating problems because nobody could afford to be unreliable in an operation on which others were working so hard. At least among the collaborations of our sample, collaborators were sufficiently open with each other about their difficulties, or lack thereof, that there were several occasions in which collaborations profitably redeployed their resources in order to address areas that turned out to be more troublesome than initially expected. And fourth, understaffing limited the spread of credit for the making of an illuminating discovery. During an experiment's construction, one junior faculty collaborator recalled overhearing a conversation among the experiment's "gurus" over how they would divide the Nobel Prize they expected to receive for the experiment's results.
A minority of interviewees worried about the effects of doing experiments on a shoestring. The most common complaint was that graduate students spent time on intellectually unchallenging construction tasks when they could have been preparing and comparing various simulation and analysis programs. One interviewee feared that physicists were undertaking construction tasks which they were unqualified to do well and safely because of the budgetary impact of hiring skilled laborers.
Even though collaboration organizers kept collaborations as small as possible, the larger experiments created administrative positions within collaborations. Executive committees sought to insure that evolving component designs did not undermine collective coherence, to reallocate resources should the development of a particular component run into snags, and to provide the several senior members of the collaboration with a formal forum for discussing and reaching decisions on the collaboration's internal and external administrative problems. Software coordinators regulated changes to codes and programs used widely within a collaboration. Deputy spokespersons oversaw construction or data runs. And ad hoc publications committees served as referees between the producers of a physics analysis and a collaboration as a whole. Issues that were either the stuff of collaboration meetings or within the purview of a senior collaborator's unilateral actions in smaller collaborations were thus initially thrashed out in formalized subgroups of larger collaborations. But even for most large experiments, meetings of the entire collaboration remained the forum for making most decisions on basic strategies for designing, running, and producing results from the experiment.
One physicist, who worked on one of the smaller, early experiments from this study, left high-energy physics rather than work in ever larger collaborations. Some who have managed to keep working on smaller experiments looked at the larger collaborations with a mixture of perplexity and disdain. But the people on the inside found satisfaction in large collaborations even when they had expected to feel uncomfortable. One experiment organizer, who became a physicist to avoid becoming like his father, the president of a medium-sized company, still felt "pleasantly surprised" at the manageability of the personal interactions of a 40-physicist experiment, and succeeded in understanding and contributing to the experiment from top to bottom. He feared that he will not be pleasantly surprised again, but he was not leaving the field. Another interviewee found that the worst is over, for the moment, for high-energy physicists—that while the experimenters in the larger collaborations from our sample struggled to operate as a unit, his "super-large collaboration" at CERN forgoes unitary operations as "too unwieldy" and gives much more autonomy to his institutional unit, "which is a very manageable size."
Experiment organizers tended to worry about getting enough collaborators for an experiment rather than putting together a complementary blend of skills and sub-specialties. One organizer remembered welcoming a university group into a collaboration because "at that time we needed to have bodies." Another stated that balancing skills in building a collaboration was meaningless because everyone typically had to learn plenty of new things in the course of doing the experiment; to flesh out his collaboration, he looked for people with "a good reputation, solid people" who would inspire "mutual confidence" among all the collaborators. Only three collaborations (aside from two Soviet-American cases discussed below) came together as a result of complementary expertise among the participants, and of these three, one was an atypical experiment, poorly suited to graduate education, in that it aimed to make only one measurement in order to search for one hypothetical particle.
The overall impression from our interviews was that individual American physicists were presumed to be familiar with, if not expert in, all phases of an experiment, and a university group encompassed all the skills needed for an experiment. Throughout our sample, physicists invariably wrote and managed experiments' computer programs; though a few physicists were known as "computer-oriented" and specialized in working on data acquisition systems for experiments, they tended to be employed at national laboratories. Some physicists saw themselves or certain of their colleagues as primarily apparatus builders or data analyzers, but everyone wanted graduate students to participate in both types of work in the course of their thesis experiments. The one meaningful distinction among groups during the years covered by our sample was between those specializing in electronic and bubble chamber experiments. One electronic experiment was especially attractive to physicists in bubble-chamber groups who wished to switch or expand their groups' style of work.
The two Soviet-American collaborations in our sample both had their origins in particular experimental techniques that the Soviet groups had developed. Both Soviet and American interviewees commented on the conditions that created this grounds for collaboration. One Soviet interviewee reported he was labelled a physicist in the U.K. and the U.S.A., though he was considered an engineer in the U.S.S.R.; one of his American collaborators came away with the impression that individual Soviets specialize more permanently with the consequence that they become very adept at what they do and less able to keep up with experimental innovations. An American participant from a different U.S.-U.S.S.R. collaboration believed the Soviets have created a class of people "between what we would call engineers and physicists;" these people, though not interested in the physics results, did take data shifts and therefore were included as authors for experimental papers. The apparent Soviet practice of building groups out of experts in the technologies of experimental techniques as well as experts in the physics of elementary particles was perhaps due to the placement of Soviet researchers in Institutes of the Academy of Sciences rather than in universities. However, one Soviet interviewee also pointed out that cultivation of novel experimental techniques was essential to Soviet participation in international collaborations outside the U.S.S.R. Because the ruble was worthless outside the U.S.S.R., Soviet physicists could not bring money to a foreign experiment and therefore had to bring expertise and equipment that was not readily purchased in the west.
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During the period covered by our study, two types of institutional groups participated in high-energy physics experiments: research groups at the accelerator laboratories and university groups. Because academic high-energy physicists in the U.S.A. were funded as university groups, whose size and budgets were limited by both university and governmental dynamics, and because accelerator-based groups were fewer in number, collaborations could become larger only by including more academic institutions. The addition of institutions brought collaborations both extra resources and organizational complexity. This fundamental trade-off was probably the greatest source of daily friction within collaborations.
When a new institution was added to a collaboration, not only did the collaboration gain more physicists, it also potentially gained access to the institution's research and development laboratories, machine shops, computers, and an inexpensive supply of undergraduate labor. In the competition to join collaborations with experiments that are likely to be approved, physicists at universities with strong resources had an obvious advantage over those at universities with fewer resources, and the physicists at the accelerator laboratories were best situated of all. 12 of the 19 selected accelerator experiments had in-house collaborators, and university physicists often spoke of the desirability of access to the computers and machine shops of the accelerator laboratory at which they wished to do an experiment. Furthermore, inclusion of research groups at the accelerator laboratories may have actually reduced organizational complexity given the relative ease with which in-house physicists oversaw the installation of apparatus. (Three of the six collaborations without in-house collaborators included groups located within commuting distance of the accelerator and a fourth tried but failed to interest accelerator-based physicists in its experiment.) However, university groups during the period covered by our sample were neither impotent in the face of a lack of collaborators at the accelerator nor necessarily dominated by the accelerator-based groups with which they collaborated. Four of the six experiments without in-house collaborators did build large detectors, and there was one instance of a collaboration between university and accelerator laboratory groups where the university machine shops took on work for the laboratory physicists, who could not afford to pay their own shop to fabricate the desired components.
The collaborations in our sample took any of three approaches to their multi-institutionality and did not necessarily adhere to any one approach throughout the experiments they performed. Sometimes collaborations sought to take advantage of their multi-institutionality by making it a framework for their working relations. Sometimes collaborations ignored their multi-institutionality as irrelevant or ill-suited to the tasks they faced. And sometimes collaborations found multi-institutionality created outright liabilities that had to be lived with for the sake of getting the experiment done.
Collaborations tried to make a virtue of multi-institutionality when physicists wished to divide labor for efficiency or duplicate labor to insure reliability of results. The former was frequently employed by collaborations that built large, multi-component detectors that were considerable research and development projects in and of themselves. In 12 of the 19 experiments, most of the collaborating groups worked independently on components once the collaborations had set basic design parameters. When such management worked well, interviewees remembered healthy, productive intra-collaboration competition: each group sought to gain credit for building the best component, and to avoid becoming known as the builder of the component that limited the quality of the experiment's measurements. Such management entailed risks and difficulties as well. There were instances where the independently built components, once assembled at the laboratory, produced systems effects that made for extra work for some collaborators, although our sample of successful experiments included no examples of a component being substantially rebuilt in response to systems effects. There were also instances where one group's component caused or threatened to cause a setback to the collaboration's timetable, although our sample included only one example of an individual physicist seeming sufficiently blameworthy to leave the collaboration.
Systematic, institutionalized duplication of labor, as opposed to ad hoc double-checking of important or unexpected results, was much less common, presumably because physicists who were so uncertain about each other that they desired duplication usually did not collaborate in the first place. Only four collaborations tried duplicating labor; in three of them, one of the duplicating lines of research collapsed, and in two of these three, the efforts at duplication caused hard feelings within the collaboration. However, in the one collaboration that kept up the practice, physicists recalled the intra-collaboration competition as a "healthy tension;" the "really acrimonious" disputes that arose when the two institutions reached conflicting results were honorably intellectual, "and we always went out and drank beer after the big fights."
Most collaborations sought to ignore their multi-institutionality during data analysis, even if they exploited it while building apparatus. Their usual strategy was to concentrate data analyzers at the site of the best available computer for "crunching" the data and to base individual analyses on collectively produced data summary tapes and programs for reconstructing events in the detector. Seven collaborations also ignored their multi-institutionality while building their experiments. The most common precondition to this practice was that the experiment's technical drive stemmed not from someone conceiving of an improvement in detector design or strategy, but rather from academic or foreign physicists conceiving of an innovation in target or beamline and needing to work out their ideas in close coordination with collaborators at the accelerator laboratory. In these cases, the important technical divisions in the experiments did not coincide with the institutional divisions in the collaborations, and the collaborations assaulted their multi-institutionality via telephone, telex, e-mail, or meetings. In certain collaborations, multi-institutionality created outright liabilities that became apparent after it was too late for corrective action. In two cases, the needs of junior faculty to use an experiment to gain tenure within their home institutions induced behavior that other collaborators found objectionable. In one of these cases, a junior faculty member tried to set up a data-analysis chain based at his institution—presumably to demonstrate his competence in that phase of the experiment and to provide a basis for claiming personal credit for discoveries or important measurements—when the rest of the collaboration preferred to work collectively within the framework set up by a collaborator who was especially skillful in programming and analysis. The junior faculty member's collaborators found him secretive and his efforts counter-productive. In the other of these cases, the collaboration made two junior faculty at different institutions co-spokespersons, in order to avoid granting one the advantage of the title and role in his campaign for tenure, only to find that they competed to impose their personalities on the experiment and could not resist questioning and seeking to overturn each other's decisions. This collaboration found their behavior polarizing and a source of administrative confusion. Finally, there was one example where a disagreement between two physicists over the physics of the experiment took on an institutional cast in the eyes of one of the physicists' graduate students, who felt that the other physicist was unreasonably dedicated to finding objections to his analysis. Had the two physicists and student all been in one institution, the student could have appealed to a department chairperson or dean to mediate, but within the collaboration there was nobody with effective power over the physicists to mediate, and the student had no recourse to persevering in the face of unconstructive criticism.
Those collaborations in our sample that found multi-institutionality problematic all lived to publish results. As one of the co-spokespersons in the two-spokesperson experiment retrospectively realized, the collaboration contained plenty of "hungry people" who were not going to let problems between the spokespersons deprive them of data and publications, and a collaboration of bosom buddies leading "a bunch of bums" would have done far worse. However, the evidence here did suggest that collaboration organizers would be wise to consider how they can satisfy the needs of junior faculty in advance of committing themselves to including particular institutions, and that all post-doctoral physicists should resist, as professionally unethical, the temptation to involve their students in their intra-collaboration disagreements over physics.
Hierarchies and Social Relations
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Everyone in a collaboration knew who was a full professor, an assistant professor, a postdoc, a graduate student, an engineer, and a technician, but privilege of rank was rarely in itself the cause of strained social relations within collaborations. There was a dearth of stories about collaborations in which individuals inappropriately "pulled rank" on their juniors or lacked appropriate respect for their seniors. Occasionally students or postdocs claimed that senior people were making "the decisions that matter," but did not specify what the issues were. However, most physicists remember their collaborations as participatory democracies where decisions were made by consensus and where individuals were distinguished by knowledge, ability, and sometimes the degree to which they had invested their careers in the experiment. Engineers reported that they avoided collaboration meetings, which they felt turned into gripe sessions where "the physicists put you on the hot seat." But they professed comfort in dealing with physicists on a one-on-one basis. Graduate students and engineers enjoyed a symbiotic relationship in an experiment; the students kept the engineers posted on discussions in collaboration meetings and the engineers taught the students "hands-on science," which could prove professionally useful during slack periods in the market for high-energy physicists.
What strained social relations in our sample of collaborations more than the simple span of ranks they contained, were structural problems imposed by their size, their inability to reward and discipline those faculty-level members who could operate autonomously within their home institutions, and the pressures of competing with other collaborations. These factors sometimes had unequal impacts on collaborators on the basis of their rank or institution. But they were never cause for a physicist to leave an experiment in progress.
Six of the more recent collaborations in our sample bowed to the complexities of coping with their larger sizes and created executive committees that took care of some portion of the collaboration's business outside of collaboration-wide meetings. In five of these six instances, the collaboration meetings, which continued to be run as participatory democracies, remained the most important forums for discussions of the experiments' progress and results. Physicists not on the executive committees of these collaborations more or less cheerfully accepted that the committees were more effective or efficient than collaboration meetings at keeping the several groups coordinated, making decisions or reaching compromises on issues for which there was no collaboration-wide consensus, setting forth a collaboration "party line" in policy struggles with laboratory administrators or industrial suppliers, or just giving strong-minded senior people a more intimate setting in which to argue with each other. Junior people on these experiments retained the power to manage the work they were undertaking. In one of these five collaborations, when the graduate students felt the executive committee was overstepping its bounds in considering ways to divide up possible dissertation topics, the students themselves met and decided on a division of topics. The students' division was the one that was followed.
In the sixth case, interviewees viewed the executive committee's meetings as more important than the collaboration meetings, and physicists at opposite ends of the hierarchy were all initially unhappy with the collaboration's administration. The spokesperson felt the executive committee members were too parochial in guarding the privileges of and seeking credit for their home institutions, and insufficiently sensitive to the needs of the experiment as a whole; a graduate student felt the committee spent too much time debating who would present results that had not yet been achieved and too little time on the problems of technical coordination. As the collaboration neared completion of assembling the experiment's hardware, the graduate students were upset by uncertainty over the experiment's potential to generate enough dissertation topics. In contrast to the collaboration discussed above, the students were not able to resolve the issue on their own. The collaboration saved itself by holding a retreat; after several days of small-group and collaboration-wide discussion, all were convinced that the experiment could generate double the number of needed dissertation topics.
The collaborations in our sample lacked the administrative powers to reward and discipline their faculty-level members. The collaborations could not grant or withhold promotions, raise or lower pay, increase or decrease the number of students or postdocs a faculty member could hire, or provide quicker or slower access to a machine shop or research and development laboratory. All of these powers rested with the several institutions that employed the collaborators. Collaborations' lack of powers became problematic in three kinds of situations.
First, when a narrowly focussed experiment involved many more faculty than it had physics topics to address, the collaboration was prone to divisive disputes over the paucity of rewards available. In one experiment in particular, where the physicists designed and built a detector to search for a hypothetical process, collaborators became sensitive over who received credit for the narrow range of results all wished to produce, and collaboration meetings featured rancorous arguments over who would present results at upcoming conferences. This particular collaboration enjoyed a long life by investigating many ways the hypothetical process could occur and by serendipitously discovering another use for the detector. Other collaborations that performed specific search experiments disbanded after they had achieved their designated results, leaving some of their faculty members mildly disgruntled with their personal "return" on their investment of time and effort.
Second, when experiments could address multiple topics but only one topic at a time, or could yield data susceptible to multiple treatments in data analysis, collaborations were "Balkanized," and the inability of collaborations to discipline faculty led in some cases to easy dissolution. Individuals or small cliques of faculty would usually adopt one of the possible lines of inquiry and then fight over whose interests deserved collaboration-wide support. Although present in the upsilon string of fixed-target experiments (See Probe Report), this phenomenon was especially apparent in collider experiments. Electron-positron annihilations create only those particles whose masses equal the energy of the collision; thus collaborations comprised of physicists interested in particles of different masses always faced a contentious issue in deciding at what energy the accelerator should be set. Interviewees from one experiment in particular recalled "endless meetings" and "semi-annual blood lettings" when the collaboration had to take a position on what energy the collider should be run at and thus what kinds of events the collaboration could study. So long as the collider ran well and the data "pie" was growing, the collaborators could at least tolerate, if not enjoy, arguing over the size of the data "slices" and which data runs should be dedicated to whose favored accelerator setting. When the data grew harder to come by and the collection of a meaningful amount of data on some topics effectively meant no further data would be collected on others, the collaboration could not discipline its members to hold to a subset of physics goals that was consistent with what the accelerator was likely to deliver. Instead, the collaboration disbanded so that the faculty members could give more attention to other experiments, even though collaborators believed there were still data worth collecting.
Third, collaborations' inability to reward or discipline collaborators preempted or inhibited collaboration-wide debate over the design of detector upgrades. In our sample, the separate institutions applied for funding and controlled access to their laboratories and machine shops, and in two instances in our sample, that power was exercised independently of the collaboration. One collaboration ended debate over two competing designs for upgrading a particular component when one of the proponents of one of the designs succeeded in obtaining funding to build his design. In another collaboration, the original builder of a component had to accept a consultant's role to another institution's physicists in the building of an upgraded version because he could not commit his university's resources to building the upgraded version. (Although not noted by any interviewee, this autonomy of constituent groups within collaborations may limit the scope of collaboration democracy; long-range planning is removed from the arena of collaboration meetings, where physicists of all ranks may participate, and reverts to the arena of discussions over funding, where senior physicists typically predominate.)
The pressures from inter-experiment competition became divisive within three collaborations where one or some collaborators presented claims to have made a discovery or a difficult measurement. The delicate art, which physicists have long practiced individually, of balancing the fear of appearing foolish for publishing an erroneous claim against the fear of losing credit should a competitor publish a correct claim first was not readily practiced in these collaborative settings. In one case, the group leaders, convinced of the reality of a discovery and fearful of being "scooped," together drafted publications without giving others a meaningful opportunity to make criticisms or suggestions. They effectively dared the rest of their collaborators to remove their names from the author list of papers and suppressed debate that could have "fine-tuned" the paper to reflect more accurately a collective assessment of the certainty of the claims and the weak points of the experiment. In another case, a collaboration yielded to the enthusiasm of the proponents of a discovery claim when the accelerator laboratory's administration declined to provide beamtime to double-check the claim in advance of its public dissemination. The claim turned out to be erroneous, and the non-proponents now speak of the lack of appropriate skepticism and openness among the claim's proponents. In a third case, a disagreement between two collaborators, who were apparently struggling with a personal falling-out as well as their physics differences, blocked prompt publication of results. A third collaborator, who expressed dissatisfaction with his home institution and was presumably eager for a success that would gain him some leverage in his efforts to improve his situation, was disgusted that others published their measurements first while his collaboration struggled to draft papers to which all collaborators would subscribe.
There were no examples in our sample of an institution quitting a collaboration or being driven out of a collaboration because of destructive social dynamics, and there was only one instance of an individual physicist leaving an experiment in progress because of grievances with his collaborators. That incident did not involve structural, collaboration-wide strains, but stemmed from the physicist having lost the confidence of his collaborators in his ability to carry out the task for which he had taken responsibility. Institutions have left collaborations when they judged an experiment had reached the point of diminishing returns in comparison to their other options, and individuals often left collaborations when their institutional affiliations shifted. But virtually never did an institution or individual leave an experiment "in a huff" over treatment received. The overall impression from our sample is that physicists tolerated inequities and conflicts in order to be part of an experiment.
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The two governmental funders of high-energy physics in the U.S.A., the Department of Energy, which is a direct descendant of the Atomic Energy Commission, and the National Science Foundation, came into existence shortly after World War II and established traditions of funding academic researchers through their universities. While high-energy physics experiments have long since outgrown the capabilities of individual universities, university units continued to be administrators of research funds for their high-energy physicists. This arrangement made the cost of individual experiments difficult to calculate and compare, because a university's contribution was embedded in the cost of all the activities supported by its contract for high-energy physics research. However, there were at least two powerful reasons, besides institutional inertia, for this fragmented administrative framework: collaborations have been transitory while universities have been stable fixtures in the institutional landscape; and university groups have needed the potential to regulate the activities of individual faculty in the interests of maintaining a mix of activities that best served the needs of the department and its graduate students. Several interviewees had the impression that the funding agencies are increasingly insisting that experimenters provide a unified proposal for their consideration. Rather than funding an experiment through the support of several institutions' proposals, the agencies used the accelerator laboratories as central money-managers of funds for an experiment with several institutional collaborators. That was how the experiments on the PEP accelerator at SLAC were handled. This collaboration-centered study, however, is not a good foundation for generalizing on the evolution of agency practices.
Most of the experiments in our sample were funded through universities; this policy encouraged the multi-institutionality and the internationalization of collaborations. Interviewees sensed there were imprecisely defined limits, which were best left imprecisely defined, on how much money would be spent on the research of any single high-energy physics group. Thus any group with the ambition to design and build an expensive experiment, or to stretch an extant experiment to make more measurements than the group could handle, had to convince physicists from other institutions or countries to dedicate some portion of their institutions' resources to the experiment. (Research groups of the national laboratories were an exception to this statement; they also had the option of building expensive apparatus as a "facility" that would be available to other high-energy physics groups, and our sample included two experiments that used such facilities.)
Because our sample consists only of experiments that received funding and ran, one would not expect to find much evidence of funding procedures breeding resentment. And, in general, one would not have expected funding procedures to breed resentment because attracting collaborators (and their resources) and establishing scientific merit were neatly in tandem. However, occasional funding-based problems did crop up for the experiments in our sample. There was one apparent case of conflict over how closely theory and experiment must be related in order for an experiment to be worth funding; one group of experimentalists claimed that a similar proposal to the one selected for study here had been denied funding, but that a second version received favorable, generous treatment because theorists had subsequently developed a basis for predicting what results the experiment should achieve. In one collaboration between sets of relatively cash-rich and labor-rich institutions, responsibilities had to be carefully divided so as to give the labor-rich institution enough work to hold its interest without undermining the confidence of the cash-rich, who would have preferred to buy commercially available apparatus. In two collaborations where all but one of the institutions was DOE supported, members of the NSF-supported institution felt they had to be made responsible for a distinctive, clearly differentiated part of the experiment in order to gain the necessary NSF support to participate in the experiment. And finally, in another instance, one collaboration diversified its funding sources to the point where both the high-energy physics and the nuclear physics program offices of both DOE and NSF were involved; during the time it took to get the commitments from all four offices straightened out, the administrations of some of the involved universities loaned funds to their physics groups to begin work.
University-based experimentalists took for granted that their contracts with the funding agencies would cover travel, the support of post-docs and graduate students, and the operation of any university laboratories or shop facilities dedicated to the high-energy physics group. Uncertainty existed over the prospect of acquiring funds to buy the materials and services needed to construct major, new detector components. The uncertainty placed a premium on reusing equipment, and six experiments in our sample did not require much U.S. capital. Some experimentalists found virtue in this necessity and took delight in bypassing the extra scrutiny that came with requests for capital funds, short-circuiting the long lead-times associated with building new components, and quickly mounting experiments with previously built apparatus plus what could be built within the confines of the secure budget.
The prospect of applying for capital funds could not be indefinitely postponed, and university units took a variety of approaches to managing their members' needs to build major pieces of apparatus. At one extreme was a group whose members "don't really know what each other is doing" and relied on the low probability that several members would want to build apparatus in a given year. In the middle were groups with sub-groups that aggregated some of the members' needs, and groups whose members worked independently but appointed a Principal Investigator with the authority to work out an intra-group distribution of the resources provided by the government. At the other extreme were groups that operated as a unit, collectively deciding on the experiments they would or would not pursue.
EXPERIMENT STRINGS, DETECTOR DEVELOPMENT, AND NEW TECHNOLOGIES
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At its outset, this study effectively defined an "experiment" as the activity between the time physicists banded together to obtain an experiment number from an accelerator laboratory to the time that physicists stopped trying to publish papers on the basis of what they were allowed to do by virtue of having that experiment number. Embedded in that definition are the assumptions that the criteria for assigning experiment numbers were consistent and corresponded to meaningful changes in experimental research. The post hoc reasonableness of those assumptions is dubious. Among the fixed target experiments in our sample, new experiment numbers were assigned to collaborations that came together to build an experiment "from scratch," collaborations that upgraded some or all apparatus, collaborations that added to their extant apparatus, and to one collaboration that changed virtually nothing and whose members remain perplexed by the assignment of a new number. The collider experiments in our sample were all built from scratch, assigned a number at their inception, and almost never reassigned a number even though they usually investigated several topics and were sometimes upgraded extensively. (The one exception to this generalization was an experiment that received a new number when the detector was moved wholesale, without change, to a different accelerator laboratory; the interviewees considered the data-taking runs on the two accelerators to be all one experiment.)
Given the lack of consistent significance to experiment numbers, experiment-by-experiment comparisons according to the assigned numbers is problematic. However, because fixed-target experiments were usually done in "strings," and because interviewees speak of collaborations that performed strings of experiments as units with social continuity and integrity, it is reasonable to compare how collaborations developed and exploited their experimental capabilities to create strings and to seek an explanation for why physicists performing collider experiments perceived those experiments to be freestanding, that is, independent of predecessors and successors.
Strings were generated when physicists applied for approval to run a variation in some element(s) of a previous experiment. In our sample of 19 experiments, 15 were fixed-target experiments, and 11 of these 15 can loosely be classified as second or higher in a "string" in the sense that some of the principal organizers of the experiment had worked together on a similar, previous experiment. (Three of these 11 would not qualify as part of a string if the definition were tightened by requiring organizers from more than one institution to have worked together on a previous experiment.) Of the other four fixed-target experiments, two were organized with the intention of becoming foundations for a string and one gave rise to ambitions for starting a string. Only one of the 15 fixed-target experiments in our sample neither stemmed directly from nor directly inspired hopes for another experiment.
The forms of continuity that attracted interviewees' attention were in instrumentation and design. When some of the same physicists received a new experiment number for data runs that reused some or all of the apparatus of a previous run or that used entirely new apparatus in a design that recapitulated or embellished the design of a previous run, those physicists viewed the two experiments as a string. The most common strategy for generating strings of experiments in our sample (11 of 14) was to hold constant the beam and target while varying the detector. Beam- and target-varying strings appear to have been rarer for both administrative and intellectual reasons. Administratively, beamlines were within the jurisdiction of the laboratory and managed in the interests of multiple users, while targets, even though they served individual experiments, had to conform to the safety and design parameters of the accelerator. Thus producing a series of variations in beam or target enmeshed experimenters in additional layers of laboratory management and oversight. Intellectually, beam- or target-varying strings required experimenters to deal with a wider range of phenomena, and their proponents had to be willing to become conversant in a larger number of specialized domains than proponents of strings that varied detectors. In two of the three beam- or target-varying strings, the experiments shifted between measurements of sub-nuclear and nuclear parameters.
Detector-varying strings are divisible by how experimenters modified their detectors and how they justified the modifications. Detectors were modified by either adding components so as to extend the range of data the collaboration could collect or by upgrading extant components so as to increase the efficiency or resolution of the detector. Experimenters justified receiving additional beamtime for these variations by arguing that they would either permit a better investigation of the previous experiment's physics or permit the examination of subjects that the previous experiment had not (or could not possibly have) planned for. There is no correlation apparent between type of detector development and type of justification.
Collaborations performing strings tended to be risk-averse in modifying their detectors. Only two collaborations pursued mid-string detector changes that involved new and risky techniques, and both of these collaborations were adding components to a working core. Collaborations that upgraded individual components or entire detectors only pushed at the limits of the capabilities of current techniques or canvassed manufacturers to find the expertise needed to employ a particularly desirable material. Even the two collaborations that added new and risky components to their detectors had either redundant detection capabilities elsewhere in the detector or a back-up version of the component based on conventional technique. Apparently, collaborations that felt that their working apparatus gave them a solid claim to ongoing beamtime would not risk their credibility with the laboratory administration on making untried technology work, but they could bear the risks of innovation when the new components duplicated conventional apparatus.
Interviewees felt that justifying successive experiments on the basis of new topics to be addressed was the better strategy. One interviewee, who did receive permission to augment his detector in order to examine the same topic as a previous experiment, opined that proposals for such follow-up experiments promise more than they can realistically produce in order to give the follow-up proposal the impact of its predecessor. Another interviewee from a collaboration that had recently rebuilt its detector admired the shrewdness of his collaboration's spokesperson, who presented the case for further beamtime as though the collaboration were on an orderly march through a series of measurements. The interviewee thought that the point of further running was for the collaboration to build up the size of its data sample in order to let the experimenters search for subtle effects once the data were taken. However, the spokesperson recognized that "somehow you can't really say that [to a laboratory's Physics Advisory Committee]. So you say you want to measure this quantity. So he chose a very difficult quantity to measure, which required a lot of statistics." Thus the collaboration got beamtime to improve on its earlier work under the guise of pursuing a particular measurement. (At the end of the run, the collaboration still did not have a large enough sample to make the advertised measurement, "but we did a lot of other things.")
Whatever their experimental tactics and strategies, the memberships of collaborations performing strings changed greatly over time. However, at the core of every such collaboration in our sample was a small, stable partnership of physicists who dedicated a substantial portion of their research careers to the study and use of particular particles, processes, or techniques. Rather than always starting from scratch to read the direction and data needs of physical theory or to develop detector technologies that could best exploit the next advance in accelerators, these physicists sought improvements to and extensions of their existing experiments, and opportunistically exploited intersections between their subjects and the conceptual framework of contemporary physical theory. Such partnerships of physicists accumulated the experience and resources that attracted others who were "shopping" for an experiment or who discovered they had their own, usually shorter-term interests for doing an experiment in that particular area. The more enlightened and self-secure of these partners granted leadership opportunities to more junior people who had the inspiration and ambition to organize and run an experiment within their bailiwick.
Thus strings appear to be the product of a combination of social, technical, and scientific conditions. When a small set of physicists can form a mutually beneficial partnership to exploit the possibilities of technical flexibility and incremental improvements in the study and use of particular particles or processes, the result is a string of experiments. The fact that nearly all the fixed-target experiments in our sample were parts of strings would seem to indicate a cultural preference among experimentalists for working in this vein. The one fixed-target experiment in our sample that neither stemmed from a preceding experiment nor inspired hopes for a further experiment was socially unique in that it was performed by a collaboration in which theorists and accelerator physicists together outnumbered experimentalists.
Physicists doing experiments at colliding-beam accelerators faced strongly different technical conditions than physicists at fixed-target accelerators. Whereas fixed-target accelerators split and focus their beams on a variety of targets either for direct experimentation or to generate a variety of customized, secondary beams with which physicists could perform experiments, colliders only generated interactions between the one or two particles they accelerate. (All the collider experiments in our sample were performed on electron-positron colliders; henceforth our use of the word "collider" should be understood to refer to electron-positron colliders.) Furthermore, whereas experimenters at fixed-target accelerators stretched their apparatus out linearly behind the target, experimenters at colliders surrounded collision points with concentrically nested detector components because the experimenters' frame of reference and the center-of-mass frame of reference coincided. Consequently, experimenters at colliders were less able to distinguish their experiments by controlling what entered their detectors, and they faced more severe engineering problems and constraints in modifying their apparatus. The continuity typical of fixed-target string collaborations—successive modifications of apparatus in order to delineate all facets of a particle's properties and experimental uses—was technically more difficult to achieve for a collaboration working on a collider experiment. None of the four collider collaborations in our sample pursued a string strategy.
All experiments running simultaneously on a given collider were limited to studying the output of the same collisions, so the four collider collaborations in our sample established their identities by stressing one or another form of detection technique—e.g., tracking of charged particles, detection of neutral particles, or measurement of particle energies—rather than one or another particle or process to be studied. With direct competition to make discoveries, or at least the most precise, meaningful measurements from the same collisions, three of the four collider collaborations tried to maximize further their chances of making a distinctive contribution by developing new technology. One collaboration developed a novel detector component; one used a known technique in a novel design and on an unprecedented scale that together required innovative, difficult assembly procedures; and one used conventional components but in a novel configuration. The fourth sought competitive advantage by shunning novelty in favor of being ready to take meaningful data as soon after the collider turned on as possible.
The unity created in collider collaborations by commitment to developing a detection technique, however, was often limited by differences in the physics interests of collaborators. All the collider collaborations chose or were required to cover as much of the solid angle around the collision point as possible. One collaboration was divided between those interested in events that were primarily detected at low-transverse angles to the collision and those interested in high-transverse events; another collaboration split over the reliability of detection at low-transverse angles, where it was difficult to separate signals from interactions of particles in the two beams from the passage of non-interacting particles in the beams. And all collider collaborations had to reach a position on what energy the accelerator should be set for upcoming runs. Because electron-positron annihilations create a state of pure energy equal to the sum of the energies of the colliding particles, there is no possibility of investigating particles (and their decays) that are not created at the energy of the collisions. Two collaborations were divided over the best setting for the accelerator because collaborators wished to use the detector to study different particles.
Collider collaborations did not perform strings because they could not readily exercise discrimination over what entered their detectors, nor readily add to or modify the components in their detector, and thus their principals could not unite around examining in different ways the physics and experimental uses of particular particles. Instead, collider collaborations were coalitions held together by a common interest in a particular detection technique and a particular accelerator. The demise of either spelled the end of the collaboration. While none of the collaborations in our sample experienced detector failure, accelerator laboratories have let older accelerators deteriorate as they shifted their best personnel to the creation of a new accelerator. Interviewees in all four collaborations pointed to either the decline of the accelerator or their inability to control its running energies as ending their experiments before data-taking possibilities had been exhausted.
ROLE OF SPOKESPERSON
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Narrowly speaking, a spokesperson has been an administrative convenience, an individual designated to speak for the collaboration to laboratory management and to inform collaborators of laboratory requirements. However, the first communication between collaboration and laboratory management—the presentation of the experiment proposal to the laboratory's Physics Advisory Committee—has been appropriate for a collaboration's intellectual leader, the physicist who had thought most thoroughly about the experiment and invested him/herself most deeply in seeing the experiment performed. Subsequent communication rarely required the conveyance of intellectual passions and strategies, but in the words of one interviewee, "it's certainly a hell of a lot better if the spokesperson does offer intellectual leadership, because if you don't know what you're talking about to a lab, you really can't get the lab to understand what you want." Thus collaborations usually made an experiment's instigator their spokesperson. The role of spokesperson, another practitioner observed, was both cherished as a symbol of scientific initiative and despised for the administrative tasks that come with it. While not all physicists disliked serving as administrators, collaborations in the later period covered in this study appear to have generated more managerial tasks, and the meaning of being spokesperson and the role the spokesperson plays seem to be in flux.
In the 14 fixed-target experiments in our sample, the intra-collaboration role for the spokesperson after the experiment's approval was generally to coordinate the activities of the collaborators and to oversee the installation of the apparatus at the laboratory. These experiments did not generate issues that made the spokesperson's duties seem particularly critical to the development of the experiment, in his/her own or collaborators' eyes. The spokesperson for one of these experiments said nothing in his interview about being spokesperson, and a non-spokesperson interviewed for a different experiment could not recall who the spokesperson was. Others spoke of "collective decision-making" or "pure democracy" as the practiced form of governance. When hierarchies based on professional rank were evident to the participants, the spokesperson "had no particular role" beyond that of other group leaders. When the office of spokesperson for a collaboration did not function well, as was the case in the collaboration where the two co-spokespersons would reverse each other's decisions in their competition to stamp their personalities on the experiment, the collaborators still managed to build a detector that out-performed its competitor at the laboratory.
While the spokesperson's role in fixed-target experiments, even when less than efficiently filled, did not make or break any of the experiments in our sample, only once did any spokesperson of a fixed-target experiment relinquish the role as more trouble than it was worth. Spokespersons did not retain their title because the duties were light; several commented on the burden of familiarizing themselves with all aspects of what they were coordinating. Rather the task of coordinating collaborators was itself evidence of scientific leadership and initiative. Because collaborations had so few powers to reward and discipline their members, spokespersons had to reason and persuade their way through the conflicts and misunderstandings that inevitably arose, and retention of their position was evidence of their skills of persuasion. Junior faculty on the experiments in our sample thus particularly coveted the office of spokesperson in the belief that it would help their tenure campaigns; five of the collaborations had junior-faculty spokespersons for the experiments in our sample, and a sixth had a junior faculty spokesperson for a later experiment in a string.
The four collider experiments and three of the four fixed-target experiments approved in or after 1979 and not part of a string according to the more restrictive definition (see p. 14) contained managerial practices not found in the earlier fixed-target experiments. All the collider experiments and two of the three fixed-target experiments had some sort of administrative substructure, such as deputy spokespersons, executive committees, or ad hoc committees, to handle collaboration business. Three of the four collider experiments shifted spokespersons over the course of their runs—one on an annual basis—while the third fixed-target experiment changed spokespersons because the initial spokesperson, chosen for his administrative abilities and favorable institutional position, resigned as spokesperson when he changed jobs. All these collaborations apparently found the administrative burdens of overseeing an experiment to require social innovation.
The management of collaborations has certainly needed to be strengthened as the drive to produce more refined, sophisticated measurements required larger, more complex detectors that absorb the design, construction, and analysis efforts of more physicists. In most of the more recent experiments, neither the individual spokesperson nor the collaboration as a whole could coordinate and evaluate the many tasks of the collaboration's members. Thus they resorted to the use of committees or additional officers to handle some collaboration business. And thus even experiments that did not create substructures showed signs of needing them, as when an autocratic spokesperson delegated authority to a junior colleague, or when a loosely run collaboration lost track of the status of its individual members' projects.
The practices of shifting spokespersons and selecting them for their administrative skills or position also suggest that the characteristics of some experiments and collaborations required that managerial skills be placed ahead of intellectual initiative in collaboration governance. This seems particularly true for collider experiments, whose geometry of concentrically nested components made them more tricky to build and whose acceptance of all events emanating from collisions led to more possibilities for experiments within experiments. In one collider experiment, the initial spokesperson, whose invention of a new kind of detector component was the collaborations's raison d'être, resigned because he found himself to be a poor technical coordinator and wanted to concentrate on the problems of the particular component he had invented. In another, senior collaborators at the outset recruited an engineer to manage the coordination and assembly of components. In a third, the spokesperson retained his position, which he described as chief-executive-officer for construction, but relied heavily on two senior collaborators for help in dealing with a unique industrial supplier whose product was not meeting specifications. And all four collaborations encountered managerial problems because their members were divided by their interests in various types of physics or their willingness to trust components that detected particles traveling parallel and close to the beam. When an experiment consisted of an intricate construction project followed by the investigation of several intellectually distinct physics topics, there was little role for enduring leadership, and shifting the burden of managing such stressful operations and internally divided organizations may keep resentments towards any individual from accumulating.
ORGANIZATION FOR DETECTOR CONSTRUCTION, DATA ANALYSIS, AND COMPUTER PROGRAMMING
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The primary factors in producing a collaboration's organization for building a detector were logistical convenience, the availability of appropriate personnel, and technical experience. Large components and delicate components were best built near or at the accelerator to minimize transport problems. Tricky components were best designed and built at institutions with high-quality engineering staffs, while mass-produced, labor-intensive components were best built at institutions with access to inexpensive, often undergraduate help. Also when particular physicists had prior success in building a similar type of component, they tended to recapitulate their earlier success in their later experiment. Rarely did interviewees speak of being "end-use driven," that is, building particular components because they expected them to be strategic in examining a particular branch of physics. And rarely did collaboration organizers report that they consciously evaluated possible individual collaborators with an eye to acquiring a balanced set of physics interests that was suitable to building a particular detector.
Although responsibilities for building parts of the detector were often assigned or claimed independently of physics interests, these responsibilities nevertheless had medium-term ramifications in some collaborations. A large task for many of the collaborations in our sample was the reconstitution of the mass of digitized, electrical pulses, which made up the experiments' raw data, into categories and events that physicists could use to make calculations or measurements. The group that built a component would typically be responsible for writing the software that performed this "pre-analysis," and the people who did this work would find they had an initial comparative advantage over others in working on physics topics that made heavy use of their component. Such was most often the case in multitopic experiments on which students from more than one university were simultaneously writing dissertations. However, when experiments ran for longer than was needed to collect data for "one generation" of graduate students and postdocs, comparative advantages based on detector-construction assignments tended to dissipate. The new students and postdocs would be initiated into the experiment in a less specialized fashion, and they would want to pursue more complex topics that combined the demonstrated capabilities of the several detector components.
The quantity of work that went into writing the one-of-a-kind programs to convert the signals from individual detector components into physics information insured that collaborations building a many-component detector for a multi-purpose experiment would treat those programs as communal property that all should use and nobody should duplicate. However, for the more tightly focussed electronic experiments and the experiments that collected data on film, the possibility of multiple analyses of raw data was real. Furthermore, with the advent of interactive data-analysis programs that permitted physicists to process data from their terminals rather than submit batch jobs, even physicists in many-component experiments efficiently performed "cuts" on the data to create individualized data samples at a higher level of generality than previously. These conditions posed a "federalist" dilemma to collaborations: to what extent should reconstruction programs and general data samples be subject to central collaboration authority to insure homogeneity and commensurability of results reached by physicists from different institutions; and to what extent should local customs in data management be allowed to flourish in order to cross-check results and to support the widest possible spectrum of tastes and interests? The former policy, by being more efficient, would seem preferable when a collaboration is in heated competition with others to reach an exciting result, while the latter, by being less prone to allow collaboration-wide errors, would seem preferable when a collaboration has a physics niche more to itself. However, the practices of individual collaborations appear to have hinged more on the personal preferences and working relations among a collaboration's leaders than on the external conditions collaborations faced. Some physicists saw anarchy in the use of multiple programs at a general level and trusted in their collaborators' abilities to spot any flaws in widely used programs; others saw dictation in the collaboration-wide use of someone's favored set of general programs and trusted in their collaborators' abilities to argue their way professionally to a consensus should the use of multiple programs yield conflicting results.
Because computer programming has been so entwined with the extraction of physics from the data, experimentalists have largely done their own programming and have not relied heavily on trained specialists in computer science or engineering. Some interviewees viewed themselves as "computer-oriented" and specialized either in the data acquisition problems of getting all the electrical pulses onto identifiable parts of magnetic tape or in the software-management problem of making sure the programs to handle the data from the several detector components work together harmoniously. Our sample contains fragmentary evidence that computer-oriented physics has become a viable, informal sub-specialty analogous to specialization in the design and construction of certain kinds of detector components. Interviewees from two of the collaborations in our sample spoke appreciatively of innovations in computation that were made by individuals who had made a point of thinking about the common factors in experimenters' uses of computers rather than just the needs of a particular experiment. However, collaboration organizers did not generally have to make a point of finding people who already had or were willing to acquire the computation skills an experiment needed.
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International collaborations appear to be children of necessity. None of the international collaborations in our sample originated in prior personal or professional contacts as was commonly the case with domestic collaborations. From the perspective of U.S. experimentalists (which is the perspective of most of our interviewees) any of four factors behooved experimentalists to seek foreign collaborators. First, a foreign group had developed an experimental technique that U.S. physicists wished to use and learn. Second, an experiment required more manpower and money than could be readily raised domestically. Third, a laboratory director spotted common interests in proposals from domestic and foreign collaborations and brokered a merger of the two. And fourth, U.S. experimenters with a working detector desired more beamtime than a U.S. accelerator had the will or ability to provide. For the non-American experimentalists, collaborating with Americans was a means for performing experiments that the foreigners' domestic infrastructure could not support.
Four kinds of problems, beyond the obvious ones of language, appear in international collaborations: technical, cultural, logistical, and political-legal. The experimenters were left to their own devices to deal with technical and cultural problems; logistical and political-legal issues involved people outside the collaboration.
Technical problems cropped up in collaborations that had their origins in the complementary expertise and resources of the participating institutions. In these collaborations, the foreign physicists preferred to build their components in their own laboratories and shops. When the foreign physicists' nation employed different metrics or standards from the U.S.A., the integration of the components with the rest of the detector and the American accelerator required additional work. That work was well within the power of physicists to perform, and there were no examples of such problems not being routinely dispatched.
Cultural tensions were most noticeable in U.S.-Japan collaborations. This condition may be due as much to the recentness of Japan's large-scale entry into high-energy physics as to the depth of cultural differences between Americans and Japanese. Both of the U.S.-Japan collaborations in our sample resulted from over-extended U.S. collaborations with approved experiments using the 1979 Implementing Arrangement on the US/JAPAN Cooperation in the Field of High Energy Physics to acquire additional money and people. In neither case had there been prior institutional ties among these American and Japanese groups; nor did the process of pulling together a proposal provide an opportunity for any of the physicists to grow accustomed to dealing with each other before the pressures of building and assembling components threw them into intense and close working relationships.
Japanese and American physicists from both of the U.S.-Japan collaborations in our sample noted that Americans argued more vociferously and showed less deference to hierarchical relationships and that the Japanese held more of their discussions outside formal meetings. In one collaboration, detector designs were so far along before the Japanese became involved that the Japanese physicists joined American groups and did not build anything as a group unto themselves, while in the other, the Japanese did build a particular piece of the detector as a group. However, it is difficult to generalize on the consequences of these arrangements for easing cultural tensions within the collaborations. In the former collaboration, a U.S. physicist still felt disoriented by Japanese processes for reaching consensus or differentiating open-ended projects from delimited tasks even though the Japanese were not operating as a group. In the latter collaboration, a Japanese physicist still felt burdened at having to be more vocal than was comfortable for him even though he was part of a Japanese team. The significance of these differing arrangements may reside more in their subsequent consequences for Japanese physicists than in their impact on how these collaborations performed their experiments. Two American physicists from the collaboration where the Japanese did not function as a group expressed concern that the Japanese physicists became "over-Americanized" and were having trouble doing science through Japanese institutions, but the senior Japanese physicist in this collaboration was glad that his juniors had to work so closely with Americans because he wants high-energy physics to be part of a general opening of Japanese society to international influences.
Cultural differences, though less pronounced and less common, did sometimes surface between West European and American physicists. The differences lay not in the group dynamics of collaboration meetings but in contrasting assumptions over the degree to which collaboration-wide rules, especially for handling raw data and reconstructing events, should be instituted over the autonomy of the participating institutions. One European-American collaboration, which was formed at the behest of the accelerator laboratory's director, spent two years arguing over whether a pan-European system for reconstructing events in this kind of experiment should be the norm for the collaboration or whether all participating institutions should retain the privilege of using and modifying their own programs. The Europeans apparently won by strength of will borne of having already forsworn local autonomy in the course of creating the pan-European system. In another all-American collaboration, a European who was working for one of the American institutions feared the dispersed physicists would reach incompatible, incommensurable results because the collaboration was lax in instituting collaboration-wide controls over basic analysis programs; he did his best to make the on-line programming a structure for post-run analysis.
The logistical problems of an international collaboration usually obliged the foreign groups to pick up and move to the experiment's site. That strategy could have posed severe fiscal and administrative problems stemming from exchange rates and the rules that governments impose on the use of public monies, but U.S. laboratory administrators were flexible about juggling laboratory funds in order to cover those things that foreign physicists needed but could not buy and not to cover those things that foreign physicists provided for the whole experiment. Only one of the international collaborations in our sample was successful in maintaining significant work at several sites and using meetings and communiqués to keep everyone informed. Two others tried to have at least multiple centers for data analysis: one gave up because the foreigners could not readily keep the analysis software up to date, while the other persisted but ended up publicizing erroneous results because one group could not readily scrutinize the work of the other. One set of collaboration organizers, when confronted with the interest of a foreign physicist who had independently designed an experiment similar to theirs, agreed only to accept his participation as an individual and rejected having his university as an institutional collaborator because "it would have just made our life unnecessarily more complicated."
The potential for political-legal problems has been most spectacular in American-Soviet collaborations, (though one West European physicist required a laboratory director's help with immigration authorities when the experiment lasted longer than his visa). The physicists' primary fear was that their governments would treat them as pawns in diplomatic maneuvers over events outside of physics, and their primary response was to "conspire together to fight each other's [governmental] bureaucracies." But more importantly, the collaborations' leaders built physics-based friendships that could survive the diplomatic problems that physicists themselves created; two East-Bloc physicists from experiments in our sample defected—one after and one during their experiments—but the leaders of their groups kept up their relationships with American physicists. Less spectacular, politically-based problems stem from differences in science policies of the nations of collaborating physicists. One international collaboration encountered difficulties in its formation because the experiment was slated for running on an accelerator in the process of being upgraded; while the high-energy physics community of the nation that was investing in the improved accelerator could not politically afford to let technical uncertainties about the upgrade inhibit the planning of experiments, the physicists of other nations had a much more formidable job convincing their administrators of the wisdom of committing resources to an experiment on an unproven accelerator. In another international collaboration, physicists of different nations had to contend with the sense that they needed different types of accomplishments to maximize their chances of winning governmental support for future experiments.
Despite the difficulties of working in international collaborations, almost all the participants found that the value of building relationships with foreign physicists more than outweighed the difficulties. Time and experience should erode cultural misunderstandings, and further innovations in communication and transportation may alleviate logistical burdens. But as experiments grow larger, longer, and more expensive, legal and political impediments to participating in a foreign experiment can only grow more threatening. Not only will physicists need visas and travel privileges, but also their spouses will probably want the right to pursue their careers during a long stay in a foreign country. Not only will physicists have to argue that an experiment is likely to make a significant contribution to physics, but also that their participation in an experiment will fit into a broader framework of policy for the use of national resources for research.
DISSEMINATION OF RESULTS
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Interviewees for six experiments from the early period of this study made little or no mention of conference talks. For the rest, conference talks were an important, though not always rare, commodity that a collaboration exercised care in distributing. Talks were invariably considered valuable for bringing results quickly to the wider community's attention, though there was variance on the standards of review collaborations imposed on talks as compared to publications. And talks were invariably considered valuable for conferring credit and granting exposure to the collaboration's lesser-known members who had driven forward a particular line of analysis—though just who decided the deserving individual varied across collaborations.
Although the question set was not designed to elicit the standards that collaborations set for conference talks, some variations in opinion are apparent. Two collaborations imposed less stringent standards on talks than on publications. In one, "a result that you think is right within reason" could be presented at a conference while journal articles had to be as trustworthy as possible for future physicists. In the other, laboratory seminars were used to try out questionable results or ideas. By contrast, interviewees from three experiments reported that the collaborations rigorously reviewed the content of at least some talks; in one case, a collaboration waited several months to present a central result to the accelerator laboratory's seminar, even though the collaborators felt certain about the result, while they worked at making the result as convincing as possible. Such discipline, however, did prove difficult to enforce pleasantly. One of the collaborations suffered from "bad citizens giving impromptu talks" while in another "a bit of feeling" was aroused when one collaborator blocked another from giving a seminar at an accelerator lab.
Except when choosing someone to present important results at major conferences—in which case the presenter's reputation and speaking abilities as well as his contribution to the results were taken into account—most collaborations did not use collaboration meetings to decide who spoke at conferences. A variety of ways were used for delegating such decisions. In two collaborations, the spokesperson either openly or effectively decided; more commonly, the group leaders collectively made the decision; when institutional lines remained meaningful through the course of an experiment, conference presentations were sometimes granted to institutions with each group responsible for deciding who would speak. Two collaborations did collectively decide on conference speakers. In one, the responsibility for analyses was well enough defined that there was rarely any issue over who should present results; in the other, most collaborators were concerned with one central topic, and collaboration-wide discussion insured equity and curbed "a few individuals who like to give all the talks." In general, where disputes over who gave presentations was occasional, it seems collaborations delegated responsibility for making those decisions, but where such disputes were rare or frequent, collaborations collectively made those decisions.
For the production of journal articles, the power of writing the first draft was inconsequential in the overwhelming majority of experiments. In only one instance, where the experiment's leaders felt themselves to be in a race to claim a discovery, has anyone reported that the mass of collaboration members were denied the opportunity to criticize an initial draft. For the experiments approved before 1976, there were no formal intermediaries between a paper's drafter and the collaboration as a whole. But in six of eleven experiments approved since 1976, collaborations have created committees to work with paper drafters before or after the collaboration as a whole has discussed the results. As collaborations have grown larger and more geographically far-flung, there are obvious economies in minimizing the number of times a collaboration meets to discuss the merits of a particular proposed publication, but there are no neat criteria for distinguishing the collaborations that did and did not institute such procedures.
Interviewees reported instances where papers sailed through intra-collaboration review with one set of revisions and instances where the collaboration insisted that the initial drafters start again from scratch. The general ethos, which has remained constant over time, is that consensus within the collaboration should be reached before a paper is submitted to a journal with a paper's detractors subject to the constraint that "you can't be the only one, and if you are, you better not be it each time." There were no reports of individuals in the experiments under study asking to be removed from author lists out of distrust of a paper's results; indeed, one interviewee recalled that the collaboration averaged the results of differing, independently-produced analyses rather than either putting off publication or publishing separate papers. (There are reports of people taking their names off papers from other experiments.) In experiments that effectively contained experiments within experiments, collaborators have removed their names from author lists from a sense of not having contributed to the results; such actions may indicate a belief that the work was not worth the effort to produce it.
At least five of the collaborations examined have tried to recognize an individual's contributions to a particular analysis by placing him at the head of the author list. Discussions of who belonged in that position, to an even greater extent than who deserves to present a paper at a conference, generated "more heat than light," and one veteran of such discussions recommended that they be scheduled for just before lunch or dinner, when everyone is eager to adjourn. One collaboration that stuck to recognizing individuals with first place on an author list decided that the results of two independently-written doctoral theses should be included in one article; the ensuing debate over who should be listed first was "the most acrimonious" in a collaboration notable for a high degree of internal competition and fierce debates over data interpretation. Those collaborations that used an alphabetized author list did not have such headaches, and one spokesperson actually preferred alphabetized lists because they drove home the point that "there's more to doing an experiment than doing a particular analysis." Besides occasionally stressing first place on an author list, collaborations sometimes tried to boost the significance of the author list by holding down the list's length through the exclusion of engineers or through rules that set how long a physicist could remain an author after he left the collaboration. (Such rules also protected physicists who left an experiment before significant data came in from losing credit for their efforts to design and build the experiment.) However, the overwhelming impression given by the interviews is that reputations in high energy physics have been built through word-of-mouth, letter of recommendation, and participation in conferences.
For two-thirds of those collaborations whose members expressed an opinion, Physical Review Letters was and remains the journal of choice. But a minority preferred or has come to prefer Physics Letters, because it turns around manuscripts more quickly and is more flexible on issues of article length.
ORGANIZATIONAL STRATEGIES AND COMMUNICATION
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Basic institutional and intellectual conditions of high-energy physics experiments required that all collaborations combine three organizational strategies, each with a characteristic pattern of communication. First, because detectors must be assembled and data taken at a laboratory, the laboratory had to be treated as an organizational headquarters to which the outlying institutions passed and received information. Second, because no single institution had the resources to mount an experiment on its own, and because reproducibility of results was an essential confidence-builder when puzzling or controversial findings were claimed, labor had to be divided and duplicated with collaborators working independently and reporting to the collaboration as a whole their progress, methods, and results. Third, because any individual's research could make use of equipment he had not built and software he had not written, collaborators had to contribute to an information pool that enabled each to take full advantage of what others had developed.
Individually, collaborations faced a host of technical, institutional, historical, and geographic factors that made for noteworthy variation in the difficulties they found most problematic. Each collaboration idiosyncratically blended complementary organizational strategies and compromised among conflicting strategies in order to have the best chance of handling its toughest difficulties. However, no collaboration could (happily) allow its toughest difficulties to drive the shaping of strategy to the exclusion of accommodating the interests of those with lesser difficulties. Technical factors were an obvious source of compelling problems for collaborations, but the other factors also significantly influenced the shaping of strategy—sometimes in ways that ran counter to technical factors.
Viewed over time, our sample brings out one major trend and two major continuities. The creation of intra-collaboration information was increasingly formal (e.g., collaboration-wide mailings and memoranda) and increasingly electronic in the larger, more recent experiments. Collaborations continued to divide labor, and the collaboration meeting remained the forum for discussions that led to decisions concerning the tactics and results of experiments. Even interviewees who found collaboration meetings unpleasant did not suggest alternatives to their use to debate and decide the physics issues in an experiment.A. Technical Factors
By contrast, when the detector was unimposing and the greatest technical challenge to the experiment lay in the development of target or beamline, there was usually much inter-institutional communication between the accelerator staff and external proponents of the experiment. In one such experiment, regularly scheduled telexes between the accelerator laboratory's research group and the target builders kept both institutions technically coordinated. In another, collaboration meetings were needed only sporadically because of the volume of telephoning among the participating physicists.
Finally, when detector components individually presented challenges, but problems with their integration seemed manageable through on-the-spot adjustments, a division of labor was instituted. In these experiments, regular meetings were the rule and frequent memorandum writing was encouraged so that all collaborators became sufficiently well versed in the components they were not building to understand the limitations in the data they produced.
Regardless of how communications were organized during construction, data analysis was usually handled through a headquarters framework. In many experiments, the collaboration possessed little discretion; one group (most often an accelerator laboratory research group) had easier access to the computer facilities needed to handle the quantity of collected data, and that group's institution became the headquarters for data analysis. Even when a collaboration included more than one institution with adequate computer facilities, one institution still often became data-analysis headquarters in order to insure most easily that all data were being analyzed with the most up-to-date programs. In the case of bubble chamber and emulsion experiments, where the data had to be initially measured by eye rather than machine and were thus too voluminous for any single institution, the labor was divided. Post-run collaboration meetings were used to check that the several measuring institutions were producing consistent results.
B. Geographic Factors
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When a collaboration was widely dispersed, the physicists tried either to reduce communication needs by dividing the labor or to communicate more inter-institutionally in order to allow all collaborators to participate from their home institutions. Even collaborations building concentrically-nested detectors for collider experiments often divided labor so that distant groups built the muon detectors, the outer-most portion of the detector, in their own shops. A fortiori, widely dispersed collaborations building loosely fitting detectors relied heavily on inter-institutional communiqués or a division of labor. All international collaborations in which the non-American group(s) were involved from the beginning treated the non-American groups as discrete units. (The case is different for American collaborations that added non-American groups, in order to boost manpower, after the proposal was accepted and an organization for building the detector worked out.) By contrast, in geographically concentrated collaborations, divisions of labor gave way to the other communication strategies. In one experiment performed by university groups that all had easy access to the accelerator laboratory, face-to-face encounters at the accelerator were an important form of communication and one of the participants remembered feeling as though "we were working together as if we were all in the same institution."
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When an experiment's organizers were university faculty, their needs to fulfill commitments to their employers, or to boost their standing with their employers (as in junior faculty approaching tenure reviews) augured for an organizational framework that let collaborators work from their home institutions. The laboratory did not become a powerful headquarters even when the organizers succeeded in recruiting a research group from the accelerator laboratory—a common tactic because accelerator-based research groups could pave the way to acquiring such resources as time on the accelerator laboratory's computers. But when accelerator-based researchers organized an experiment, they usually made the laboratory the headquarters and university collaborators had to accommodate.
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When collaborators had not worked together previously or had not in some other fashion built up confidence in each other's virtues, both technical and social, there was a strong tendency to divide and duplicate the labor and use meetings to compare results. When labor was divided, blame could be squarely assigned for a component that did not perform to expected standards, and credit assigned for components that did; when labor was duplicated, cross-checking of claims was possible within the collaboration before any results went public. In the most extreme case, one collaboration, consisting of two sets of physicists who had not previously worked together, set up two completely independent data-analysis chains and spent collaboration meetings in acrimonious, though intellectually honorable, arguments over the results they had each achieved. Intra-collaboration competition was thus substituted for the interpersonal trust that physicists needed in collaborations that communicated via a headquarters group or inter-institutionally.
How collaborations handled conflicting criteria or blended complementary options appears idiosyncratic to the individuals involved. Like everyone else, physicists vary in their willingness to travel, their powers of verbal and written expression, and their need for solitude or social stimulation to work effectively. However, it seems to be the case that happy collaborations cultivated a secondary communication pattern even when one form dominated. For example, collaborations with a headquarters still delegated important work to distant institutions, to keep the distant collaborators' interest as high as desirable. Or collaborations that communicated across institutional lines to coordinate component designs still used the accelerator laboratory as a construction headquarters.
Viewed over time, our sample does not exhibit any clear trend in organizational strategy, though the use of collaboration mailings and memoranda were more common in the more recent, larger experiments. But one continuity does stand out. The collaboration meeting remained the forum for discussions that led to decisions concerning the tactics and results of experiments. Some physicists found meetings unpleasant—occasionally an interviewee complained about meetings providing free rein to a long-winded colleague, the drain and expense of travel was a common lament, and personal relations were strained when collaborators who worked independently discovered at a meeting that they were in conflict. Even so, there was a dearth of suggestions for alternatives to the use of collaboration meetings to debate and decide the physics issues in an experiment. In only one collaboration did the physicists handle more business in meetings of group leaders than in meetings of the whole collaboration, and that collaboration was the only one where there were acute worries over whether the experiment would generate enough physics to support the needs of its members for differentiated topics.
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The ideal experience for a graduate student in high-energy physics is to become involved with an experiment as it is being planned, write a thesis that analyzes data that the experiment produced, and emerge familiar with all phases of a high-energy-physics experiment. Interviewees recalled pre-1980 experiments as reasonably conducive to that ideal; rather than finding themselves little fish in a big pond, the students benefitted from being involved in a broad, yet intellectually manageable, range of subjects and techniques. No interviewee for a more recent experiment has said outright that the experiment proved a bad vehicle for graduate education. But many worry that their next experiment will be the one whose length and complexity force students to spend too much time on too few subjects, and some have begun wondering how such changes in experiments will affect the personal qualities students need to succeed in this field.
Long, complex experiments pose two types of dangers for graduate education. The first is that the time from planning to data runs will exceed the norms for duration of a Ph.D. program, so that students will no longer be able both to construct apparatus and to analyze data from an experiment. In one of the experiments being studied, some students had to wait for data to analyze because the novel detector took longer to build and debug than expected; and in another experiment that assumed technical risks, a university collaborator directed graduate students toward other projects that seemed more certain of generating material for dissertations. Several faculty forecast that universities will have to award degrees for theses that deal solely with instrumentation. (It is apparently unproblematic to justify theses that deal solely with data analysis.) Such students would either have to round out their educations as post-docs or build careers as hardware specialists. Others recommended that students earn degrees by analyzing data from an experiment that was already running while building apparatus for an experiment that will run after they get their degrees, though it is easier to analyze data from a detector one knows from the inside and to lavish craftsmanship on a component that will collect data the builder plans to analyze.
The second danger to graduate students from long, complex experiment is that the experiment will take data over several runs, and the student who has become expert on some part(s) of the detector will become too absorbed in making the experiment run smoothly. One interviewee reported that one of his students, in a recent experiment not included in this study, became so adept at managing runs that he became shift supervisor and "spent so much time making the apparatus work and making programs work that he didn't spend as much time studying the physics." Another preferred to preempt this possibility by having students return to campus once they have enough data from which to write a thesis. Such an arrangement is of course possible only when a collaboration manages its data and software so that analyses can be done on campus, and the arrangement carries potentially profound, difficult-to-predict implications for the student's development: the on-campus thesis writer has the opportunity to audit courses and attend colloquia that may broaden his education, while the laboratory-based writer can constantly talk shop and make contacts with high-energy experimentalists on his own and other experiments.
To be a success in high energy physics, in the opinion of some interviewees, now requires that students possess more than conventional scientific talent. One physicist, contemplating the uncertainties in mounting experiments, thinks students must make "political judgements" about which experiments will get beamtime and data and that the politically savvy student will have the advantage. Another, contemplating the ease with which a student can cultivate a technical expertise that will let him float from experiment to experiment, worried that the field is attracting students more interested in the technology than the physics of experiments. The students with ambitions to become scientific leaders, he feared, will have to be "little sharks" in order to gain the resources to have a visible impact on an experiment.
STYLES OF THE NATIONAL LABORATORIES
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The comments of interviewees about the national laboratories clustered around four topics: the laboratories' technical capabilities and the responsiveness of their technical staffs, the character of interactions with the laboratory's administration, the quality of non-work time spent at the laboratories, and the overall "user friendliness" of the laboratories. Nearly every laboratory user had complaints about the laboratory at which his experiment was run. Laboratory staff members, not surprisingly, were more tolerant or defensive about their laboratory's character.
The ability of experimenters to work harmoniously with the accelerator laboratory's staff was generally important for happy experiments and particularly important when some novelty or potential in a laboratory's beam made that laboratory the preferred site for the experiment. Virtually all users concurred that relations with a laboratory's staff were facilitated by having physicists from the laboratory's research division in the collaboration, and university-based initiators of experiments have consciously searched for laboratory collaborators. There are, in this sample, examples of experiments performed at Brookhaven and SLAC without laboratory collaborators; Brookhaven users in this situation tend to complain about the quality of services they received while SLAC users tend to complain about the quantity of services they received. Most Fermilab experimenters—especially those who had done experiments at CERN, the apparent leader in providing quantity and quality of services to experimenters—felt they had to take care of more matters on their own.
Laboratory directors and Program Advisory Committees did not receive much criticism in these interviews. The conditions that they insisted experimenters satisfy were rarely the object of controversy (though everyone was talking about proposals that were accepted and experiments that ran rather than ones that were not or did not). There was only one instance reported of a laboratory director telling an experimenter how to build an experiment; and the interviewee, a long-standing member of a laboratory's research division, ignored the director and has never, before or since, received such advice. Occasionally, experimenters complained that laboratory administrators adhered too strictly to their policies. For example, one experimenter felt that his collaboration was forced to announce a provocative result in order to lay a public foundation for requesting more beamtime when he would have rather struck a discrete deal for more time and double-checked the result before making any announcement. Most commonly, experimenters expressed regrets about the effect on extant facilities and running experiments of a laboratory administration's decision to dedicate resources to upgrading an accelerator or building an accelerator.
The isolation of Fermilab and Brookhaven from cosmopolitan pleasures wore especially on unmarried physicists who craved a social life, but SLAC was frequently criticized for not providing enough help with visitors' housing, dining, and transportation needs. Cornell, whose collider was drawing increasing interest because it covered a more interesting energy range than SLAC's PEP, could become the object of similar complaints. CERN appears to have been the most pleasant laboratory for a visitor to live near for extended periods.
SLAC, when compared to other laboratories, was invariably considered the least friendly to outside users, and SLAC faculty acknowledged that the strength of SLAC's in-house groups usually behooved outsiders to hook up with an internal group. Three contrasting explanations were offered for the strength of SLAC's in-house groups: one non-SLAC physicist believed that lack of widespread interest in SLAC at the time of its origin forced SLAC to cultivate strong in-house groups; a SLAC faculty suggested that the intrinsically high backgrounds in electron experiments, and the consequent complexity of the detectors need to collect results, required that in-house groups be cultivated for detector development; another SLAC faculty suggested that the proximity and relationship between SLAC and Stanford somehow led to strong in-house groups. Whatever the explanation, SLAC faculty justified their power by arguing that experiments are better run by people who can dedicate themselves full-time to the experiment and that complaining users are fundamentally distressed at their inability to be full-time experiment directors at an off-campus laboratory while discharging their on-campus responsibilities.
With the exception of the appendix, "A Comparison of the Situation at CERN With That in Similar U.S. Facilities," the essay as printed here was first issued by the History of CERN Project as CERN Report CHS-32, June 1991. A revised version will be published in Elisabeth Crawford et al. (eds.), Denationalizing Science, Sociology of the Sciences Yearbook. Copyright ©1992 Kluwer Academic Publishers.
What will never happen again is what happened to me once when I was a graduate student.... My thesis supervisor rang me up one day and said, "Hey, I have just had a great idea and we could do it by slightly modifying our experiment. We just have to sneak in a few extra hours beamtime." And we did an experiment. And the next week we repeated it.... I have never done an experiment like that in high-energy physics, where you just on the spur of the moment did something, a little bit of bricolage, a little bit of playing around, got a significant measurement, went away, analyzed it for two days, published it. We're a long way from that.-- UA1 physicist who did his Ph.D. on a small cyclotron in the late 1960s.
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One of the most striking features in the postwar development of high-energy physics has been the growth of large teams of physicists on the experimental workfloor. Before the war, experimental research, even with big accelerators like those at Berkeley, was generally done with relatively simple equipment, and remained an essentially individual affair. However, as detectors became more complex, costly, and time-consuming to build, increasing numbers of physicists, often from more than one institution, began to do experimental work together with the device. This phenomenon emerged in the late 1950s, and the size of teams has tended to expand ever since. A typical bubble chamber collaboration at CERN (European Center for Nuclear Research) in the mid-60s comprised perhaps fifteen physicists plus technical support, while an electronics or "logic" experiment might have had about ten physicists grouped together around the equipment. A decade later about 50 physicists from seven institutions routinely signed the papers reporting results obtained with CERN's largest bubble chamber (Gargamelle), while the first set of electronic experiments at the Super Proton Synchrotron (SPS) typically comprised some 20 to 40 physicists from four to six different laboratories. By the mid-80s even these team sizes were dwarfed by the collaborations planning to do experiments at LEP, CERN's Large Electron-Positron Collider. In 1985 the Delphi collaboration, for example, comprised over 350 physicists from 37 institutes in 17 countries. Needless to say, the major collaborations on the Superconducting Super Collider (SSC), appropriately located in Texas, and scheduled for completion in the late 1990s, are expected to be at least twice this size. Very roughly, then, the number of physicists in a single collaboration taking data with the largest detectors used in high-energy physics has been doubling every five or six years since the mid-1960s, and might reach 1000 by the year 2000.
It is striking how little has been written about this phenomenon, considering its sociological and historical interest. It was something of an issue in the early 1960s, when large teams first appeared on the horizon, and a number of interesting studies of the change and its implications were made. Very little was done for the next two decades, until Galison and, from a somewhat different angle, Pestre again drew attention to the changes in the organization of the experimental workplace and to some of the institutional problems surrounding collaborations in high-energy physics. At the same time there has been a growing interest in the theme among the U.S. physics community itself, doubtless in anticipation of the arrival of the SSC. In 1985 the NSF sponsored a symposium to explore the costs and benefits "of international scientific cooperation between the U.S. and other countries in big science." In 1988 a HEPAP Subpanel reported on "future modes of experimental research in high-energy physics." And the Center for History of Physics of the American Institute of Physics has just completed a major study, based on interviews, of multi-institutional collaborations in high-energy physics in the U.S.A. and in Europe.
While it is difficult to generalize from this literature, one image that emerges, and which is tenacious partly because it reinforces what many "spontaneously" believe, is of the steady industrialization of the experimental workplace in high-energy physics. Multilayered managerial structures have been imposed, hierarchical relationships have replaced free exchanges between equals, bureaucracy is rampant, and decision-making processes have become increasingly formalized. From the point of view of the individual physicist, work has become boring and repetitive, with little scope for creativity and autonomy. In short, "basic" research in experimental high-energy physics has now adopted the work patterns of applied research. The free-wheeling, creative atmosphere of the university laboratory has been supplanted by the constricting procedures and regimentation of the large corporation.
This picture is undoubtedly symptomatic of important changes in the nature of experimental work. Yet it must be handled with care. For one thing, it is partly the result of studies which have focussed on the work done in Luis Alvarez's group in Berkeley in the early 1960s. Here an assembly-line approach was indeed adopted to facilitate the processing of hundreds of thousands of photographs taken on the 1.8m hydrogen bubble chamber. As such the studies are, to some extent, specific to a certain type of detector—work with electronic detectors left far more scope for individual initiative, specific to a certain laboratory—there is no evidence that European bubble-chamber physicists went to the extremes adopted at the LBL in the early 1960s, if only because they lacked the technology to do so, and specific to a certain period of time in the late 1960s new technologies were invented which considerably reduced the drudgery in the analysis of bubble-chamber film. Generalizing the factory model to the field as a whole is thus particularly hazardous in this case.
A second reason for caution is that the model is laden with nostalgia, with a yearning for a romanticized past, for a golden age. It emerges particularly forcibly in the sayings and writings of people like Don Glaser, who won the Nobel Prize for inventing the bubble chamber, of Luis Alvarez, who won the Prize for developing and exploiting the technique, and of Bob Wilson, the founder and first director of the Fermi National Accelerator Laboratory just outside Chicago. Glaser left the field rather than work in what he called (in an interview made in 1983) "the factory environment of big machines." Alvarez, speaking in 1967, "began to despair at an industrialized nuclear physics that had become, in his words, `just a little dull.'" Wilson has described, with masterful ambiguity, his "fight against team research." It is clear, however, that all three were highly individualistic and creative people. Their remarks and attitudes, while certainly reflecting and sustaining a certain ethos in the physics community, are not necessarily a reliable guide to the actual state of affairs. Nor should they be taken as representing what the average competent physicist doing "normal" science feels about his or her work situation.
My main aim in this paper is to lay the foundations for a better understanding of multi-institutional collaborations in high-energy physics, better, that is, than that provided by the "factory model." To this end I shall present the findings deriving from archival research and interviews with physicists who worked in such collaborations at CERN between 1975 and about 1985. These are analyzed with reference to a number of "classical" sociological questions—how are such collaborations formed? How are they organized? How is credit attributed to individual researchers? Is there scope for individual autonomy and creativity within them? My central finding is that the experimental workplace in high-energy physics is far less structured, the atmosphere far more informal, and personal satisfaction far more widespread, than the factory model would lead one to believe.
The results presented in this report are based on an in-depth study of the two most important electronic experiments done at CERN in the late 1970s and early 1980s. The first, code-named UA1, a "4pi solid angle detector for the SPS used as a proton-antiproton collider at the centre-of-mass energy of 540 GeV," was approved on 29 June 1979. Its spokesman was Nobel Prizewinner Carlo Rubbia, and when it began taking data in 1981 the collaboration comprised some 130 scientists from eleven institutions, including one in the U.S.A. The other experiment was to serve as a "backup" to UA1. Code-named UA2, "Study of antiproton-proton interactions at 540 GeV c.m. energy," its spokesman was Pierre Darriulat. UA2 was approved on 14 December 1978, and began taking data at around the same time as UA1. At this stage it comprised some 50 scientists from six European institutions. About 25 scientists from a variety of institutions in the two collaborations have been interviewed within the framework of this project. Their remarks have been supplemented by the private collections of papers of two physicists. These papers were also collected during the course of the project and a detailed running list of the contents of the more extensive and important set of them has been drawn up.
HOW ARE COLLABORATIONS FORMED?
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Morrison has described briefly how and why collaborations are formed and grow, and we have little to add to what he says at a general level. The interest lies in illustrating, and in trying to refine and to extend some of his ideas with reference to a specific case. This we shall do here by spelling out in some detail the factors shaping the birth and growth of one particularly important collaboration, the UA1 (Underground Area 1) collaboration whose initial spokesman was Carlo Rubbia.
Early in 1977 Carlo Rubbia organized a proton-antiproton study week at CERN in anticipation of either CERN or Fermilab going ahead with a major p-pbar (proton-antiproton) project. About 35 people from CERN, some European laboratories, and from the U.S.A. (one or two) participated. At the end of the week, which lasted from 28 March to 2 April 1977, a paper was prepared "for the attention of the CERN Management" which summarized the conclusions reached on the characteristics of the detectors required at a p-pbar facility. The meeting also set up a structure "to guarantee a continuing activity" of this work.
During the next six months about 30 so-called p-pbar notes were written. These were technical memoranda most of which discussed the features of the detector needed to do colliding beam physics at very high energies. They were written by scientists based at several different institutes (Annecy LAPP, CERN, Rome University, Saclay, University of California at Riverside...) and circulated among all those interested.
On 8 November this core set of people (about 25) met formally and held a "general discussion on how to get organized from now on." Six institutions were represented. They set themselves an extremely tight schedule. 1 December was the deadline for the final sketch of the detector. The final drawing of the detector with optimal parameters was to be ready by Christmas. By mid-January the proposal to be submitted to the SPSC (the experiments committee responsible for making recommendations about what proposals should be accepted) was to be typed. And on 31 January 1978, we are told, there was to be "Propaganda made—Proposal submitted."
The "collaboration" met formally (in the sense that minutes were written and circulated among those present) at least once a week from then on until mid-January. The numbers present stayed constant at about 25. However there were important changes in the institutions represented. Aachen, Annecy LAPP, CERN, Collège de France, Saclay and University of California, Riverside were the initial core. There was a representative from Harvard University at one or two meetings, and from the Inter-University Institute in Brussels at another: neither institution remained formally part of the group. More significantly, a number of British groups joined during this time. At the meeting on 15 November it was reported that there was an "Interest from Rutherford Lab. (where C. R. [Carlo Rubbia] and B. S. [Bernard Sadoulet] are going to make some propaganda on Monday)...." The trip was made, and the following week, on 22 November, Rubbia reported that "One result of the seminar held at RHEL [was] the interest of Birmingham for our project" indeed two Birmingham representatives attended this meeting. By mid-December Rubbia had been informed in writing of Rutherford's interest in the collaboration: they would like to join "our group together with 4/5 other physicists and ad hoc technical support." (The physicists were doubtless the representatives from the third interested UK group, Queen Mary College.) At this point (13 December 1977) Rubbia felt that the collaboration was approaching its optimal size, and that "from now on it [would] be harder to join our group." In particular it was agreed "that any other large institution who would like to join [would] give serious problems."
The proposal for experiment P92 (subsequently called UA1) was submitted to the SPSC on deadline—30 January 1978. It ran to over 150 pages including references, and was signed by 52 scientists. 48 of these were from the nine main institutes we have mentioned—Aachen (5 representatives), Annecy LAPP (6), University of Birmingham (10), CERN (8), Collège de France (4), Queen Mary College (4), University of California, Riverside (3), Rutherford Laboratory (4), and Saclay (4). The other four signatories of the proposal were visitors from Wisconsin, Harvard, and Rome.
At the collaboration meeting on 7 February 1978 Rubbia reported that two proposals and two letters of intent to do colliding beam physics had been submitted to the SPSC and that each group would have to defend its proposal at open presentations as early as 21 February. He felt that his collaboration would need 60-90 minutes to describe first the experimental set up and then the physics program. Regarding the latter, it was felt that although "one speaker only for the physics program would be better for the continuity of the talk," on the other hand "four speakers from different labs [would] show that we are already a working collaboration." It was suggested that Sadoulet describe the detector and that the physics be split into three topics to be dealt with by Dowell (Birmingham), Linglin or Della Negra (Annecy) and Rubbia. Rubbia would speak on the W and the Z particles, the major discoveries that were anticipated by the collaboration.
Early in April Rubbia reported on the progress with the SPSC. Collaboration meetings were now being held every two to three weeks, and were being regularly attended by about 40 people from the nine collaborating institutions. Rubbia remarked that two out of five proposals (those that became UA1 and UA2) had been considered and refereed, and that "Nothing appeared in the minutes but ours went through without any major objection."
At the end of May 1978 the so-called Coordination Committee for experiment P92 met for the first time. A member of the CERN Directorate who was responsible for the experiments to be done at the p-pbar collider (P. Falk-Vairant) was in the chair. He explained that this committee would meet roughly bimonthly, and that its task would be to "follow and supervise closely the progress of the proposed experiment." Each collaborating institution was to be represented on it. (This committee subsequently came to be called the UA1 Executive Committee). One of its first tasks was to draft an agreement setting out the responsibility of each institute in the collaboration. It would include a time table, cost estimates, a list of physicists with at least a three-year commitment to the proposed experiment, detailed information on manpower needs, and so on.
About this time too the collaboration was informed that two further institutes, Rome University and the Institute for High-Energy Physics in Vienna would like to join the collaboration. Both were ultimately accepted, though not without some difficulty, a point to which we shall return below. Indeed when the CERN Research Board accepted the UA1 proposal on 29 June 1978 the number of participating institutes was still just nine and the document distributing responsibilities between the laboratories had not yet been drawn up. This was finally settled by 31 October 1978. A mere three years later the huge detector, which weighed around 2000 tons and which included some highly sophisticated, state-of-the-art technology, began taking data for the first time.
The most important point we want to stress about this 18-month process of formation and growth is that it occurred because of the combined effect of a number of very different considerations. Certainly the scientific interest of the experiment and the technical design of the detector were the cornerstones underpinning the formation and consolidation of this collaboration, and its successful implantation at CERN. However, on their own these cannot account for the process we have just described: a number of other social, institutional and political considerations have to be taken into account if we want to understand how and why the UA1 collaboration "gelled."
Firstly, there was the mutual trust and respect between the scientists themselves, the conviction that each group in the collaboration was capable of pulling its weight and delivering its part of the detector on time and in good working order. It was precisely because this trust was lacking, because it was feared that it was not a "strong group," that the collaboration initially reacted so negatively when it learnt that a team from Vienna was interested in joining. Conversely, the addition of the Rome group was unproblematic. One of their representatives (Salvini) had been actively working with the collaboration as a CERN visitor since early 1977 and his name was included on the original proposal.
Another obviously related consideration affecting the entry of groups into the collaboration was the knowledge that they had the infrastructural support behind them at their home institutions needed to take on a major construction project. This was one main reason why Rubbia visited the Rutherford Laboratory even though he had not worked with some of the British groups before. "We are fairly weak, hardware wise," he told the embryonic collaboration at CERN, "and we are eager to accept hardware people like RHEL."
Political considerations, though never explicit, were also not far beneath the surface. The p-pbar project at the CERN SPS only received the Council's backing in June 1978. While its acceptance was always something of a formality (it was rather cheap), the fact remains that some physicists were totally against it on the grounds that it might jeopardize LEP. Others, notably in Britain, were not keen on it for fear that it would seriously impede fixed-target physics at the SPS. One way of swinging the all-important delegations from major Member States behind the project was to include physicists from institutes in their countries in a collaboration which promised, after all, to do the most exciting physics of the 1980s. Thus it is perhaps not a coincidence that Rubbia and Sadoulet went to Rutherford "to make some propaganda" for P92 only six weeks after two members of the CERN Directorate had discussed CERN's plans with UK users at the RHEL and had found a "lack of popularity of p-pbar, which we must try to correct," as they put it.
The importance attached by the CERN directorate to having outside laboratories in its Member States participate in the experimental program doubtless also played a role in shaping the composition of UA1. For example in March 1978 Walter Thirring, an extremely influential Austrian theoretical physicist, wrote to CERN expressing both enthusiasm for the p-pbar project and concern that "as the size and complexities of large experiments go up it will become increasingly difficult for smaller laboratories to compete with the large laboratories of the bigger member states of CERN." The grounds for Thirring's concern are clear. The early core of UA1, as we have seen, was made of groups from CERN itself, along with those in Britain and France (and a small contingent from Riverside), countries which had large national facilities of their own. We have just seen the importance attached by the spokesman to having the infrastructural resources at a site like Rutherford deployed for UA1. University laboratories in small countries simply could not call on such resources. To counteract the corresponding tendency to concentration the CERN management strongly favored, not just a wide representation of institutes in this experiment (and in UA2), but the representation of institutes in the smaller Member States in particular. And indeed, it was shortly after Thirring's contacts with senior management that the group from Vienna joined the collaboration.
This brings us to the contribution of the senior CERN management. It was crucial inside the organization. A man like Research Director-General Leon Van Hove was crucial in that he backed the somewhat risky p-pbar project from the start (despite the doubts of many physicists and the lukewarm attitude of his partner and Executive Director-General John Adams), and persuaded and cajoled all the top policy-making committees at CERN to finance the scheme. He also ensured that experiment UA1 had all the necessary infrastructural support inside the laboratory, where in the words of one of the participants it was given "red carpet treatment." The management also played an important role in the Member States. A man like Paul Falk-Vairant, member of the Directorate responsible for p-pbar experiments, undoubtedly encouraged groups in his native France to back the proton-proton-antiproton project. By all accounts he also strongly supported Pierre Darriulat's experiment proposal P93 (later UA2), which had a strong French core, and which was in competition with a proposal by Nobel Laureate Sam Ting (and which apparently had Van Hove's backing). In short the CERN Directorate, largely united over generalities, sometimes divided over particularities, made a fundamental contribution to the growth and consolidation of UA1 and of UA2.
There is one other actor who should be mentioned to round off the picture. This is the SPSC, the committee comprised of senior physicists from CERN and the Member States, whose task it is to consider experiments proposed at the SPS and to make its recommendations to the CERN Directorate. It is they who supported UA1 without hesitation. It is they who made the decisive choice between Darriulat's proposal and Ting's, after consultation with external referees and a dramatic "shoot-out" between representatives of the two groups at an open meeting in December 1978.
It is they who decide on the scientific desirability and technical feasibility of an experiment, who strive to draw a clear line between "objective content" and "non-scientific context," who both confirm and legitimate a choice from a "strictly scientific point of view."
The formation and consolidation of a collaboration is thus a complex process which brings together a number of very different protagonists who have different institutional locations and roles, and who make different kinds of contributions to its ultimate success at different stages in its evolution. At the heart of the process there is the core of scientists who push the project. It is they who have to persuade other members of the community to join them, who have to ensure that influential sections of the management back them, who have to steer their proposal through the experiments committee. In short it is they who have to sell their idea at CERN and in the Member States. We are indeed a long way away from the situation described in the quotation at the start of this paper.
HOW ARE COLLABORATIONS ORGANIZED INTERNALLY?
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Work in a large collaboration has to be organized. The size of the detector (it can weigh thousands of tons), the nature of its construction (particularly if it is modular, with different units being built by different groups), the time constraints (the need to meet deadlines and to compete with rivals), the mass and variety of data to be analyzed (there are many physics topics to be studied), the sheer number of people involved (tens or hundreds working together)—all of these demand that some sort of organizational structure is set up inside a collaboration. And when one contrasts this situation with the picture of the individual scientist following freely where Nature leads, it is but a short step to identifying work inside a large collaboration with work inside a "factory" or large corporation. In this section we want to explore the plausibility of this analogy. We shall see that, while superficially there are some parallels (planning and coordination of project, division of tasks, hierarchy of responsibilities...), any simple identification of an experimental collaboration with a business corporation fails. And it fails because the qualified physicists and engineers who work in large teams tend to regard and to treat each other as professional equals and peers, people who are working alongside them to achieve a common objective.
There is one important distinction to bear in mind before we get under way. The factory model, in so far as it has any plausibility at all, can only apply to the period during which the detector was being constructed. In the case of UA1 and UA2 this lasted for three to four years (from design to commissioning), which was remarkably fast for devices of this type. During this phase the work was carefully organized and planned as we shall see. Once the detector started taking data, however, and the analysis of physics results began, a far looser organizational structure was put in place. Physics analysis, the HEPAP tells us, is "intrinsically next to impossible to 'manage.'" This is not to say that physicists are free to explore whatever topics they like, but simply to indicate that the constraints on what they do are not those identified in the "factory" model—and to insist that whatever merits that model may have, its value is restricted to the construction phase of the detector.
The detectors for UA1 and UA2 were not built exclusively at CERN. Both consisted primarily of a number of interlocking modules with a 4pi geometry (rather like the layers of a cylindrical onion) along with triggers which selected interesting events and a data acquisition system. These various components were shared between the collaborating institutes which generally built them at home, bringing their various subdetectors or components to the host laboratory for final testing and assembly. The division of labor between the various centers was defined in a formal "Agreement on the Sharing of Responsibilities..." and is shown in Figure 1, along with the deadlines imposed on each participating institution.
How were these responsibilities distributed? To begin with it was clear that the central detector of UA1, the heaviest and most technically advanced part of the device, should be built at CERN. This component, as envisaged in the UA1 Agreement, consisted of "a volume filled with about 11000 drift chamber wires in order to record an image of the many tracks.
|Table 1. The commitments made by the collaborating institutes in UA1 in terms of various categories of personnel, of money, and of computing time. The first and last are from the draft agreement for sharing responsibilities inside UA1 dated 31 October 1978. The financial responsibilities are provisional estimates in millions of Swiss Francs made in December 1978 and exclude salaries.|
1. The computing time was for data analysis and it was assumed that the collaboration would need 1000 hours a year on a CDC 7600 or equivalent.
2. Rutherford Appleton Laboratory, which had overall administrative responsibility for the British participation in UA1.
3. The combined contribution of Annecy LAPP and the Collège de France was 2.5 MSF.
produced in the collisions. The electronics for the detector capable of continuous recording between [proton-antiproton] bunch crossings is entirely new," the document went on, "and must be developed," adding that CERN "accepts entire responsibility for the device including the electronics and readout." Apart from the sheer logistic difficulty of transporting such a detector from, say, Paris to Geneva, the fact that CERN had the money, the personnel, and a large number of highly-qualified people on the spot who could dedicate themselves full-time for three or four years to this one task meant that the host laboratory necessarily built this module. As for the remaining components, they were distributed on the basis of the interests, past experience, and resources of each participating institute, though of course there was also a certain amount of horse-trading between the various collaborating laboratories. The UK groups in UA1, for example, would have liked to build the rather challenging electromagnetic calorimeter. Instead this job went to Saclay, while the British groups were given the less demanding hadron calorimeter. At the same time the latter secured the trigger processors for both calorimeters, an item which played a crucial role in the data taking.
In agreeing to build a part of a detector an institution was also committing personnel, money and computing time to the collaboration. Table 1 shows the extent of these commitments as envisaged at the end of 1978. It confirms the heavy involvement at every level by the major institutions in two big Member States, Britain and France. Indeed, along with CERN, the three institutes in each of these countries were together responsible for about two-thirds of the physicists, programmers, and engineers involved in the construction of the detector, were expected to bear over 85% of its cost in terms of material, and anticipated providing 90% of the required computing time for data analysis.
The coordination of the building, assembly and installation of the UA1 detector was entrusted to a Technical Committee chaired by Hans Hoffmann. This committee met every week throughout the construction period. About 25 people regularly attended these meetings. In addition many other formal meetings (in the sense of meetings for which minutes were kept and circulated within the collaboration) were held at CERN during this phase of UA1's life, each intended to deal with specific tasks. Thus we find Central Detector meetings, Muon Detector meetings. Calorimeter meetings, Trigger meetings, Gas System meetings, On/Off-line Software meetings, Database meetings, Graphics meetings etc. In addition there were regular meetings of the whole collaboration and of the Executive Committee, these being the only two formally constituted bodies which met regularly throughout the entire life of the collaboration, from construction through data taking and analysis.
The most striking feature which emerges from an analysis of the attendance at these committee meetings is the key role played by a small core of people. We find that perhaps 20 scientists are responsible for writing the minutes of the various meetings and that they are mostly senior people: about 15 of them "represent" their institutes on the Executive Committee. We find that although as many as 85 different people may attend meetings of the Technical Committee during a year, there is again a small number, maybe five or six, who attend regularly, week after week, people like Sergio Cittolin who was responsible for the data acquisition system, Bernard Sadoulet who was responsible for the central detector, and Guy Maurin who was responsible for the overall administration of the group. Finally we find that the spokesman and head of the collaboration, Carlo Rubbia, while taking the chair at collaboration meetings, and not missing an Executive Committee meeting, was far less often present at lower level meetings. This was even the case with the all-important Technical Committee, where he apparently attended about 60% of the time in 1978, about 40% in 1979, and seldom if ever in 1980. The picture then seems to be clear, and coherent with the classic pattern of business organization. We have a pyramidal structure, with the spokesman at the apex, the "boss;" a layer of middle management, say 25 people in the centre who were responsible for the daily organization of the construction of the detector; and a broad base of scientists below that (remember that there were about 130 physicists and engineers in the UA1 collaboration in 1980/1), a mass of people who were more or less excluded from the loci of power and of decision-making.
There are two criticisms that can be levelled at this model. Firstly, it is wrong to assume that because there is a hierarchy of responsibility inside a large collaboration, then necessarily the bulk of the scientists are excluded from the decision-making processes. As a general rule this is simply not so. The main purpose of the meetings that are held is not to pass on instructions but to share information, to communicate and to consult, and to decide collectively. Correlatively, attendance at meetings is not an obligation imposed from above, but a response to a perceived need to be informed about things that directly concern one's work. In fact many meetings are arranged on an ad hoc basis to discuss a particular problem, and are dissolved after two are three sessions when the problem has been resolved. There is planning and there is coordination inside a collaboration, and there is a core of people who have more responsibility than others, and who have to ensure that certain things get done. But as a general rule there is not top-down management, there is shared decision-making.
The second weakness of an overly formal picture of how a collaboration is organized is that it misses the ongoing, informal relationships between the members. The scientists and engineers in a collaboration, from the senior physicists down to the junior graduate students, are in constant working contact with one another and with the technicians, rubbing shoulders together, discussing what has to be done and how best to do it, making myriads of mini-decisions throughout their long, often very long, working days. Those with special responsibilities are never far from the workplace, their offices arranged to ensure accessibility and to facilitate communication. Meetings punctuate this ongoing exchange of information. They are pauses intended to iron out specific problems or to discuss new ideas, after which everyone plunges back onto the "shop floor."
There is one last qualification to be made before we leave this point. We have suggested above that the picture of a collaboration as having a pyramidal structure is misleading, that the managerial structures are more fluid, hierarchical relationships are more blurred, bureaucracy is less important, than any unsophisticated industrial model—and the literature has not yet moved beyond that level of analysis—would lead one to believe. Indeed, one might add that when interviewing physicists in UA1 and UA2 many of them were puzzled by the notion of there being a middle management in the collaboration and felt that it was somehow inappropriate. At the same time it has to be said that, at least as far as UA1 was concerned, the picture painted above is somewhat idealistic. For here there was undoubtedly a boss, Carlo Rubbia, who by his genius, his determination, his charisma, and by his notorious inability to tolerate opposition, in fact imposed his will on the collaboration, to the extent that no important decision could be taken without his first giving the green light. At the same time it is instructive to note how many of those interviewed resented this, revolted against a structure in which there was Rubbia and the rest, as one of them said. In short, some collaborations might indeed be organized like large corporations with a top-down management structure but it goes against the grain of scientists who believe that authority and power should derive from experience and expertise, that compliance should be the result of consultation and persuasion not coercion, and that decisions should be made collectively not imposed from above. And who like to work together, and who would like to organize their work together, around these assumptions.
To conclude this section, one brief comment about the organization of work during the data-analysis phase. As we suggested, the general rule here is to let each physicist follow his or her specific interests. That granted, there is however one fundamental constraint: that only physicists based at CERN can hope to work on hot topics like the search for the W or the Z particles. There are many reasons for this. Firstly, there is a large number of people concentrated at CERN, people who are interacting continuously with the detector and with the data that it is producing, people who meet every evening to discuss the significance of new candidate events. No university department, say, can hope to reach the "critical mass" of scientists who have the time, the freedom from other responsibilities, and the different points of view which are needed to extract a significant signal from the background noise. Secondly, the results are generated at CERN and so can be analyzed immediately. To analyze the data in the UK, for example, copies of tapes have to be flown to London, transported to Rutherford, and loaded in the computers there, all of which introduces delays which are significant when one is racing to beat a rival. And finally there is the infrastructure of CERN, the computers above all, but also services like administrative support and press relations, all of which are there to exploited if an important result has to be produced and announced quickly. In brief the need to get results fast, and by sedimentation from an ongoing process of discussion, evaluation, and reevaluation of data by a totally dedicated group of scientists, inevitably means that "discovery" physics is, and must be, done at the host laboratory.
IS CREDIT ALLOCATED IN LARGE TEAMS?
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There are three ways whereby scientists doing basic research conventionally gain credit for what they do: by publishing in the refereed literature, by speaking at conferences, and by impressing their colleagues and peers by their diligence and professional competence. Traditionally the first of these, publications, have been the most important means of assessing output and ability. However, with the growth in the size of collaborations, and their current policies for drawing up author's lists, other more "subjective" criteria are coming to the fore, to the consternation of a physics community which finds itself trapped between past values and present realities.
Publication in the refereed literature is still the single most important goal of the researcher in basic science. The publication serves two main sociological purposes. Firstly, it is an indicator that the authors have, in the eyes of their peers, made a novel contribution to knowledge. As such, and particularly in an activity like basic science which is driven by competition, a publication serves to attribute priority to its authors for the results they have obtained. Secondly, publications are widely regarded as an "objective" criterion of achievement in the field. As such, publishing articles is central to the functioning of a community which aspires to giving rewards primarily on the basis of scientific merit. Having one's name on a paper is thus of considerable importance to physicists.
How are author's lists drawn up? First, the usual basic distinction is drawn between constructing the detector and doing physics with it. The publications deriving from the former, which deal with technical innovations, are submitted to journals like Nuclear Instruments and Methods. Their author lists are relatively short and include only people who have been directly involved in the work described in the paper. There is apparently no great difficulty in settling authors lists for this kind of publication, as most physicists see such work as essential but relatively unimportant as a means of gaining credit amongst their peers it is "considered by physicists to be a sort of second hand publication..." one of them said.
The situation is more delicate when it comes to publishing physics results. On the one hand, granted the work that they have done on it for many years, physicists want to have their names on papers deriving from "their" detector. On the other hand, given the variety of results achieved with some of the "multipurpose" facilities, they cannot possibly hope to be actively involved in all aspects of analysis. To satisfy these potentially conflicting considerations, collaborations tend to adopt a policy of generosity. They put the names of everyone involved in the collaboration for any length of time, who has made a significant contribution to its work, and who has a global understanding of the physics results reported, on every analysis paper. There are local variations within this scheme of course. Visitors or graduate students who were not involved in building the detector have to dedicate a minimum period typically a year of doing analysis along with the rest of the group before qualifying for author's lists. Some physicists who are highly specialized in one aspect of the work might only sign a subset of the papers. The very early papers might include the names of one or two people which will later disappear—the accelerator engineer Simon Van de Meer who shared the Nobel with Rubbia was given credit on the UA1 paper announcing the discovery of the W, and was then removed from the author's list. But the general rule remains unchanged. Any physicist who is seen to have made a significant contribution to any aspect of the collaboration's work signs every paper.
By being generous in drawing up author's lists collaborations reduce to a minimum the potential for conflict which arises when people feel their names have been unjustifiably left off a paper. In fact it appears that only about 5% of the names ultimately included are ever contested in a collaboration. The main source of difficulty concerns engineers and technicians. On the one hand many physicists recognize that some engineers and technicians have made important contributions to the development of the detector, and feel that they should duly be given credit for this on papers reporting results even if they are not really au fait with the physics. Against this it is felt that the proper place for engineers and technicians to publish is in journals like NIM which are dedicated to detector research-and-development, and that anyway a publication list is not as important professionally for them as it is for physicists—rewards are distributed differently in the different fields. As a result the consequences of putting engineers,' and particularly technicians,' names forward for authors lists can be so divisive that it takes a very determined group leader to push the idea through. As one interviewee explained, a publication bestows a very high status on a technician in his or her institute, and can lead to enormous friction, not only inside the home institute itself, but also with other institutes in the collaboration who are not putting forward technician's names.
Two last comments before we leave this point. Firstly, the ambiguity about including the names of engineers and technicians on physics papers is a consequence of the fundamental changes in experimental work that we are looking at in this paper. On the one hand it arises from the multidisciplinary character of the collaboration (see Table 1), from the fact that physicists, programmers, engineers and technicians work together over long periods of time around the same piece of equipment, all of them contributing in important ways to the final result. On the other hand, it is symptomatic of the changed role of the physicists themselves, of the blurring of the boundaries between the physicists and other professional categories. To be a physicist in a collaboration of this kind is to master a number of very different techniques, techniques shared by computer scientists, by electronics engineers, by high-level technicians, and so on. The main criterion for having one's name on a paper reporting physics results may be that one is a physicist. The difficulties that we have just described arise because the notion of who is a physicist is itself contestable.
The second point worth noting is the confusion in physicists' minds about the value of publications. On the one hand, they are extremely concerned to get the credit that comes from having one's name on a paper, and determined that justice be seen to be done in author's lists. This is because they cling to the traditional view of the value of papers and, as importantly perhaps, because external assessors—fundgivers, faculty boards—still regard publication lists as an "objective" measure of performance. At the same time there is a tendency for physicists to place less weight on the publication as a means of gaining reward. All those interviewed would agree that "publications count for very little" now, the credit one has being diluted by the fact that an individual is "merely" one of tens or hundreds. The policy of generosity may avert conflict. But it imposes anonymity ("I don't even read the authors lists" anymore, one interviewee said), and the obligation actively to seek rewards in other ways as well.
Conferences are the second main way for gaining credit in the physics community. They serve two important functions. Firstly, even though results are tentative and unrefereed, contributions to conferences serve to establish priority. They are particularly important in a field that is at once highly competitive and in which experimental data are thick with interpretation. On the one hand, physicists want to report their results quickly—indeed the week or two before an important conference are a time of feverish activity in a collaboration. On the other hand, physicists know that it can take a long time to converge on an agreed interpretation of their data, and for the community to accept them as reliable. Conferences are a way of resolving the dilemma, a way of presenting data fast without over-committing oneself to them.
The second important function of conferences is as a forum for gaining visibility in the outside community of peers for both the individual and the group. Conferences are loci for making, or breaking, credit and credibility. One person is plucked from "anonymity" in the collaboration and propelled into the limelight. At the same time the entire collaboration is given prominence and publicity.
That granted, collaborations obviously take considerable care choosing who is to speak at conferences, particularly when presenting their first results. There is a wide scope for diverse and conflicting interpretations of their findings in the early stages of their work. As a result it is deemed essential that highly competent, and confident, members of the collaboration speak at this phase. Of course such an opportunity further reinforces the power and prestige of senior physicists both inside the collaboration and inside the community—what Merton called the "Matthew Effect" is omnipresent in large collaborations. At the same time everyone knows that it would be suicidal to put a junior, or timid, member of the collaboration in the firing line when results are likely to be heavily contested. They have opportunities later, when the collaboration has established its credentials, when data and papers are flowing regularly off the detector, and when members are being invited and encouraged to speak at many conferences.
Granted the importance that physicists attribute to speaking at conferences, to the extent that sometimes they even contest the order of the program, it was striking to find that those interviewed were generally satisfied with the way talks were distributed. There are two main reasons for this. Firstly, neither interesting results nor conferences at which to present them are a scarce resource for large, successful collaborations, so that most people get an opportunity to speak on their work sooner or later. Secondly, physicists seem to accept with resignation the uneven, hierarchical distribution of rewards inside a collaboration, to accept that some people regularly speak at the more important conferences than others. That "resignation" is not a sign of subservience, though. Physicists inside the collaborations studied had clear ideas about the competence of their colleagues, and felt that it was in the common good that the best speakers presented the most significant results at major sites and meetings. It was good publicity for the individual. But also good publicity for the collaboration as a whole.
The third and last way of gaining credit inside a collaboration is by making an individual contribution to an aspect of the collaboration's work. This could be anything from designing and commissioning an important piece of detector hardware to tackling a particular physics topic in an interesting and unusual way. The key thing is to do something which individuates you from the other members of the collaboration—and to ensure that other people in the group know what your contribution is. As one interviewee put it, there is no point having bright ideas if you do not tell others about them, and there is no point either in burrowing away on your own if no one else is aware of what of you are doing. In short, it is increasingly difficult inside large collaborations to gain recognition simply because one is a good physicist. One also has, to a certain extent, to "sell" oneself, to make sure that one's efforts are visible to the rest of the collaboration. What you know matters. Who you know—and who knows you—also matters, and increasingly so.
IS TEAMWORK ANTITHETICAL TO INDIVIDUAL AUTONOMY AND CREATIVITY?
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The "factory model" of large collaborations reflects and reinforces another pervasive view about work in large teams: that it leaves no space to individual autonomy and creativity. Individual researchers, as Robert Wilson puts it, are conventionally seen as "doing creative, poetic, and enduring work..." while team research is regarded as "superficial, uncreative, and dull; ...." Mertonian sociologists would go further. Since "basic science is an individualistic enterprise," team research cannot be compatible with basic research. As we shall see in this section, all of those interviewed confirmed Wilson's feeling that these attitudes are little more than "preconditioned responses" and "cliches." They persist because they are part of a constantly regenerated ideology which pivots around images of the scientist as an individual creative genius. They are increasingly irrelevant, not simply because they do not square with the realities of an individual's life in a large collaboration. More fundamentally, I shall argue, they are inappropriate because physicists working in such teams have a very different idea to their predecessors of only 20 to 30 years ago of what doing physics actually means. They draw—they have had to draw—the boundary between their activity as physicists and the activities of technicians and engineers in ways which are new, at least for Europe (as opposed to the U.S.A).
But more of that later. First, let us try to capture what individuals working in the collaboration we studied felt about team research. While there were obviously differences in emphasis between the respondents, one of them summed up the situation in terms which would probably be acceptable to all. "I feel sorry," he said, "that teams have become so big. On the other hand, we have to live with it. And [I would] say that we [have] managed a lot better than I could have [foreseen]." This attitude is confirmed by the findings of an American HEPAP subpanel who were also surprised to find that even young investigators were not disenchanted with teamwork. "We happily transmit the view from within large collaborations," the panel reported in 1988, "that—at least for many—life is far more challenging and far less anonymous than it sometimes seems to be from without, despite all the frustrations. Teamwork then, is not fundamentally incompatible with individual fulfillment and job satisfaction, an observation which would surely be utterly banal and unsurprising but for the pervasive grip of the myth of the lone scientist.
The most basic reason why individuals do not feel crushed inside large collaborations is that there is a high degree of fragmentation and distribution of tasks (see Figure 1). As a result physicists find themselves actually working in small groups, sometimes of only five or six people, groups that will be responsible for a particular part of the detector or for the analysis of a particular set of data. Within these groups there is considerable scope for individual autonomy and creativity. In fact the detectors are so complex, and the data so profuse, that there is an enormous variety of work to be done: hardware research-and-development, electronics, computing, analysis.... Ironically, then, and quite contrary to what conventional wisdom would have us believe, there can be more scope for individual autonomy in a large collaboration than in a small one.
That autonomy, of course, is not a priori guaranteed. On the contrary—and this is another reason why the reality of group research does not square with the myth—individual physicists and institutions take deliberate steps to try to ensure that they are not dominated in a collaboration. They are careful about whom they team up with. As one university physicist in UA2 put it, he preferred to work in collaborations with five or six other groups rather than in a very large collaboration like UA1 because in that way "a rather smallish group as we were could have a major role." In a similar vein the three British teams went into UA1 as "one strong group because we felt that we had to put up a united front and because we felt we would work better that way." Participating institutes also try to take responsibility for a crucial part of the detector as this will give them more weight, e.g. by building the trigger processors for the calorimeters in UA1 the UK groups were guaranteed a central role in the collaboration. Finally when it comes to data analysis, physicists do their best to ensure that they can work in an area which interests them. As one group leader put it, he had "always been very careful about the behavior of my group inside the collaboration," making sure that "we are doing interesting things," not just building detectors for other people, but "doing our physics." In short, if physicists find that they have space for individual satisfaction inside collaborations it is also because they adopt deliberate strategies to protect their autonomy and that of their group.
So far I have concentrated on structural and strategic explanations of why work in collaborations is compatible with individual autonomy and creativity. There are also more personal considerations. Above all there is the pleasure of being involved in a collective effort directed toward a shared objective. This might mean working night and day with 50 or 100 people down in a humid and cold pit to assemble a detector as quickly as possible. Or it might involve spending hours with one's colleagues discussing the significance of the data coming off the device. These are aspects of group life which are simply not accessible to the individual worker or, indeed, to the worker in a small team.
This brings me to the last advantage of team research that I want to mention: that there are a large number of people available to discuss results during the analysis phase. This is invaluable given that novel data off a detector are open to a wide range of diverse interpretations, and that convergence on a shared meaning requires an intensive exchange of ideas. By meeting frequently with their colleagues every day if they are working on a hot topic (cf. above)—the members of the collaboration slowly build a rationally justifiable version of the phenomena which they believe in, and which they can present to their peers as a "result." Seen in this light, group discussions surrounding data are not only satisfying to the individuals who participate in them. They are epistemologically essential.
What of the disadvantages of research in very large teams, what do the participants feel they have "lost?" The feature most often mentioned by those who have worked in smaller groups is that they can no longer contribute to, and master, all aspects of the experiment. They are forced to specialize, and increasingly so as the teams get bigger. As a result they do not feel that they are "in touch" overall with the equipment they are using, that somehow the detector and its data are out of their control.
We have argued above that doing experimental physics in a big collaboration can indeed be satisfying to individual participants. And as we have remarked, at one level this finding is banal, little more than a useful antidote against a number of cliches and "preconditioned responses" about the nature of team research. At the same time, from another, more interesting point of view, this result is of considerable significance. For it indicates that experimentalists in large collaborations have a conception of their role, of what it is to be a physicist, which allows that it can be creative and satisfying to spend four or five years—perhaps more—of one's life designing and building a piece of complex, heavy equipment, that that too is "doing physics."
This has not always been so, at least not in Europe. Certainly physicists have always understood that equipment was needed to do an experiment, and have often designed and built it themselves, perhaps with the help of one or two technicians. But this kind of work was done quickly, exceptionally in a few weeks (see the quotation at the head of this paper), more likely in a few months, at most perhaps in a year. After that they would get down to taking and analyzing data, doing physics with a big P as the practitioners usually call it. However as the timescales for detector building have extended, and as physicists have become involved in all aspects of construction, so they have come to redefine what physics is (to the extent of being willing to give a Ph.D. in physics to a graduate who works entirely on developing a piece of detector hardware). And to redefine their identity as physicists.
Of course these attitudes were not uniformly shared among those we interviewed. There was some nostalgia for the past. There was also the usual conservatism about the future: while it was "reasonable" to spend three to five years building a detector (as they had done), doing so for eight years, the time needed for some LHC and SSC devices, was "another thing." But the central image was clear:
Interviewer: Did you yourself play a role in building equipment?Physicist: Yes.Interviewer: You stopped doing physics?Physicist: No. That's doing experimental physics.
The contemporary experimentalist's concept of "doing physics" is not simply different, it is also obviously far broader and richer than that of his or her predecessors of only a generation ago. The following sequence of quotations give one an idea of what is involved. The physicist just cited was asked if he would not have liked to be taking data on another experiment while building the detector for UA2 (which took over three years of full-time effort). He replied:
No, I can't do that. I mean I really want to be, when I have an experiment to do, [involved] from the beginning. I can't do other things.... That's my problem. I mean in fact, when you design and build a calorimeter...you don't actually go blind into a certain design. You build a prototype and then you take this prototype to a beam and then you play with the beam and you change the components.... You design a system of flashlights which send artificial signals to the photomultipliers to keep the stability under control, and this requires writing a program that manages all this pulsing by computer, and writes files of calibration constants. Then you know you change the thickness of the lead and the scintillators to see how much you can influence the linearity....
This takes about a year, whereupon the design is frozen, and discussions with industry begin in earnest. Since the photomultipliers have to be very stable
You have to do a lot of searching among the various photomultipliers on the market to find out which one is the most stable. You have to discuss with industry. That's all physics. And then eventually you write technical notes and you publish in technical journals. Its not only screwing screws. Its development , its R & D.
Once the order is placed,
...it takes a few months before you have the first pieces coming back for the assembly, and during that time you start thinking about physics again. You develop simulation programs, you write special physics routines which will eventually be used in the final analysis. And then when the things come back from industry, and they're assembled, then our calorimeters have to go back on test beams for calibration.... We spent a year...at the PS, calibrating everything in the calorimeter cell.
Building detectors, in short, involves a variety of activities and mobilizes a number of very different skills and techniques, all of which are now seen to be an integral part of doing physics, not a distraction from its main purpose, all of which are included in what it means to be a physicist.
Included too, as these quotations show, is a relationship with industry which was more or less foreign to European physicists working at CERN in the late 1950s and early 1960s. At that time it was the engineers, the accelerator builders, who were actively engaged with industry, who designed and built prototypes, who exchanged knowledge and experience with their counterparts in firms, who pushed suppliers to the technological limit. For physicists, on the contrary, the relationship to industry was essentially passive. It was seen as a supplier of sophisticated though standard equipment, which was bought off the shelf and treated more or less as a "black box." This is no longer so. The relationship with industry is far more dynamic, interactive. Physicists now see it as a source of new ideas and techniques to be exploited and adapted to their novel purposes. CCDs, or Charge Coupled Devices, are a good case in point. Developed in the early 1970s, the technology was originally limited "to expensive and complex military systems." By the mid-70s it appeared that the technology "may be on the verge of making a `big splash into low-cost high-volume applications.'" And an informal note was circulated inside the embryonic UA1 collaboration explaining their potential for "use with charged particle detectors." Put differently, the concept of being a good experimental physicist now includes being aware of what new products industry, and especially high-tech industry has to offer, and of being able, as Dominique Pestre put it, "to use industrially available material in new and interesting ways."
This new identity, these new attitudes among European physicists, are in fact indicative of a generalization of the role of the physicist which emerged in the United States between the 1930s and the 1960s. Basic science was transformed in this period, above all by its integration into the military-industrial complex. A new way of doing physics emerged, a new kind of researcher was molded, a researcher who, to quote Pestre again, "can be described at once as physicist, i.e. in touch with the evolution of the discipline..., as conceiver of apparatus and engineer, i.e. knowledgeable and innovative in the most advanced techniques..., and entrepreneur...," i.e. capable of mobilizing and managing important human and material resources. Until the early 1960s this transformation in the role of physicist was restricted to the United States, where it was embodied in the activities of men like Luis Alvarez: European physicists were largely excluded from it. But then a new generation came on the scene, the men and women of whom we are speaking here. They completed their Ph.D.s in the early 1960s. Most of them have spent at least two or three years working in the States. And—competition oblige—they have internalized the role of a physicist which working in large collaborations around big detectors demands of them.
In our interviews there is another, interesting symptom of the internationalisation of the "American" conception of what it means to be a physicist. It is the view that physics is fun. In fact it is striking that those we spoke to hardly if ever assessed their experience in large collaborations in terms of the space allowed them for "creativity" or for "freedom to follow their own ideas." These concepts are more or less irrelevant, relics of a bygone ideology, appropriate to the impoverished poetic genius of myth, not to the hard-nosed professional of reality. For them what counts is having fun. This "hedonism," Forman has argued, emerged in the U.S.A. in the late 1950s, where it was at once indicative of the new social niches being filled by physicists, and of their rejection of the old idea of themselves as morally superior beings. Its implantation in Europe is yet another indicator that the Old Continent has, at last, "caught up" with the New.
While at one level this notion of fun, admittedly vague, apparently means the satisfaction which comes from playing with new ideas, it seems to have another significance for those working in teams. It refers to the quality of life in the collaboration. For one physicist it was what was lacking in UA1, undermined by the ever-present danger of a bruising conflict with the spokesman. As he put it, thinking back over his thirteen years in the collaboration, "it was exciting but it should have been more fun." Fun is what one has with others, and it is based on building up meaningful and durable links with colleagues. These links are established through spending minutes and hours, days and nights, months and years working together around one piece of equipment. They are the result of hard work and dedicated collective effort. They are reinforced at countless collaboration meetings, workshops, summer schools, and conferences, many of them in exotic places. And they require an atmosphere which leaves space for individual freedom and for collective play and relaxation. They are the backbone of a community which is concentrated more and more at a few research sites around a few huge detectors. And whose solidarity and internal organization are so formidable that they are able to raise, and to go on raising, the money that they need to do increasingly expensive physics—and to have fun.
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Bud, R., and S. Cozzens, eds., Instruments and Institutions: Making History Today, Proceedings of a Conference held at the Science Museum, London, March 1991 (SPIE, 1992).
Crozon, M., La matiére premiére (Paris: Editions du Seuil, 1987).
Forman, P. "Social Niche and Self-Image of the American Physicist," in M. De Maria, M. Grilli, and F. Sebastiani, The Restructuring of Physical Sciences in Europe and the United States, 1945-60 (Singapore: World Scientific Publishing Co., 1989), 965.
Galison, P., "Bubble Chambers and the Experimental Workplace," in P. Achinstein and O. Hannaway (eds) Observation, Experiment, and Hypothesis in Modern Physical Science (Cambridge: The MIT Press, 1985), 309-73.
_____, How Experiments End (Chicago: Chicago University Press, 1987).
_____, "The Evolution of Large Scale Research in Physics," in HEPAP (1988), 79-93.
_____, "Bubbles, Sparks and the Postwar Laboratory," in L. M. Brown, M. Dresden, and L. Hoddeson, Pions to Quarks. Particle Physics in the 1950s (Cambridge: Cambridge University Press, 1990).
Hagstrom, W. O., "Traditional and Modern Forms of Scientific Teamwork," Administrative Science Quarterly, 9 (1964): 241-63.
Heilbron, J., and R. Seidel, Lawrence and his Laboratory. A History of the Lawrence Berkeley Laboratory. Volume I. (Berkeley: University of California Press, 1989).
Report of the HEPAP Subpanel on Future Modes of Experimental Research in High Energy Physics, July 1988, US Department of Energy Washington, D.C., Report DOE/ER-0380.
Heusch, C. A., U.S. Participation at CERN: A Model for International Cooperation on Science and Technology, paper prepared for the Workshop on U.S. Participation in International Science and Technology Cooperation, Washington, D.C., September 28, 1983, and published as an EP Note, January 20, 1984 (Geneva: CERN, 1984).
Holton, G., "Les Hommes de Science ont-ils Besoin d'une Philosophie?" Le Débat, no. 35 (May 1985): 116-38.
Kowarski, L., "Team Work and Individual Work in Research," in N. Kaplan (ed.), Science and Society (Chicago: Rand McNally, 1965), 247-55.
_____, An Observer's Account of User Relations in the U.S. Accelerator Laboratories, Report CERN 67-4 (Geneva: CERN, 1967).
Krige, J., The Relationship Between CERN and its Visitors in the 1970s, Report CHS-31 (Geneva: CERN, 1990).
_____, "The International Organization of Scientific Work," in S. E. Cozzens, P. Healey, A. Rip, and J. Ziman (eds), The Research System in Transition, NATO ASI Series D, Volume 57 (Dordrecht: Kluwer, 1990), 179-97.
_____, "Institutional Problems Surrounding the Acquisition of Detectors in High-energy Physics at CERN in the Early 1970s," in R. Bud and S. Cozzens (eds.), Instruments and Institutions: Making History Today, Proceedings of a Conference held at the Science Museum, London, March 1991 (SPIE, 1992).
_____, and D. Pestre, "The Choice of CERN's First Bubble Chambers for the Proton Synchrotron (1957-1958)," Historical Studies in the Physical Sciences, 16 (2) (1986): 255-79.
Morrison, "The Sociology of International Scientific Collaborations," in R. Armenteros et al., Physics from Friends. Fetschrift for Ch. Peyrou (Geneva: Multi-Office, 1978). Also published as internal report CERN/EP/PHYS 78-38 (Geneva: CERN, 1978).
National Science Foundation, International Cooperation in Big Science. Papers Presented at a National Science Foundation Symposium, Washington, D.C., February 19, 1985.
Pestre, D., "The Organization of the Experimental Work Around the Proton Synchrotron, 1960-1965: The Learning Phase," in A. Hermann, J. Krige, U. Mersits and D. Pestre, History of CERN. Vol. II. Building and Running the Laboratory, 1954-1965 (Amsterdam: North Holland, 1990).
_____, and J. Krige, "Some Thoughts on the History of CERN," paper presented at a Stanford Centennial Workshop, August 25, 1988 organized by P. Galison and B. Hevly on the topic Big Science: The Growth of Large Large-scale Research. It is to be included in a collection based on the meeting to be published by the University of California Press.
Pickering, A., Constructing Quarks. A Sociological History of Particle Physics (Edinburgh: Edinburgh University Press, 1984).
Swatez, G. M., "The Social Organization of a University Laboratory," Minerva, 8 (1970): 36-58.
Taubes, G., Nobel Dreams. Power, Deceit and the Ultimate Experiment (New York: Random House, 1986).
Traweek, S., Beamtimes and Lifetimes. The World of High-Energy Physicists (Cambridge: Harvard University Press, 1988).
Watkins, P., The Story of the W and the Z (Cambridge: Cambridge University Press, 1986).
Weinberg, A., "Scientific Teams and Scientific Laboratories," in G. Holton (ed.) The Twentieth-Century Sciences. Studies in the Biography of Ideas (New York: W. W. Norton, 1972), 423-42.
Westfall, C., "Fermilab: Founding the First US 'Truly National Laboratory,'" in F.A.J.L. James (ed.), The Development of the Laboratory. Essays on the Place of Experiment in Industrial Civilization (London: Macmillan, 1989), 184-217.
Wilson, R. R., "My Fight Against Team Research," in G. Holton (ed.) The Twentieth Century Sciences. Studies in the Biography of Ideas (New York: W. W. Norton, 1972), 468-79.
APPENDIX: A COMPARISON OF THE SITUATION AT CERN WITH THAT IN SIMILAR U.S.
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The AIP project on how multi-institutional collaborations in high-energy physics are set up and grow has made provision for comparisons between the situation in Europe and the U.S.A. While the results are still tentative, and generalizations are rather precarious, three points do seem to have emerged.
Firstly, speaking generally, there are marked similarities in the organization of experimental work in high-energy physics on both sides of the Atlantic. This is only to be expected. The size and the nature of equipment, on the one hand, and the need to compete on the other, necessarily imposes a certain uniformity on the practice of high-energy physics. At the same time these similarities in practices in the late 1970s and 1980s are indicative of the fact that Europe, which lagged behind the U.S.A. in this field for the first two or three decades after the war, has caught up. European physicists, who generally felt looked down on by their American colleagues in the 1960s, are now more self-confident, and feel themselves to be on a par with their American collaborators and rivals.
A second important finding which emerged from interviews both in CERN and in the U.S.A. was that the infrastructural support at the Geneva laboratory was generally regarded to be better than in most American facilities. American physicists appeared to be more individualistic, and more likely to take the initiative in having an ad hoc lash-up, or in developing computer programs particularly suited for their own personal needs. European physicists, benefiting from a strong and available in-house staff of engineers, computer scientists, and technicians, tended to rely more on this kind of support in their everyday work. The American style of doing experimental physics, if one can call it that, with the scope that it gave for individual initiative, seems to have been particularly well suited to experimental practice in the 1970s. It was generally felt, however, that the perhaps rather more ponderous, but also more professional and perfectionistic approach of the Europeans was better suited to the big detectors of the eighties and the nineties.
A third important finding concerned the relationship between CERN and its user community. As a matter of policy CERN has been set up to serve the entire European physics community, and has an important responsibility to it. Geneva is the undisputed center of gravity of high-energy physics in Europe, and for this reason of course it has built up the important infrastructure that has just been described. The situation seems to be rather different in the U.S.A., where the relationships between in-house staff and outside users have sometimes been rather more strained. The situation will no doubt change if or when the SSC is built, particularly if it is a joint venture between the U.S.A. and other countries. The cost and the uniqueness of the machine will demand collaborative patterns which will probably be closer to some of those which have been developed in Europe where the groups are not only multi-institutional but actually multinational. This could affect such down-to-earth matters as the scheduling of experiments. Many European physicists found that this could be subject to last-minute changes at U.S. facilities, a matter which caused them considerable inconvenience considering the distances that they had to travel. At CERN by contrast, machine schedules are kept to rather rigidly—a system which facilitates forward planning but can frustrate those who want to do something quickly. If or when U.S. laboratories have to collaborate with physicists coming systematically from Japan and Europe, a more inflexible system of scheduling will probably have to be imposed.
C: A SMALL SAMPLE SET OF INTERVIEWS WITH WOMEN IN HIGH-ENERGY PHYSICS (by
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In keeping with the interest of the AIP Center for History of Physics Advisory Board, the Collaboration Study included a focus on women in science. The project's interview program included only ten women who had participated in the selected experiments. Project staff developed a question set to administer to women that was more personal and of broader scope than the question sets administered to women interviewed as part of the selected experiments. The question set for women was developed near the completion of the project's already ambitious interview program, severely limiting the number of women the staff were able to add to the project schedule. Only five women were interviewed using the new question set and the paucity of data precludes us from presenting any conclusions here about the concerns or experiences of women in physics. In the next stage of the project, we will use the question-set for gender issues when interviewing women in space science and geophysics so that we will be able to build a better foundation for generalizing on women in the physical sciences.
Our interview program of 19 selected experiments included only ten women. To increase our perspective on women in the high-energy physics community, we interviewed five women who were not on our selected experiments using a more detailed question set focusing on the issues of gender in high-energy physics careers. Topics included family and early educational influences, sexism, and discrimination as they affected their professional work. Interviewees included a graduate student, an assistant professor, a tenured professor, and a senior lab physicist, all currently active in high-energy physics, and a woman who left high-energy for another field in physics. They were educated in English- and French-speaking Canada, Germany, and the United States. Some of the issues discussed below include responses of women from our selected experiments, who were asked less-detailed questions about the effect of gender on their professional work. This second group includes graduate students, postdocs and junior and senior faculty educated in Canada, France, Italy, and the United States. Unless stated otherwise, the responses discussed below refer to the five interviews specifically about gender issues.
We have learned that it is difficult to interpret the responses given to gender issues. For example, some interviewees would give responses that indicated they had experienced considerable sexism, but would then dismiss the situation they had described as though it were not even worth mentioning. One interviewee spoke very clearly through most of the interview, but during her description of male behavior that makes her uncomfortable in meetings, her voice became inaudible and the transcriber was unable to make a clear transcription of her comment.
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Interviews uniformly pointed to the school system, at the junior high and high school levels, as an important place to encourage girls to feel that they have as much likelihood of success in science as do boys.
High-school education was pointed out by all interview subjects as an important place to focus efforts on encouraging more women to go into physics, because that's where they felt they had had to resist powerful peer pressure in order to pursue science (see Section VII. "Recommendations From Women Physicists," below). Only one said that a female high-school science teacher was an important role model, but she also noted that most of the school's science teachers at this girls school had a patronizing attitude to the students and did not seem to expect them to succeed. Other interviewees did not recall high-school teachers as having influenced their choices. Three out of the five interviewees attended single-sex high-schools. It's hard to believe such a high representation of girls' schools is a coincidence, though it may be, since this is such a small sample of the population.
By the time these five were studying science in college, they seem to have been following a chosen path. One mentioned feeling intimidated, going to a hard-core science university after attending a high school with poor science education and having relied on parental guidance for most of her earlier science training. Others said they were used to being "weirdos," so being a minority of 2% was not any more alienating than their previous experiences. One, in fact, mentioned that going to a serious science college posed an adjustment problem because it made her feel normal for the first time. The impact of Sputnik, with its advent of recruitment of students into science education by universities, stimulated one of the five to choose a science career. Her primary interest had been in art, but when she began looking for a more lucrative career choice, science, as a profession highly advocated in her high school, became an obvious option. When MIT recruiters came to her high school, her guidance counselor told her to see them; she applied and received early acceptance with financial assistance.
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Entering graduate school meant exhibiting proof to others that these women had proven ability and commitment to physics. Lack of women classmates was not seen as having made as great an impact on their graduate school experience as did the attitudes of advisors, though one mentioned being lonely in graduate school because she lacked women friends. Another mentioned being disappointed that her advisor did not allow her to take on hardware tasks that she felt were important for her to learn; she felt this was distinctly sexual discrimination. Another, from the interviews for selected experiments, said that—while she was unaware of it at the time—she believes in retrospect that her advisor's selection of her thesis topic was sexist (analyzing emulsion plates and doing reams of tedious calculations: an effort which had been traditionally acceptable as "women's work").
Though the decision to become high-energy physicists came toward the end of college careers, many influences affected the eventual choice along the way.
Only one of the five interviewees, an American who attended a girls' school with very little science, credited her parents, who were both biologists, with stimulating her interest in a science career. Parents of the other four were less supportive. Role models included a female high-school teacher and Marie Curie, for one, and parents, for another. Most, however, were not able to identify any role models, but were stimulated by their own intense desire to learn and to accept challenges.
The only visible impact of nationality on these interview subjects was the difference in educational systems. Interviewees observe that most women in physics have been European and, only recently, have more Americans been represented among their female colleagues. Interviewees from Germany and Italy (the Italian was on a selected experiment) both mentioned that compulsory science education for several of the school years before entering university was no doubt important in explaining the higher frequency of choice among European women for physics. In the U.S.A., high-school students normally are exposed to no more than one year of physics, and that is rarely compulsory.
TO BECOME A HIGH-ENERGY PHYSICIST
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All of the five interviewed for their perspective on gender in high-energy physics had a clear desire to become scientists before attending college: three because they were drawn to philosophical questions about the nature of the universe, one because she desired a more financially feasible alternative to her artistic pursuits, and the fifth because it seemed like the most challenging curriculum. None became committed to particle physics until after matriculating as undergraduates; they became drawn to it through summer jobs or classes they took in junior or senior years. One might have gone to graduate school in medical research had she not been invited to be the graduate student of a highly eminent particle physicist at CERN.
ADVANTAGES AND DISADVANTAGES
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According to interviewees, the single most obvious effect that being a woman has on a physicist's career is that it makes her more visible. For some women, visibility induces a need to perform above average all the time, because the attention is judgmental in nature, suggesting a low estimation of female abilities. But one interviewee has found visibility to be an advantage in that she has been invited to be on a greater number of prestigious committees than most of her peers. She feels embarrassed about how many people seem to know her.
One senior physicist believes that men who head large projects have the advantage of not carrying domestic burdens, and that wives still put the most energy into arranging family events and organizing the household. (Four of the five women we interviewed were married, three of these to physicists.)
Three of the five women interviewed have children. They found institutional support for maternity leave and day-care wanting. One feels lucky to have gotten two quarters off around the birth of her child, because her university department only grants one quarter for maternity leave (as a new faculty she was entitled to a quarter which she tacked onto her maternity leave). In her opinion, three months is the minimum acceptable maternity leave. Another had no maternity leave and spent more for a baby sitter than she earned at work. When this situation became intolerable, her department chair could not understand why she was having a hard time. The third said her laboratory granted no maternity leave. She had to use accumulated sick leave for time off work. None of the interviewees had easy access to day-care at their place of work.
One said that comments male colleagues have made (e.g., their belief that it isn't possible to be a mother and still earn tenure) makes her wonder if men saw her as a less serious physicist when she became pregnant.
There is disagreement about whether a woman should "stop the clock" on her tenure. Stopping the clock is a policy, being discussed at many universities, that would allow women on the tenure track to discount time taken for maternity leave from the time period reviewed by the tenure-granting committee. One said she does not want to and has not stopped the clock during maternity leave because she doesn't want to put off getting tenure. Another said that if the time for earning tenure is prolonged for women, much more will be expected of them before they are awarded tenure. Others, however, say it is necessary that women be able to stop the clock in order to get tenure.
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Only one interviewee said she had strong interest in "feminism." She has been very disappointed by the degree of sexism she has encountered—degrading images of women in laboratory and university machine shops and even on a transparency used during a large collaboration meeting. Her requests that these be removed have been completely ignored and she has been warned, by a female colleague, not to "make waves" if she wants women to become fully accepted. Another wonders if she just hasn't noticed sexism. Other women clearly find peers who complain about sexism a "drag" to work with.
Three interviewees (including one from a selected experiment) believe that women provide more opportunities for a greater number of collaborators to be heard during meetings, that women are more receptive to other physicists' ideas, and that they encourage a more cooperative and less competitive dynamic within the collaboration. Most others do not notice any gender-related dynamics at collaboration meetings or elsewhere, except that male colleagues occasionally make sexist comments that they feel are best ignored, and do not believe that collaborations with more women would be any different than current collaborations.
DISCRIMINATION AND HARASSMENT
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An Italian physicist noted that although there have been more women physicists in Europe for some time, none of them have gotten into top positions at CERN. Another physicist agreed that women have been no more successful in the American laboratories.
Two of the women we spoke to (one of the five and one from a selected experiment) said they were discriminated against when it came to promotions. Both women had already won respect within the field before they experienced sexual discrimination; possibly they had met a ceiling for women in their institutions.
One interviewee was seduced by her professor during graduate school. Another was sexually harassed by a professor. When she argued with him, he had her fired from her lecture job. She filed a complaint and the professor was reprimanded, but she did not get her job back and her financial support was withdrawn. This professor is now on a national committee for the advancement of women in science. The interviewee found later, when she applied to another graduate school, that her former department chair had contacted the chair at the school to which she was applying to "warn them" about her being a troublemaker.
RECOMMENDATIONS FROM WOMEN PHYSICISTS
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• The provision of day-care facilities is very much needed. Day-care is not provided by the laboratories represented in this sample and at one university there was a three year waiting list for day-care.
• A semester off of teaching is recommended.
• Education for men about sexism was recommended by one interviewee.
• High-school education was mentioned by all as an important focus for attracting more women into physics.
• Outreach to young women, not just in physics classes, but to affirm their abilities to succeed and to broaden their horizons was suggested as a way of increasing the number of women choosing physics as a career.
• The most substantial improvement recommended was improved high school and college introductory physics courses. One professor said she hates teaching the freshmen physics course at her university. She says it is boring, focusing on the least interesting questions in physics. Introductory classes fail to introduce students to the exciting issues of contemporary physics research. Classes that discuss the lifestyle of physicists and the work that they do would be much more effective in making students think seriously about becoming physicists.
• The contrast between European and American physics curricula was noted by the two European interviewees as a significant factor in the number of women pursuing physics Ph.D.s. Most American high schools only offer one course, while European secondary schools may require physics for several years; one of these interviewees pointed out that if a student gets an uninspiring teacher one year she can still get a good teacher another year. In addition, students with more courses are able to learn more sophisticated and stimulating physics in a European high school. It may well be that improved physics education would have more success than any gender-focused attempt to attract more women into physics.
PROBE REPORT ON HISTORY OF THE PSI EXPERIMENT (by Peter Galison)
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Beginning in the 1960s and continuing through the mid-1970s, an extraordinary set of experiments took place at the Stanford Linear Accelerator Center (SLAC), experiments that were joined in the latter part of this period by a group of physicists from the Lawrence Berkeley Laboratory (LBL). These experiments, which began as an effort to build a colliding beam facility in which electrons would ram into oppositely-moving positrons, ended in the discovery of a new family of particles starting with the psi. In a sense, the legitimation of these new particles, which were probed simultaneously by a joint team from Brookhaven National Laboratory (BNL) and the Massachusetts Institute of Technology, opened a new era. Physicists have come to think of this era as the "third spectroscopy," the first was atomic, the second nuclear, and this third the spectroscopy of quark systems. For the high-energy physics community, there is no doubt that this new spectroscopy set the quark model, and high-energy physics more generally, into a time of rapidly changing instruments, experiments, and theories.
The particular experiment that found the psi was labeled SP-17, SP for the facility at SLAC where it took place, SPEAR (Stanford Positron Electron Asymmetric Ring). In this ring, the SLAC/LBL collaboration built a complex and composite detector known later as the Mark I detector, a device that combined the individual electronic components of spark chambers, muon detectors, scintillators, and (for the time) sophisticated computer-run trigger and data acquisition system. As it was the first attempt to build a nearly 2-pi sensitive electronic detection system, the Mark I itself became something of a prototype for many future colliding beam detectors.
My purpose in writing this probe report is not to give an extended analytical study of the discovery of the J/psi, of the type I have given elsewhere for the discovery of neutral currents. It is, instead, an exploration of the archival sources relevant to writing a proper history, written to alert archivists, physicists, and administrators to the kind of questions and themes that interest at least one historian of contemporary physics. I will therefore focus in some detail on a wide variety of different kinds of sources ranging from reports to raw data, and will explain how I would use them in historical work. My hope is that this will supplement the survey work and archival records explorations that will be provided in other parts of these AIP reports.
It will be useful to divide the analysis into three quasi -spatial divisions: microanalysis, mesoanalysis, and macroanalysis. Under microanalysis, I have in mind two lines of inquiry. First, there is the microphysics itself, including the development and changing views of the physics goals of the experiment, the selection, acquisition, processing, and interpretation of data, and the interaction of experimental practice with current theory—both "grand theory" and the lower-level phenomenological calculations and models that link experimental data to field theory. Second, microanalysis must include the detailed organization, construction, testing, and running of the apparatus—in the case at hand how the team of physicists and engineers built, borrowed, or modified apparatus to constitute each of the component parts of the detector.
Under mesoanalysis, I have in mind the history and sociology of the laboratory dynamics: how the experimental group vies with other groups for beamtime and resources. In the present case, one wants to know how the constituent institutions interacted—what traditions of work organization, physics questions, and equipment came with the LBL team and what emerged from the SLAC group.
Finally, by macroanalysis I have in mind the larger issues that linked the laboratory to the broader world. In the case of the J/psi it is impossible to ignore the direct interdependence of the Mark I detector with the development of SPEAR, and this in turn cannot be understood without situating the project in the history of colliding beam facilities, the competition between hadron and lepton research programs, and the location of particle physics within the research environment of the Vietnam and immediate post-Vietnam epoch (1965-1975).
Readers interested in a linear account of the fast-paced events of November 1974 and its immediate aftermath would do well to consult three helpful sources: Michael Riordan's popular book, The Hunting of the Quark (New York: Simon and Schuster, 1987), which combines the author's own recollections as an experimental physicist with some documentation and many lively interviews; Andrew Pickering's, Constructing Quarks (Chicago: Chicago University Press, 1984) in which he invokes a sophisticated sociological approach (published sources and interviews) to analyze the acceptance of the Standard Model; and Gerson Goldhaber's participant's reflections in Maglic's Adventures in Experimental Physics.
SOURCES FOR THE PSI AND HISTORICAL INQUIRY
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The written sources cited in this report were supplemented by some 10 interviews conducted with participants in the experiments. These ranged from Schwitters (then a postdoc) to the then director of SPEAR (Burton Richter) and some of the leading members of the LBL group, including Gerson Goldhaber. In addition to their intrinsic value as oral histories of the experiment, these interviews were vital in locating many sources that were not part of the archival record, such as notebooks letters, draft proposals, and experimental data.
I now turn to each of the microscopic, mesoscopic and macroscopic domains in turn, illustrating each with particularly important (or in some cases very typical) documents, glossing them for what I expect to find useful as my longer term historical inquiry.
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1. Physicists and Engineers. One of the most salient characteristics of post-World War II physics is the radically altered relationship between experimental physicists and cryogenic, electrical, and mechanical engineers. I look in particular for moments of interaction between these groups, especially as they lead to a better understanding of how engineering constraints or opportunities shaped the fabrication and direction of the physics work. For example, the following rather telegraphic comments from the minutes of Detector Meeting of 3/13/72, from Rudy Larsen to SPEAR Detector Distribution, p. 2 illustrate a multitude of important points:
Feldman: Has discussed possible space conflicts (Trigger counters cooling ducts) with Bill Davies-White; Davies-White has cognizance of situation.
Discovers light pipes can be 5" longer than previously thought, so should now be no problem at all; prototype pipes being machined and search for possible vendor starts. Four of scintillators received, remainder by first week in April.
Bill Davies-White, a mechanical engineer, was responsible, inter alia, for coordinating the mechanical integration of the different components of the detector. I would want extensive documentation of how the conflicts between the different subgroups were resolved, and how engineering demands and physics demands were brought into compromise solutions.
2. Physics and Computation. The Great Bubble Chamber Era of 1955-1970 ushered in a fundamentally new role for computers in modern science. Without them, the bubble chamber would have issued millions of pictures and they would have accumulated like a Borghesian library: an infinite labyrinth open to all and useful to no one. With the computer, this information was brought under control; the computer was used to do everything from calculations of the geometry of tracks to the constructions of physical interpretations. With the electronic age of experimentation that followed 1970, and perhaps most strikingly beginning with the Mark I, the computer played an even greater role. Without Monte Carlo simulations, the apparatus would have been vastly harder to design, the selection of events would have been more or less impossible, and the sharing of data among various groups for analysis would have been blocked. Different kinds of documents are relevant here; I will give some illustrations.
3. Data Acquisition. Before any information can be recorded at all, the format for the data needs to be established. Documents such as (A. Boyarksi to Distribution, Subject: Event Formats and Common Blocks) set out in diagrams and words how the information is to be recorded. The historical significance of this is that it reveals what kind of information at the most primitive level is being extracted from the detector. Boyarski was the computer "czar" of the experiment, taking charge of a great range of activities from the computer control display of information about the SPEAR beams, through the computer monitoring of the detector, to the preparation of data summary tapes that were used by almost everyone within the groups and many outside it.
Once the data were acquired, they went through many stages of analysis. This process of reduction is of great interest, and documents relating to it are of several types. Perhaps surprisingly, quite a bit of effort went into the meticulous examination of individual events, as was evident by the detailed scanning undertaken by Gerson Goldhaber and others of CRT scope images that were preserved on microfiche. One typical document is the following: (Schwitters to SP1,2 Experimenters, 4 October 1973):
In order to acquaint everyone with the performance of the magnetic detector, search for new ideas and problems in the data analysis, and to plan our data taking strategy for the near future, we are initiating a program of hand scanning of events on the IBM 360/91 using the 2250 scope facility.
Schwitters went on to provide an "idiot sheet" to assist in using the computer to access and classify the events. As the above quotation hinted, at stake in the exercise was not only the data, but the certification of the wire spark chamber itself.
4. Monte Carlos for Detector Design and Calibration. Documents analyzing this phase of work include computer printouts, intra-group memoranda, and minutes of group meetings; notebooks tend not to be used to record progress with programming (there are some exceptions). But a crucial historical task for this type of work is the doctoral dissertation, because the graduate students quite often are given programming tasks. The psi case is no exception, and Robert John Hollebeeks's (1975) University of California at Berkeley thesis, "Inclusive Momentum and Angular Distributions from Electron Positron Annihilation at
|s||= 3.0, 3.8, and 4.8 Gev|
is particularly useful (see especially pp. 52ff.). Here one can follow the arguments for the establishment of the parameter eTASH(p, z) [e = epsilon; TASH = trigger associated shower; p = momentum, z = position] which gives the efficiency for the detection of a shower associated with a trigger. Arguments range from a highly simplistic physics model assuming production in invariant phase space to quite complex models involving detailed nuclear and particle physics, explicit dependence on detector response characteristics, and expected data cuts in momentum, polar angle, etc.
A historical argument seeking to show how the collaboration came to have confidence in its conclusions would include a detailed analysis of both semitheoretical and essentially experimental determinations of this parameter. While the thesis gives an excellent synchronic analysis of the different models deployed to determine TASHes, a truly diachronic study would require the availability of periodic in group reports, printouts etc.
5. Work Organization. In earlier high-energy physics experiments, even just a few years prior to the discovery of the J/psi, the work organization appeared to be structured around a two step process. First, the collaboration would disaggregate into institutional groups that would build individual component parts of the detector. When that was done, the groups would then redeploy around data analysis, with different subgroups concerned with different background processes or different event types. With the Mark I (and thereafter), one sees a third axis of work differentiation around computer programming, spanning the full cycle of data acquisition, maintenance, distribution, and analysis. For example, in C. Morehouse, M. Breidenbach, B. Hollebeek to SPGM Distribution, 20 September 1973, one finds the following assignment of programming tasks:
1. TDC's and ADC's for pipe and luminosity monitors.C. Frieberg, M. Breidenbach2. Tape Quality Checks.M. Breidenbach3. Tape copy verification.C. Morehouse4. Filtered runs to tape.M. Breidenbach, S. Whitaker
.....17. Interface Berkeley and SLAC Simulator ProgramW. Chinowsky, G. Hanson, G. Feldman18. Comparison of Data with Monte CarloEverybody
There are, of course, many subsequent reports on the status of these individuated tasks, and the problems that arise from them. Such later documents might include the results of test runs, operating procedures, or written verbal descriptions.
6. Establishment of Common Language. As the larger collaboration begins to work together, common practices have to be established to set standards for theoretical conventions, equipment building, maintenance, and data analysis. To a certain degree, each of these categories can be found in earlier experiments, where coordination between groups occurred in the scientific community writ large. With large scale experimentation, these functions are introjected into the group itself, and it is of utmost historical (and sociological) importance to understand the dynamics by which these conventions and practices are created and enforced. Memoranda distributed to the group as a whole set out many of these standards, as the following example illustrates (Lynch to SPEAR Physicists, 21 February 1973, "Computer Programming"):
Assuming that all the foregoing problems could be solved, we are still on the path to Babel unless positive steps are taken to recognize the reality that we are a large group of people who depend upon each other. The programs we shall be using must satisfy several requirements.
1. They must give correct answers. This is the first priority. This may mean that programs should be checked by persons other than the author....
2. The programs must be reliable. This is the second priority. ....
3. The programs must be intelligible. This is the third priority. This requirement is defined in terms of documentation.internal comments, and well directed programming practice.
4. The programs must be reasonably efficient. This is the fourth priority. Efficiency is measured in terms of critical resources. For on -line programming this means core space and CPU time; for off-line, the main limitation is CPU time.
5. The programs must be easy to use. This is the fifth priority. Since we are a group where people use and depend upon the programs of others, considerable attention should be applied to the "human engineering" aspect.
Each of these categories raises further questions for any history of multidisciplinary collaborations. On what problems do the different subgroups check their results? Who used the different programs? How do they get modified, specialized, generalized, and shifted from one computer to another? As Harvey Lynch put it in the memo in question, "A particularly insidious, but common form of program decay is the construction of special purpose versions of 'standard' programs. These special purpose programs have a way of generating incompatibilities and have a way of being mistaken for standard versions, resulting in chaos."
This phenomenon is relevant for our current archival projects not only in helping to explain program rot in the analysis programs, but also the degradation and incompatibility of programs in the later use of data-summary tapes, Monte Carlos, and other programs as well. What computer languages are used? What rules are established to govern writing in machine language, etc.?
7. Confrontation with Anomalies. For decades, certainly since Kuhn's Structure of Scientific Revolutions and no doubt earlier, philosophers of science have been intrigued by the responses to phenomena incompatible with current theory. In the case of the individual scientist facing such a recalcitrant result, the standard account (Kuhn and others) is that the individual at first tries rather mundane explanations (difficulties in the apparatus, more elaborate special assumptions), and only late in the game, when faced with no alternatives, are basic elements of the underlying theory questioned. In a large group, however, the group cannot be treated as a super individual. Members deploy a variety of responses simultaneously, and the whole dynamic of experimentation must be considered anew. The following quotation (drawn from Gary Feldman to SP-2 Distribution, "Energy Deficiency in High Energy Data," 24 October 1973) illustrates one of several times when the SPEAR collaboration encountered results that clashed with their expectations. It seems that Gail Hanson, Rudy Larsen, William Chinowsky and others at Berkeley noticed that there was too little energy visible in the 2.5 GeV data. Feldman made it clear in his 24 October memorandum that the resolution of the oddity could well affect the way, not only the current, but also, all future experiments at SPEAR were conducted:
Possible explanations....are listed below. All seem sightly far fetched, but I don't know any other possibilities. There is also the horrifying prospect that a combination of some or all of the effects is occurring.
1) The analysis program is not producing correct momenta. This seems unlikely in view of the beautiful results Roy Schwitters presented to the PAC, but the experts should give a final verdict.
2) The hadronic final states are not what we expected.a) There are too many o's being produced. ...we don't understand these [shower] counters very well at present. MADSIM [a computer program] currently has a zero order guess at what the shower counters do. I know how to make a first order guess, and I will proceed to insert it into the program. what we desperately need is a second order guess. This will require a Monte Carlo simulation of the shower development in the detector and extensive calibrations to the data.
b) There are large number of kaons and nucleons being produced. Gerson Goldhaber has some time of flight data that argues against this, and to my knowledge no one has seen a convincing Ko decay yet.3) There is an anomalously high multi-particle Brodsky cross section. Willie [Chinowsky] has done some calculations which indicate that under sufficiently pathological conditions, Brodsky processes could yield the type of thing we see. [Briedenbach's counters will test this.]
4) There are (possibly several) heavy leptons being produced. See Ting Pun and Martin Perl's memos of October 10 for analysis techniques. We clearly need an understanding of the shower counters and muon-pion separation.
Even from this brief except, it is clear that responses to the energy deficit range from rather routine insertions of new hardware to the supposition of an entirely new form of matter (new leptons). This kind of confrontation with anomaly, and the accompanying disposition of work to various subgroups, is of extraordinary interest (at least to me) as a glimpse into the epistemology of large-scale experimentation.
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1. Interaction With Other Groups. As Sharon Traweek has nicely discussed in her book, Beamtimes and Lifetimes (Cambridge: Harvard University Press, 1988) competition for running time is a recurrent part of life in high-energy physics. Political considerations are crucial as the teams jockey for position both in relation to each other and in relation to laboratory directorship. Any documents relating to these struggles are helpful in understanding how the laboratory functions in relation to its experimental collaborations, and how these collaborations cope with intra-laboratory competition (e.g. within SLAC). One sees this, for example, in the following, (Rudy Larsen's memo to SP1,2 Experimenters, 15 October 1973, "Run Plan for Rest of Sept. Nov. Cycle."):
4. We'll try to allow more flexibility in the schedule.For instance, if machine studies wants to run another shift on Thurs. because they are hot on something, let them. If SP -8 wants a 2hr. and 6hr. access on weekends rather than 4 hr. and 4 hr., let them. It is no big deal to us and is in our long-term interest.
This sort of interaction between collaborations can shed much light on internal laboratory dynamics. Intra-group memoranda can reveal how strategies are prepared by which each group will make its plea for beamtime. But ultimately, this decision is made by the PAC (Physics Advisory Committee, now EPAC, Experimental Physics Advisory Committee) or its equivalent body at other laboratories. In the psi case, one finds, for example, in the minutes of the February 1974 PAC meeting at SLAC, a request for 100 shifts "checkout" (of equipment), 120 shifts energy scan, 280 shifts large block (for experimentation), and 100 shifts to calibrate the background. These were approved.
Occasionally the inter-group competition affects more than a simple allocation of beamtime. For example in March of 1974, SP-17 requested further running time to exploit the upgraded SPEAR, SPEAR II. The laboratory set two experiments (SP-10 and SP-18) in the west pit, and gave SP-14 500 hours at maximum luminosity in the east pit, where SP-17 sat (the two pits designated SPEAR's two interaction regions). The PAC secretary explained the conditions of this authorization to SP-17 (G. E. Fischer to H. Lynch and R. Schwitters, "proposal SP-17," 4 March 1974, Fryberger, personal papers):
You are requested, as part of this approval, to arrange your schedule in such a way as to permit the proponents of SP-18 to run their experiment before Dec. 31, 1975. Approval of SP-18 was made under the assumption of total incompatibility with SP-17.The approval of SP -10 Supplement #3 was made under the assumption of complete compatibility with SP -17. Should this not turn out to be the case, the burden of compatibility will rest with SP-10.
The laboratory assumes that the technical problems of sharing data tapes between SP-17, SP-10, SP-18 can be worked out. It is further assumed that a data acquisition boundary between SP-17 and SP-10 with respect to baryon identification will be set in a mutually agreeable way.
A full study of the development of SP-17 would analyze the effects of these external, laboratory -induced constraints on the detector and its use.
2. Laboratory Direction. The PAC can also play a very different role, not so much in fine-tuning the distribution of resources, as in helping to set more basic directions in high-energy physics experimentation. The J/psi discovery offers a window into a rather unusual state of affairs—where the issue at hand is not the need to shift gears slowly toward a new technology or scale of work, but the immediate alteration of priorities in physics.
At the tumultuous and now famous PAC meeting of 11-12 November 1974, excited discussion followed a chaotic night and day of data taking. All that remains of director Panofsky's comments is this paraphrase (SLAC PAC Minutes, November 1974):
The Director noted that bureaucratic and physics uncertainties were unusually large at this time, and that the scheduling at SPEAR was in a particularly chaotic state. The idea of a workshop on SPEAR Detectors was raised. The problem is that historically SPEAR was not meant to be the national facility that it now seems to be and each group can't have its own detector. SPEAR II operation is going very well, and physics results already are coming in. These results can only be described as fantastic.
The meeting has become famous because it was there that Ting, who was a member of the PAC and head of the MIT/BNL group, first discussed results with the SPEAR physicists. The drama and tension of this encounter has been related in Reardon's book, and is related (with many other details) in some of the oral histories discussed earlier in this report.
Shortly after the psi was discovered, it was followed by other new particle states, and then a rapid retooling of both the experimental and theoretical communities. The laboratory
responded by holding a workshop devoted to the new particles. From the PAC minutes (10 December 1974) the rapidity of action is evident:
This meeting was called with about one week's notice so that SLAC could respond to a total of five requests for beam to study psi production other than from annihilation. It was decided that urgency should override our usual desire for mature consideration. In fact the proposals were mostly submitted on the day of the meeting.
As rapidly as these new proposals were being put forward, others were faster: between 11 November and 10 December, Richard Taylor had proposed a search for narrow width baryon resonances in e' + p -> e' + B, the experiment had been approved, and Taylor already had his team setting up the equipment.
Probably the most significant mesoscopic documentation still needed is the full collection of SPEAR and Mark I logbooks. These would allow me to track the day -to-day interactions between the running of SPEAR and the conduct of the experiment. Because of the particular closeness (intellectually as well as in proximity of the two control rooms) detector/accelerator contact is particularly close in this case. Having tracked this level of contact, it would be possible to contrast it with the more distant exchanges between the experimenters and the control room of the accelerator.
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1. SPEAR: The Relationship Between Detector and Accelerator. Every detector (except those probing cosmic rays) depends on its accelerator. Often, however, the accelerator recedes into the background as a kind of external force of nature. In such cases, experiments cannot proceed without beamtime, but the construction and operation of the beam are so far removed from the purview of the experimenters that history not only can, but probably should be written as if they were separable problems. The history of the psi cannot be written this way. From the very first, the interdependence of the construction of the first colliding beam detectors and the building and modification of SPEAR itself were intimately connected. Many of the personnel served in both capacities, developments on the accelerator side led to modifications on the detector, and changes in the detector and its physics results led to alterations in the colliding beam facility.
SPEAR was both the culmination of many years of efforts to build a colliding beam facility, and an extraordinary ad hoc financial and technical compromise. As Elizabeth Paris has nicely argued in a separate report, the history of colliding beam facilities goes back to the mid-1950s with the invention of the alternating gradient synchrotron; this provided sufficient energy and luminosity for physicists to consider running particles into one another. The resulting impact would release far more energy per particle than could be released by shooting them into a fixed target. Considered for use in the ill -fated MURA accelerator (Midwestern University Research Association), which never saw the light of day, the notion of colliding beams was bandied about by Gerald K. O'Neill, Burton Richter, and many others. Though experimentalists planned and even began building some small-scale colliders in the U.S.A. and abroad, SLAC entered the field only to find its proposals shot down one after another.
Many of the sources for the Stanford developments are contained in Richter's papers, in those of Group C at SLAC, and in the Cambridge Electron Accelerator (CEA) papers at Harvard, but a truly complete analysis would require significant archival analysis not only in the U.S.A., but in Italy at Frascati and in Russia at Novosibirsk. The competition and sometimes collaboration between these various groups must be taken into account in the final design for many aspects of the SPEAR project.
But frustration with the seemingly endless series of defeats led Panofsky to write to the U.S. Government's Office of Science and Technology after yet another rejection (Panofsky to Office of Science and Technology, 10 September 1969, 91-014 B4F4 cited in Paris):
It appears to me that this history makes a complete mockery of the effort which is going into providing scientific advice to the various agencies of the government. In this instance there has been no correlation whatever between action and the advice. As a result an entire field of scientific technology which is the only non-orthodox tool available to high-energy physics is in danger of being lost to this country entirely.
The sense of embattlement created by outside opposition surely played an essential role in the consolidation of the social and technological -scientific developments of SLAC's group C.
Lynn White once credited the rise of modern civilization to the stirrup. In some related sense, the discovery of the psi is due to an accounting trick invented by a sympathetic AEC Controller, John Abadessa. After the SLAC proposal had been shot down by the AEC for the nth time in mid-1969, Abadessa realized he could delete SPEAR as a construction line item and replace it by a simple allocation from equipment funds. He then took the $5.27 million device—equivalent in budget to SPEAR ½—then went before the Joint Committee on Atomic Energy. (Statement of John P. Abadessa, Controller, Atomic Energy Commission, JCAE FY1971 Hearings 91-014 B4F4, cited in Paris):
Representative Hosmer: Do you think all this is legal?
Mr. Abadessa: Yes, sir; it is legal. Particularly one of the reasons I appreciate the question is to lay it out to this committee and receive the judgement of this Committee on this matter...The question of legality, I am not sure that is precisely the right word, Mr. Hosmer. We have our accounting procedures and we follow them religiously. The question here is this AEC equipment or line item type thing.
Representative Hosmer: This involved some cement and things like that does it not?
Mr. Abadessa: The housing will be temporary housing at a cost of something like $20,000 out of the total $5.2 million.
Representative Hosmer: Are the foundations temporary, too, the foundations for the equipment?
Mr. McGee: There will be no foundations. There will be a temporary enclosure which will rest on the existing slab in the experimental area.
Mr. Abadessa: Essentially this is an equipment undertaking.
Representative Hosmer: Good luck with GAO [General Accounting Office].
Mr. Abadessa: Having told this Committee, we are in a lot better shape to discuss it with GAO.Chairman Holifield: All right.
Eighteen months after funding was authorized, SPEAR was on the air.
2. Communication With the Broader Community. One of the most crucial elements of the collaboration is the boundary definition of who is to have information about experimental results. Any documentation relating to the dynamics of the temptations and sanctions that enforce the boundary of silence are highly relevant. For example, we find the following (H. Lynch to SP -1 Physicists, 10 August 1973, p. 2):
There was a somewhat spirited discussion on the topic of present physics results. A strong case was made that no public statement of any kind be made until we can confidently quote [sigma] total to 10%. Anything less convincing is to be publicly "denied" to exist. An attempt was made to lower the standard to 20%, but this was quashed. W. Chinowsky suggested that we adopt a goal of the APS meeting in Chicago (4-7 February 1974) for having such a cross section ready for announcement.
This raises questions about the 10% standard (was the standard in fact standard at that time?), about the pressures to release the data under less stringent error bars, and about the choice of forum for release of information. It also suggests exploring what happened here (and in other experiments) when restrictions on information release were violated.
3. Competition. High-energy physics is a competitive business, and the suddenness and significance of the J/psi discovery threw diplomacy to the wind. A full exploration of the claims and counterclaims of priority would require a full scale history of both the J and the psi. But even with a complete set of interviews, intra-group memoranda, and a careful reconstruction of the PAC meeting of 11 and 12 November, it is unlikely that the dispute could ever be fully settled. Some members of the SLAC/LBL and the MIT/Brookhaven collaborations will probably always remain somewhat suspicious of the other. What might be possible, however, is to understand in detail the status of the cross-section results coming in at BNL during the weeks before November 11, and to understand in detail the SLAC/LBL decisions leading up to the crucial 3.2 GeV run.
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The Group C records form one of the two best and most important sources of information on SPEAR and the Mark I detector; some of these are intra-collaboration and some are limited to Group C. They are reasonably complete, well preserved in the archives, and have a very useful finding aid. Unfortunately no analogous group papers exist at LBL. To make up for this lacuna, I have patched together many of the LBL memoranda and draft calculations from individual members of the team. These binders, files, and reports continue to reside in the offices of the relevant physicists (e.g. Chinowsky, Goldhaber, Schwitters, etc.)
Recommendation: Insofar as it is possible, try to have a group repository for intra-collaboration and intra-group memoranda. When such a source exists, or if it exists de facto in the hands of one of the group's physicists, a copy of these items are of absolutely central importance to the historian.
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These vary, of course, in importance. In the case of the psi the second most important set of papers is Richter's. Richter preserved a great deal of documentation; he was in charge of SPEAR; and he led the construction of the detector.
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These are of great interest and occupy relatively little space.
Recommendation: PAC records should be preserved and protected at every high-energy physics facility. Because of the importance of PAC's in experiment selection and the mediation between the science conducted at the level of the experiment and broader policy set by agencies of the Federal Government (Atomic Energy Commission, Joint Committee on Atomic Energy, etc.)
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While all the laboratories routinely keep blueprints and other drawings and specifications, detailed exchanges among engineers, technicians, and physicists are not systematically preserved. At LBL, there is a long tradition of writing down everything in "Physics Notes" and "Engineering Notes." These provide an invaluable aid in reconstructing the assembly of equipment, problems in design, maintenance, modification. At SLAC this sort of information is much more difficult to come by, and archival records of expenditures, transfers of hardware, etc. have to be reconstructed piecemeal from group memoranda.
Recommendation: Where the preservation of technical and engineering archives is not as routinized as at LBL, I hope that some alternative methods can be devised to capture these essential records. This might include the acquisition of the "personal papers" of key engineers, preservation of drawings and blueprints from important experiments, etc.
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Despite endless proclamations that the individual laboratory notebook is dead, I (along with others on the AIP Study) keep finding them, and finding them extraordinarily useful. Gerson Goldhaber's and Willie Chinowsky's notebooks, for example, are rich sources for understanding the transfer of track analysis methods from bubble chamber to electronic experiments. Archivists need to search for these in their surveys of documents; I have found practically none of these in the archives themselves.
Recommendation: When the archivists survey historically important experiments, it would be particularly helpful for them to obtain originals (or copies) of "personal" notebooks because these tend to be discarded, or simply made less accessible when team members move away from the accelerator site.
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The history of SPEAR is written to a certain degree in the history of its many doomed proposals to the AEC. Many of these are available, though often in scattered locations.
Recommendation: A copy of each major proposal and its drafts, from the laboratory to AEC, DOE and NSF for research facilities, should be preserved to facilitate the work of future historians.
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Principal sources for the history of SPEAR are the Richter files at SLAC, and the Group C records. Director's papers and some engineering drawings are also helpful, though as with the case of Mark I, fewer engineering records seem to exist at SLAC than at LBL. As Paris's study indicates additional crucial sources come from outside the laboratory, including CEA, government hearings, AEC archives.
Recommendation: It would be helpful to coordinate efforts, for example, by sharing information on archival holdings, appraisal guidelines, and the like with some laboratories abroad, particularly Frascati and Novosibirsk.
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There are three sets of logbooks: one for SPEAR, one for the Mark I detector, and one for the main SLAC beam. While the famous book that includes the actual "discovery moment" of the psi has been meticulously preserved at the Smithsonian, the rest of the series is not complete. The logbooks for the main SLAC beam seem to be complete; it would be enormously helpful if the SPEAR and detector logbooks could be reconstructed and centralized.
Recommendation: I would like to see all major accelerator and major facility logbooks centralized and preserved. In addition, the laboratory should require that logbooks for all experiments be kept centralized until completion of the experiment. Then, if the experiment is of manifest historical significance, the logbook could be secured for the laboratory to preserve. (Examples: W and Z discovery, J, psi, neutral currents). There will be experiments where the significance is not known until much later, but typically in high-energy physics the importance has been clear more or less at once.
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Summary written or diagrammatic descriptions of important software should be preserved—not necessarily the software itself. Documentation on analysis programs is particularly useful, especially verbal descriptions and flow diagrams. These sorts of diagrams have assisted me in tracking continuities between the Berkeley bubble chamber work and their integration into electronic efforts at SPEAR.
Recommendation: It is hard to imagine any historian making use of massive stacks of punchcards, paper or magnetic tape, or bubble or spark chamber film. Historically significant experiments, however, could preserve samples of such output along with particularly important runs (golden events etc.).
Microfiche Records of Images of the Computer Screen
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At Berkeley, Goldhaber, Kadyk, Chinowsky, et al. have (thus far) preserved microfiche images of the electronic read outs from triggered events on the Mark I. I would like to use these, and they do not occupy terribly much space. I recommend their preservation when they are already available on fiche and of obvious historical significance (as is the case here).
Recommendation: Since in general it seems to me unnecessary to preserve raw (or nearly raw) data, I would not recommend preserving such material more than the time physicists make use of them. This will depend on the type of data, but it rarely exceeds ten years. For historically significant experiments, I would recommend preserving samples.
When possible, it would be very useful for interviews to be conducted as soon after historically significant experiments as possible. These should address archival as well as historical questions.
ON THE UPSILON PROBE (by Frederik Nebeker)
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The probe of the discovery of the upsilon particle dealt with a series of seven experiments conducted at Fermilab in the period from 1970 through 1985: E-70, E-187, E-288, E-494, E-596, E-605, and E-608. The first two experiments were Columbia-Fermilab collaborations. Stony Brook joined for the remaining experiments, and E-605 involved in addition CERN, Saclay, KEK, Kyoto University, and the University of Washington. Two later experiments at Fermilab, E-772 and E-789, which may be viewed as continuations of the collaboration (though they are not closely tied to the earlier experiments), are not included in our study.
We wanted this probe to be directed toward work at Fermilab and to illustrate some of the trends in experimental work in high-energy physics in the past decades, such as the greater number of participants, international collaboration, and extended duration. The upsilon experiments satisfy these desiderata as well as being extremely important in their findings (including the discovery of the bottom quark).
We gathered material on these experiments and compiled a fairly complete list of the approximately 130 people—physicists, engineers, and technicians—who took part. We located almost all of them, conducted 57 tape-recorded interviews, and talked or corresponded with another 25 people. The summary that follows was based on these interviews and correspondence, on records in the possession of the experimenters or their institutions (notably Fermilab), and on published materials about the experiments.
THE UPSILON EXPERIMENTS
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A narrative of the course of the experiments, from E-70 through E-605, has been written and is being revised for publication. Some general conclusions about the experiments follow.
Leon Lederman appears to have been a very strong leader, though very informal and not at all authoritarian. The style of the collaboration was described by one participant as "all-talk-at-once democracy." Decisions were reached almost always by consensus and usually at collaboration meetings. These meetings were, by all accounts, productive sessions, though a good deal of discussion was carried out by means of memos (and this discussion was characterized by one participant as "memo warfare").
It was Lederman's assiduous work on and detailed understanding of almost all aspects of the experiments, together with a physics insight that by all accounts was extraordinarily good, that made him an effective leader. Even when he was able to give little time to the collaboration—Lederman was a professor at Columbia and director of Nevis Laboratory during most of E-70/288, and director of Fermilab during E-605—he continued to take part in collaboration meetings and to exert influence over the direction of the effort. Colleagues have commented on his practice of asking penetrating questions that would set people to work thinking and calculating and on his ability to make his collaborators feel that they were working on the most important experiment in the world. Also extremely valuable to the collaboration were Lederman's personal connections with physicists worldwide. The high regard in which Lederman was held by director Robert R. Wilson and other physicists in the Fermilab administration helped in the running of these experiments, as in the ready approval of E-494 and in the willingness on the part of the accelerator staff to provide beam at various energies for E-288.
These experiments illustrate the dangers of caution and of boldness in announcing experimental findings. In the late 1960s Lederman called attention to the "shoulder" in the graph of the masses of virtual photons created in the hadron collisions of the Brookhaven experiment, but he did not claim it as a resonance or particle. "Leon's shoulder" turned out to be the long-lived particle now called the J/psi, and the experimenters of E-70 might well have been the first to see the particle clearly had they moved quickly to Phase 2 of the experiment. Having missed out there, Lederman's group was probably less cautious than they would otherwise have been in announcing the detection of a resonance at 6 GeV in January 1976. This signal turned out to be a statistical fluctuation, now referred to as the "Oops Leon." When, a year and a half later, this group found an apparent resonance at 9.5 GeV, they amassed abundant data before announcing the result.
E-605 exemplifies the tendency for experiments in high-energy physics to be increasingly international. It exemplifies too some of the principal motives for this tendency: a need for more collaborators and more financial support, a need for particular expertise, and a desire to foster experimental high-energy physics in countries without a long tradition of such research. Though international collaboration can introduce difficulties because of the geographic spread of the experimenters and because of differing practices, in the case of E-605 such difficulties were relatively minor. Meticulous planning insured that components built in different institutions fitted together at Fermilab—for example, care was taken lest the use of two systems of measure, metric and English, cause incompatibilities—and much of the work, including most of the data-analysis, took place at Fermilab. It appears that Europeans fit easily into the American setting—apart from their annoyance at certain laboratory practices—but that most of the Japanese remained rather aloof from the rest of the collaboration. A legacy of the upsilon experiments is new ties between the high-energy-physics community in the U.S.A. and those in England, Finland, France, Japan, Mexico, and Switzerland.
In the upsilon experiments lepton and hadron physics were pursued concurrently in two periods: during E-494 when E-288 was also running, and in E-605. During both periods it was, for the most part, the Stony Brook physicists who were primarily interested in hadron physics, and the others in lepton physics. This led to some conflicts, because resources had to be divided between two endeavors and because changes made to improve lepton detection often degraded hadron detection and vice versa. For example, in E-605 those interested in muon physics needed high intensity, which gave too much background unless additional shielding was put in the beam path. When this was done, however, only muon physics was possible, and as a result the Cerenkov chamber, useful only in distinguishing hadrons, was switched off in the last run.
Experiments are important in the training of physicists, both at the predoctoral and postdoctoral levels. Participation in an experiment usually involves work in detector design, detector construction, data-taking, software design and debugging, and data-analysis. Many of the skills needed by experimental physicists are not taught in courses, so on-the-job training is the norm. By being a postdoc on an experiment, a physicist adds to his experience in the areas mentioned above and acquires management skills. Predoctoral students gain experience and the material for a Ph.D. dissertation. From the upsilon experiments came 18 doctoral dissertations (and these dissertations provide the best documentation of many aspects of the experiments). On the other side of the ledger, the lengthened course of an experiment has made it more difficult for a graduate student or a postdoc (who has, in many cases, only a two- or three-year fellowship) to take part in all the phases of an experiment. E-605, for example, was approved in 1979, data-taking ended in 1985, and data-analysis continued into 1990. The lengthened interval between the approval of a proposal and the beginning of data-taking causes a problem for those graduate students who join an experiment near the beginning. It has therefore become more common for dissertations to deal with instrumentation. Two of the dissertations from the upsilon experiments, those by George Coutrakon and Anna Peisert, deal mainly with instrumentation.
Most experiments are quite dependent upon the labor of graduate students and postdocs. It appears that E-605, particularly in the later years of the experiment, was understaffed in postdocs. Graduate students then had a greater burden of data-analysis and took longer to complete their degrees. (Indeed, there are a couple of data-sets from E-605 which have not yet been analyzed and may never be analyzed.) One way the collaboration repays its junior members for their contribution is by giving them exposure in the community of high-energy physicists. With all of the upsilon experiments, junior members often made the first presentations of results at Fermilab (though not at international conferences) and it was the practice to make a junior person first author of a publication. This was the case for all publications not only the journal articles based on thesis work.
One of the achievements of E-605 was the demonstration that one could use very high- intensity proton beams and still get quality data. The experiment obtained good resolution of three upsilon peaks—upsilon and two excited states, upsilon prime and upsilon double prime—although not as good as originally expected. Measurements of hadron production at high pt (that is, creation of hadrons having a large component of momentum perpendicular to the beamline) and of A dependence (that is, the dependence of particle creation on the atomic number of the target atoms) were quite valuable. E-605 was exceptional in the amount of innovation in detector technology. Besides the Cerenkov counter, the lead-scintillator calorimeter, and the 14.4-meter analysis magnet, there were important innovations in trigger and read-out electronics.
The collaboration continued in E-772 and then in E-789. Both of these experiments made use of the E-605 detector with some modifications. But E-772 was not closely tied to E-605—it was a precision-measurement experiment, rather than a search experiment, and there were large changes in personnel and institutions—and E-772 and its successor E-789 are not included in this study.
The collaboration grew steadily from the proposal for E-70 to the data-taking for E-605, from half a dozen to four dozen physicists. One result of this growth was that procedures within the collaboration became more formalized (such as the greater use of memos for the communication within the collaboration, and the specification of agendas for collaboration meetings). There were two periods when the collaboration published few physics results: 1970 to 1975 and 1980 to 1985. In each of these periods the collaboration was assembling a new detector and the laboratory was building a new accelerator. It was only the subsidiary experiments 187, 596, and 608 that fit at all the conventional picture of an experiment, with a short period of data-taking followed quickly by a publication. E-605 was exceptional in the number of papers that concerned instrumentation and in the length of time taken in analyzing the data.
The collaboration produced 43 articles that appeared in major journals, 16 of them in journals of engineering and instrumentation and 27 of them in physics journals. (There were other, less important publications, such as conference proceedings.) There were 18 doctoral dissertations, dozens of technical memos published by the laboratories, blueprints, logbooks, computer tapes containing data, collaboration memos, personal notebooks, computer programs, e-mail messages, and letters. There were in addition other writings by the collaborators that owed something to their participation in the experiments. For example, Bourquin and Gaillard became well acquainted while working on E-70 and continued to work together after their return to Europe. Two papers they published shortly after their involvement in E-70 were certainly influenced by that experiment.
Consideration of the upsilon experiments makes clear that a string of experiments is sometimes a better unit for historical analysis than a single experiment. This is because experiments—even when directed toward different physics-questions—may be very closely related. Different sorts of relatedness are evident in these experiments.
Most important are the continuities in individual and institutional participation, in hardware and software design, in physics questions, and in the setting for the experiments. E-70 began through the efforts of half a dozen physicists at Columbia and Fermilab. Gradually a number of technicians, engineers, and other physicists joined the collaboration, and in 1975 a group from Stony Brook was added, especially for E-494. With E-605 five other institutions— CERN, Saclay, KEK, Kyoto, and the University of Washington—joined the collaboration. No institutions left the collaboration. Of course quite a number of individuals, particularly graduate students and postdocs, but also senior physicists, joined or left the collaboration at different times. There were, in fact, only three physicists who were members of the collaboration from E-70 though E-605: Bruce Brown, Chuck Brown, and Leon Lederman. Nevertheless, there was a high degree of continuity in personnel from one experiment to the next.
The continuity goes beyond institutions and people. There is a continuous evolution of detector design from the single-arm spectrometer of E-70 to the much larger double-arm spectrometer of E-605. There is continuity both in the general design of the detector and in its parts. Such an apparatus is a complex of different hardware components, including magnets, absorbers and shielding, chambers for tracking particles, calorimeters for recording energy deposited by particles, electronic circuitry to transfer data or to trigger the recording of data, and various computer hardware and software. The parts of a detector are often reused, both in detectors later built by the same collaboration and in detectors built by others. For example, the lead-glass blocks acquired for E-70 were used in later experiments in the string and are still being used at Fermilab. The borrowing often goes from one lab to another; the upsilon experiments involved the wire chambers from Brookhaven, the huge magnet from Nevis, both mentioned above, and some amplifiers from James Christenson's group at Rockefeller University. And even when the components are almost entirely rebuilt—as they were in E-605—there may be a great deal of continuity in detector design.
The hardware and the software can define roles that persist even as the individuals change. For example, programming for the online data-acquisition system was in E-70 mainly the responsibility of Irwin Gaines; this task was later undertaken by David Hom, and later still by Dan Kaplan. The triggers, the Cerenkov counters, the hadron calorimeters, and the magnets are parts of the detector that defined roles for the physicists. In addition, there were roles, such as the programming to reconstruct particle paths, which were not defined by the detector but which remained constant from one experiment to the next.
Experiments in high-energy physics often spawn other experiments, sometimes because one result suggests a different search or measurement or because someone realizes that the apparatus built for one purpose can, with little modification, be used for another. Both of these possibilities occurred with the upsilon experiments. As has been discussed, the physics goals of the experiments were closely related. Common themes were the production of virtual photons and the detection of dilepton and dihadron decay products, the search for resonances, the measurement of A-dependence, and the testing of the Drell-Yan model (which is a model of lepton-pair production in hadron-hadron collisions). The means chosen to achieve these goals were also, to some degree, constant, as in the use of a large-aperture analysis magnet or the use of Cerenkov counters for hadron identification.
Except for Lederman's precursor experiment at Brookhaven National Laboratory, all of the experiments took place at Fermilab. This conferred a large measure of continuity, despite the change in the location of the experiment from the proton laboratory to the meson laboratory and the upgrading of the accelerator. Large parts of the detectors were, it is true, built elsewhere, notably at Columbia, Stony Brook, CERN, Saclay, Kyoto, and the University of Washington. However, two of these sites themselves provided continuity from one experiment to the next: engineers and technicians from Columbia's Nevis Laboratory took part in the earlier experiment at Brookhaven as well as in all the upsilon experiments, and technicians at Stony Brook did much of the work on the Cerenkov chambers for both E-494 and E-605.
RECORDS OF THE UPSILON EXPERIMENTS
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An important objective of the probe was to learn what records were created in the course of the experiments, how difficult these records are to locate now, which of them are unique and which are most important, what steps can be taken to insure that an adequate record of the experiments be preserved, and how difficult it is to take these steps. Whenever we talked with a participant, we requested permission to look at his or her records from these experiments. We talked also with archivists at Fermilab, Stony Brook, SLAC, CERN, and elsewhere to discuss these matters. With just a few exceptions, all of the 130 or so participants in the upsilon experiments have some records from these experiments. We inquired about and looked at the records of more than half of these people, including almost all of those who had large roles in the experiments. A rough inventory of existing records has been compiled.
This probe has cast light on what records exist and which are particularly valuable for historians. The experiment proposal is an invaluable supplement to the published accounts of an experiment; very often the objectives and methods of an experiment change between the initial proposal and the experiment's completion; such changes are often not mentioned in the published literature. The contract between collaboration and the laboratory is a prime source of information about the resources required for an experiment and the division of labor on the part of the laboratory and the institutional groups of the collaboration. The experimental logbooks are essential for establishing a detailed chronology of the data-taking phase of an experiment. Of somewhat less value are logbooks on detector components. The internal memos of the collaboration often document the debates antecedent to major decisions taken by the collaboration. Personal notebooks and correspondence can be extremely important. The probe revealed also that much of what goes on within a collaboration does not get recorded, so that interviews may be needed to learn about certain aspects of an experiment.
For the upsilon experiments the most important documents are, first, the intra-collaboration memos and second, the experimental logbooks. The logbooks for these experiments are all located at Fermilab, except for the logbooks for E-494, which are at Stony Brook. No complete set of the intra-collaboration memos for the full series of experiments exists in any one location, but many of the participants have kept significant numbers of memos. Correspondence and other documentation, such as personal notebooks, of many parts of the experiments are likewise scattered geographically. The most important collections are those of Jeff Appel, Bruce Brown, Charles Brown, Yasuo Hemmi, Richard Hubbard, Leon Lederman, Akihiro Maki, Robert McCarthy, John Rutherfoord, Fabio Sauli, the Program Planning Office at Fermilab, and the High Energy Group of the Physics Department at the State University of New York at Stony Brook. Charles Brown, Lederman, McCarthy, and Rutherfoord were all, at one time or another, spokesman for the collaboration and therefore acquired and kept many important documents. Although it may generally be true that group leaders are a good source for documentation, this was not always the case for the upsilon experiments. While not group leaders, Appel and Sauli are exceptional in their carefulness in keeping records of the experiments they participated in and, in fact, have the best set of records for their upsilon groups. The Program Planning Office at Fermilab has experimental proposals and contracts, as well as other papers concerning Fermilab experiments.
We have discussed with Adrienne Kolb, archivist at Fermilab, the disposition of records on the upsilon experiments. Lederman had already donated his papers to the Fermilab archives, and, as a result of the AIP project, Jeff Appel has placed his large collection of papers relating to these experiments in the Fermilab archives.
REPORT ON THE CLEO EXPERIMENT AT CESR (by Joel Genuth)
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The CLEO collaboration was made the object of a probe because it is distinctive in its institutional relations. The accelerator on which the CLEO collaboration runs its experiment, the Cornell Electron Storage Ring (CESR), is the only university-built, university-operated high-energy accelerator remaining in high-energy physics, and it is the only accelerator whose operations are financed by the National Science Foundation (NSF). The largest institutional collaborator in CLEO has always been Cornell University, and the collaboration has always dominated, and now monopolizes, the accelerator's use for particle physics. Whereas university physicists in all the other collaborations in our sample do their experiments at Department of Energy (DOE) accelerators, where they compete for beamtime and other laboratory resources, CLEO collaborators work within an institutional superstructure that has left management of the accelerator laboratory in the hands of a university user.
CLEO's existence poses three historical questions: how and why did Cornell University survive as a site for high-energy physics experimentation; to what ends did the CLEO collaboration use its access to the accelerator; and what significance, if any, has CLEO's existence had on the direction of high-energy physics research? This probe was initiated later than the other two probes of the AIP study, and the time available for examining documentary evidence has been weighted toward the more institutional question as intrinsically interesting in its own right, fundamental to the existence of the other questions, and a better complement to the other probes, which were organized around major discoveries. Even within these boundaries, this study is preliminary and not based on the full range of documents that exist; my hope is to study the documents more fully at a later date. Part VII discusses the sources that exist for the study of the CESR/CLEO collaboration; comments on the utility and possible further use of examined sources appear throughout the essay. I have also benefitted from 24 oral history interviews conducted by myself or Lynn Maloney, but I have not explicitly attributed insights or information obtained through them.
ACCELERATOR CHARACTERISTICS AND EXPERIMENTAL POSSIBILITIES
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In the years following World War II, the physicists at Cornell's Newman Laboratory of Nuclear Science built a series of increasingly more energetic circular electron accelerators. The electron synchrotron that they started operating in November 1967 at 7 GeV reached its design energy of 10 GeV six months later, and in 1971 was upgraded to reach 12 GeV. The solid reputation Cornell had established for building and operating accelerators on the limited financial and human resources of a university was well symbolized, in 1967, in the selection of then Newman Laboratory director Robert Wilson to be the first director of the National Accelerator Laboratory, now Fermilab, to be built in Batavia, Illinois.
Most of Cornell University's high-energy physicists did their experimental research on the Cornell synchrotron, working in groups of three to seven physicists plus graduate students. Rarely did they collaborate with a comparable number of physicists from other institutions. However, a group of University of Rochester physicists began a major string of experiments on the Cornell synchrotron during its second year of operation, and outside users took 20% of the synchrotron's beamtime that year. With the slow-down of the Cambridge Electron Accelerator (CEA) and the shut-down of the Princeton University-University of Pennsylvania Accelerator in 1970, outsider use doubled and Cornell secured funding from NSF for an expansion of the experimental hall's floor area. Harvard also became a prominent institutional user, and unlike Rochester, the Harvard group engaged Cornell groups to do "two-armed" experiments using Harvard- and Cornell-built spectrometers in conjunction.
The Annual Reports of Newman Laboratory, prepared by director Boyce McDaniel for the Cornell administration, document the formation of and shifts in groups and chart the progress of their work. In combination with bibliographic and citation techniques, it ought to be possible to assess these groups' relationships to other high-energy physics research and to form an impression of the degree of recognition that synchrotron users were receiving for their research. Several physicists who became leaders of CLEO performed experiments on the Cornell synchrotron—Edward Thorndike of Rochester, Frank Pipkin of Harvard, and Karl Berkelman, David Cassel, Bernard Gittelman, and Albert Silverman of Cornell—but only Thorndike and Silverman appear even remotely likely to have any personal, unpublished materials related to their early synchrotron experiments. Their contemporary reflections on synchrotron-based research may no longer exist.
The Annual Reports also shed some light into the long-range thinking of McDaniel, who did not keep extensive files. McDaniel delighted in pointing out to the Cornell administration that the travails of the Cambridge and the Princeton-Pennsylvania accelerators brought the Cornell synchrotron additional outside users and "has made Cornell appear more prominent on the horizon of the world of high-energy accelerators." But he later added that the problems of those accelerators also served as a grim reminder of the need "to maintain a unique facility and unique program" against a backdrop of increased competition for the available funds. Accelerators always get deemed obsolete when newer, higher-energy machines come on line and attract the lion's share of experimenters' interests. What had hurt the Cambridge and killed the Princeton-Pennsylvania accelerators—the Atomic Energy Commission's decision to concentrate its resources on building, operating, and improving the higher-energy accelerators at the national laboratories—also loomed over Cornell, albeit indirectly since Cornell had NSF funding. At 18-20 GeV, the linear electron accelerator built at the national laboratory at Stanford (SLAC) delivered considerably higher-energy electrons to experimenters' targets than did the circular Cornell synchrotron; because higher-energy electrons are equivalent to waves with shorter wavelengths, researchers at SLAC were able to probe smaller regions of space than researchers at Cornell.
The documentary record indicates that Cornell's physicists pursued a straightforward course to maintaining their viability as an accelerator laboratory. They made a virtue of the technical differences between circular and linear electron accelerators, and they researched prospects for a future, higher-energy electron synchrotron. The former approach involved designing experiments to match the higher duty-cycle and lower intensity of the synchrotron as compared to the SLAC accelerator. The synchrotron delivered bunches of electrons to a target more frequently than did the linear accelerator, but each bunch was smaller; thus the synchrotron produced more frequent collisions in which less happened than in the linear accelerator. Experimenters at Cornell were consequently better able to discern the final states into which the products of collisions typically decayed, while experimenters at SLAC were better able to search for the signatures for rare processes that occurred in collisions. This qualitative distinction helped to compensate for Cornell's inability to match SLAC in the advantages of experimenting at higher energy.
To reach higher energies, the Newman Laboratory physicists initiated, in academic year 1969-1970, investigations of superconducting microwave cavities that could inject more radio-frequency power into the beam and push back the limit on achievable energies set by the orbiting electrons' emission of radiation. In 1972, they believed they had the materials and designs that would yield cavities "practical for use as the accelerating units in the synchrotron" and anticipated that their development would enable them to boost the current synchrotron's energy to 25 GeV and to design a new synchrotron that could reach at least 40 GeV. Maury Tigner, who had overseen design and construction of the radio-frequency system for the 10 GeV synchrotron, led the work. During academic year 1973-1974, a test cavity made of niobium successfully accelerated electrons, but prospects for mass-producing such cavities remained murky because of the possible effects of mass-production techniques on niobium's superconductivity.
Although no documentary evidence has been found, several Cornell physicists recall intra-Cornell discussions, prior to the winter of 1974-1975, of the possibility of dropping the pursuit of a new synchrotron in favor of using the current one as an injector for a storage ring that would hold and collide electron and positron beams. Such memories seem plausible in light of two other developments in the early 1970s. First, the search for rare processes at SLAC's higher energies yielded data that gave credence to novel theories postulating a sub-structure of quarks within nucleons; Cornell synchrotron users, rather than compete and follow up on SLAC-generated insights, would plausibly have considered trying a different experimental mode. And second, researchers at Fermilab began to make a secondary muon beam, which could be used similarly to an electron beam, in approximately the energy range that Newman Laboratory physicists hoped a new synchrotron would reach. Nevertheless, the discussions of building a collider went nowhere.
The physicists offer a variety of reasons for adherence to a new synchrotron. Some recall believing that there would not be much physics to examine in electron-positron collisions. Some point to the lack of a known technique for using a synchrotron to make a positron beam of competitive intensity. And one physicist feels that laboratory management was not sufficiently secure to take on a technologically daring project because of Wilson's departure and the leaves taken by laboratory leaders to help Wilson with the problems of bringing Fermilab on line. In late October 1974, the Newman Laboratory physicists declared to a NSF review committee that their long-range goal was a larger synchrotron, employing superconducting radio-frequency cavities, and that "we rejected the latter alternative [construction of an electron-positron storage ring] in view of the current leadership which other laboratories enjoy in this field."
The Newman Laboratory physicists stood by that declaration for about three months. In November 1974, physicists detecting the products of electron-positron collisions on the SPEAR colliding beams experiment at SLAC were among the discoverers of a new particle, double-named the J/psi to recognize discovery claims of both Brookhaven and SLAC researchers. This discovery made so many physicists willing to explain subnuclear phenomena in terms of the quark model of hadronic structure that physicists speak of the "November Revolution." However, for the Cornell physicists with ambivalence about their plans for securing their future, the discovery had the additional meaning of eliminating doubts about the quantity of physics a collider could generate provided it operated efficiently at an energy that produced an interesting particle.
Around the same time—the precise chronology cannot be determined without the notebooks of Maury Tigner, who does not know their whereabouts—Tigner reached an elegant solution to the problem of using the synchrotron to inject a sufficiently intense positron beam into a storage ring. Because positrons are created in one out of every thousand or so collisions between electrons and tungsten, achieving a decent rate of collisions in a storage ring depends on intensifying the positron beam by "coalescing" the tiny bunches of positrons that emerge from electron-tungsten collisions. While the proponents of linear electron accelerators readily found a way to handle this problem, the electron synchrotron proponents only came up with complicated, difficult techniques, involving third rings or auxiliary radio-frequency systems, until Tigner spotted the possibility of exploiting geometric relations between the synchrotron and storage ring. The synchrotron and storage ring just had to differ in radius by an appropriate amount relative to the wavelength of their radio frequency systems and the distance between the rotating bunches of positrons. Then physicists could inject tiny bunches of positrons from the synchrotron into the storage ring, return one of the bunches to the synchrotron, orbit that bunch around the synchrotron until it was in phase with one of its formerly neighboring bunches in the storage ring, reinject the bunch into the storage ring, and repeat the process until the several tiny bunches of positrons had coalesced into a large bunch. This simple, elegant plan promised to make the synchrotron competitive with SLAC's linear accelerator as an injector for a storage ring.
In early February, McDaniel informed the NSF of Newman Laboratory's intention to request funds to convert the 12 GeV synchrotron into an injector for an electron-positron collider "for energies exceeding 8 GeV on 8 GeV at a luminosity of 1032 per cm2 per second." The energy of peak luminosity had a double meaning. Not only was it consistent with the parameters of the current synchrotron, it exploited a blind spot in the programs of SLAC and the major European electron accelerator, the Deutsches Electronen Synchrotron (DESY). Those laboratories, prior to the discovery of the J/psi, had committed themselves to proposals for new colliders with peak luminosities around the highest energies they deemed economically achievable, about 16 on 16 GeV, which constituted a four- to five-fold energy increase on their current colliders. The Cornell proposal promised to make possible the efficient exploration of an energy range between SLAC's and DESY's current and proposed colliders.
SCIENCE POLICY AND THE SUPPORT FOR A NEW FACILITY
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Cornell's proposal reached a supportive, energetic NSF Program Officer in Alexander Abashian, to whom many give credit for the proposal's ultimate success. He had managed to climb the academic ladder to tenure at the University of Illinois during the 1960s, when the nation's highest-energy accelerator was at Brookhaven, the newest and most expensive accelerator was at SLAC, and the agitation of midwestern physicists to build a new accelerator had not been successful. Since the NSF program in Elementary Particle Physics consisted entirely of the support of university groups, Abashian's investment of effort into its well-being may indicate that his personal experiences left him inclined to work for improved conditions at universities for high-energy physicists. He certainly used his discretion to push vigorously Cornell's long-term initiatives to maintain a high-energy physics laboratory once Cornell's physicists had united behind a proposal that made use of their extant campus infra-structure. The NSF's working files on the Newman Laboratory proposals and contracts richly document the efforts to build a case for colliding beams experiments at Cornell. However, this material needs to be evaluated more fully than has been possible here in the context of NSF's traditions, relations with other research-sponsoring agencies, and the budgetary conditions of the mid-1970s.
The oral histories, and to a lesser extent the working files, indicate that the NSF staff in Elementary Particle Physics did not especially want to try to sell the agency on supporting a new synchrotron for Cornell. Because Cornell's high-energy physicists had run out of room to expand on campus and would need to prepare an entirely new, off-campus site for a larger synchrotron, such a project was prima facia going to be expensive in money and complex in administration. The staff seemed to doubt that sufficient enthusiasm for a new synchrotron could be generated among physicists outside Cornell to overcome intra-agency resistance to a "big-science" project involving off-campus construction, even one that was overseen by a single university.
The anonymous peer reviews and the site visits the NSF periodically commissioned for the Cornell program between 1970 and 1974 indicated a shift from widespread respect for the synchrotron and worries that it would be properly exploited to widespread respect for how Cornell was using the synchrotron but limited enthusiasm for the physics being produced. In 1970, a panel of four reviewers unanimously applauded the existence of a high duty-cycle electron synchrotron and the advantage it provided over SLAC for certain kinds of experiments. They also all noted the paucity of outside users at Cornell, but split on the significance of that condition. Those who did not object thought there were few, if highly important, experiments that benefitted from the superior duty-cycle of the Cornell synchrotron or they were "old fashioned enough" to like the "anomaly of a flourishing university laboratory." Those who objected believed the accelerator capable of supporting more and better experiments if it were not dominated by a "very tight `in' group" and if more competition for its use was encouraged within the wider community of experimenters.
Newman Laboratory researchers preferred to believe their synchrotron was fecund and its users competitive rather than to believe Newman Laboratory was a pleasing anachronism or a limited facility that was luckily able to support a few experiments of widespread interest. They prepared a proposal for expanding the experimental area and the number of beamlines. Their NSF patrons seemed agreeable but less than fully confident that they had the intra-agency clout to secure the needed funding. They asked the High Energy Physics Advisory Panel (HEPAP)—which was advisory to the Atomic Energy Commission, but potentially influential with the NSF by virtue of the breadth and prestige of its membership—for its opinion of the Cornell synchrotron's importance. Since the Defense Department had terminated its support for some university physics programs and was expected to make additional future cuts, NSF was under pressure to spread its support more widely without a commensurate increase in its budget. The staff in the Elementary Particle Physics Division apparently felt that the case for expanding facilities for experimenters at Cornell's synchrotron needed better evidence of its value to high-energy experimentalists than the Division could readily generate internally.
HEPAP was already hearing how the CEA was coping with a 30% reduction in its operating budget by concentrating on "clashing beam development" and phasing out its fixed-target programs using electron and photon beams. Shortly before the meeting at which HEPAP would consider Cornell's proposal, Marcel Bardon, then NSF's Program Officer in Elementary Particle Physics, met with CEA staff about the possibility of continuing those experiments that used electron and photon beams at Cornell. They "confirm the general impression that a substantial improvement in facilities at Cornell is essential for an effective user program." Bardon followed up that meeting with a visit to McDaniel to negotiate a marginal reallocation of resources within Cornell's grant to improve synchrotron operations at the expense of support for Cornell's own experimental program. The reallocation, Bardon explained to his superiors, "is essential for an efficient transition from the `local University' type of emphasis of the Cornell synchrotron to a mode of operation more appropriate to a facility with broad responsibilities to outside users."
A week later, Bardon presented NSF's budget and program in elementary particle physics to HEPAP, and McDaniel followed with a report on the prospects opened by an expansion and improvement of Cornell's synchrotron facilities. HEPAP's discussions led to a pair of letters from HEPAP chairperson Victor Weisskopf to NSF officials stating that because Cornell's was the last high-duty-cycle electron synchrotron left in the nation, it was "of utmost importance that this facility is available to serve the national community." Cornell received the funds for an expansion and firmly entered HEPAP's consciousness. When HEPAP later wondered whether the time had yet come for broad discussions of possible major projects, Cornell's plans were solicited, and McDaniel took the occasion to tout the energy improvements that superconducting radio-frequency cavities could make for Cornell's synchrotron.
HEPAP's endorsement of a high-duty-cycle electron synchrotron, NSF's willingness to spend in accordance with that endorsement, and Cornell's willingness to support outside users did not, however, all add up to heavy use by outsiders. The Harvard physicists investigating electron scattering at CEA shifted those experiments to Cornell (and also won approval to do an experiment on the muon beam at Fermilab), but no other American groups came in force to Ithaca. In October 1974, Abashian assembled an outside committee to visit Cornell along with NSF staff. The committee found a 90% success rate for proposals to run on the Cornell synchrotron, and it found a "rather limited" user program that "does not appear [to attract] a broad spectrum of physicists from around the country." The committee thought greater outside use would "lead to a better rounded and more viable effort," but failed to come up with suggestions for stimulating outside use. A set of anonymous reviews commissioned earlier in 1974 commented less on the dearth of outside users but criticized a lopsided feature of the experimental program: In their pursuit of the electron-scattering measurements that could not be readily made at SLAC, the researchers at Cornell were producing "safe experiments...with almost guaranteed results," focusing excessively on the final states of electron-production—a program whose track record in 1974 did not match the promise attributed to it in 1970—and failing to create any "innovative," "imaginative," or "daring" experiments. But these reviewers were no more forthcoming on what these experiments should be than the existing committee was on how to build the outside-user program.
None of these criticisms affected NSF's support for Cornell's current research. The ratings for the Cornell synchrotron research program remained "excellent" or "very good" on the grounds that the experiments were largely well suited to the accelerator and competently performed to yield accurate and meaningful results. Indeed, Abashian authorized support for much of Cornell's 1974 request on the strength of having two of four reviews in hand and later petitioned his superiors to use a NSF reserve fund to cover the dramatic increases in Cornell's electric power costs occasioned by the energy crisis. However, the criticisms may have made NSF staff wonder about their chance to preserve a university-based accelerator laboratory on the desirability of a 40 GeV synchrotron. The peer reviewers did not comment at all on the prospects for Cornell's future, while the site committee praised the progress in superconducting radio-frequency cavity research but circumspectly declared: "The long range plans of the Cornell group to build a new electron synchrotron in the 40 to 70 GeV range are in a very preliminary phase.... Physics justification, technical problems, costs, and role in the national perspective need to be understood before a strong case can be made for the facility."
Documentation that would indicate any intra-NSF preferences for Cornell's future plans has not been found, but individuals recall that conversations between Cornell researchers and NSF staff did allow NSF officials to drop broad hints about the viabilities of synchrotron and colliding beam proposals. Cornell's decision to abandon its plans for a new synchrotron and to propose using its current one as an injector for a collider was greeted warmly in the Elementary Particle Physics Division. David Berley, a NSF staff member who participated in the site committee's visit, noted for the files that he believed Cornell's intention to propose to build a collider was "an exciting development which will have a positive and constructive influence on the field of elementary particle physics."
Nobody at Cornell needed to be told that success for their proposal depended on building national support for its acceptance. In officially informing Abashian of Cornell's intention to make a proposal, McDaniel was quick to announce that "the facility will be operated as a nationally available laboratory" and that he anticipated the level of outside use to go from 30% on the current synchrotron program to greater than 50%. Two weeks later, he gave substance to that point by inviting Abashian to a general meeting he called to acquaint physicists with Cornell's plans and to encourage them to participate. The meeting was held March 22, and in its aftermath McDaniel obtained endorsements from 12 physicists to supplement the proposal proper. These endorsements expressed interest in working on an experiment or argued for the value to U.S. high-energy physics of having an electron-positron collider dedicated to the energy range between SLAC's SPEAR and PEP.
Though obviously a step in the right direction, NSF officials could hardly construe the endorsements as symbolizing national support for a Cornell collider. The endorsing physicists included none from south of Philadelphia and only one from west of Rochester, who had recently moved from Harvard to the University of Illinois. Abashian and Bardon sought to recapitulate the Elementary Particle Physics Program's earlier success at expanding the Cornell synchrotron's experimental space by seeking HEPAP's endorsement for use in the intra-NSF battle to come.
However, HEPAP's agenda was qualitatively different in 1975 from what it had been in 1970. Instead of discussing how to cope with contraction of the regional, lower-energy AEC-supported laboratories, HEPAP was considering how to cope with inadequate funds to operate existing accelerators fully while entertaining proposals for considering significant upgrades to the three highest-energy AEC-supported accelerators. Brookhaven wanted to build Isabelle, a proton-proton collider; Fermilab wanted to build the Energy Doubler, a system of superconducting magnets that could be used both to double the energy of Fermilab's beam to 800 GeV and to provide 400 GeV beam at reduced levels of power consumption; and SLAC wished to build PEP, a positron-electron collider to which a proton ring could later be added. HEPAP had already established a Subpanel on New Facilities, which was to meet in Woods Hole in June 1975. When McDaniel presented Cornell's plans to the February HEPAP meeting, he was invited to make a more detailed presentation at the May meeting, where officials of the other laboratories would be presenting their plans and HEPAP would set forth its charge to the Subpanel.
Also weighing on HEPAP in 1975 was a request from the Office of Management and Budget (OMB) for a study on the long-term strategy for construction and operation of high-energy physics facilities. The origins and depth of OMB's interest cannot be gauged from this level of documentation. However, the disbanding of the Atomic Energy Commission in favor of an independent Nuclear Regulatory Commission and an Energy Research and Development Administration (ERDA) could well have inspired OMB staff to seek economies and administrative rationalizations amidst the organizational fluidity. The OMB staff overseeing ERDA, HEPAP attenders realized, also oversaw NSF. The NSF files contain an undated, unaddressed memorandum by Abashian, "Reply to OMB Questions on Fiscal Year 1976 Budget," in which Abashian explained why the experiments on the Cornell synchrotron complemented rather than duplicated the experiments on SLAC's linear accelerator. Thus, OMB staff appears to have been situated and disposed to question the number and type of high-energy physics facilities that the government was funding.
The year before, the 1974 Subpanel on New Facilities had considered what actions might be taken on the PEP and Isabelle proposals in FY 1976. The 1974 Subpanel had postulated four possible funding scenarios for FY 1976, and officially, HEPAP charged the new 1975 Subpanel with simply updating the 1974 report, even though both the Cornell and Fermilab proposals were new. However, it is plausible to hypothesize that the 1975 Subpanel members felt they also had an off-the-record charge to make recommendations that would not fuel OMB's attention to the administration of high-energy physics. Evidence bearing on this hypothesis could be pursued through interviews of Subpanelists and examination of any contemporary records they may have kept. This issue cannot be pursued through any examination of Subpanel records because the Subpanel had no formal records-keeping or reporting requirements to ERDA beyond the final report. Even if Subpanelists had no knowledge of OMB's inquiries, their individual sensibilities could have disposed them to consider the proposals for new facilities in the context of the politics of funding. When McDaniel invited comments from physicists on the value of an electron-positron collider at Cornell, three responded by considering such a collider's relationship to PEP. Two expressed a preference for PEP and a dedication of NSF funds to support PEP users, while Frank Pipkin of Harvard took the opposite tack:
I am quite comfortable with the Cornell Proposal and feel it is a more appropriate step for the U. S. High Energy Physics Community at this time than the PEP proposal. I still have reservations as to how important is the extension of colliding beam measurements to higher energy and prefer to spend $15 to $20 million for 8 GeV rather than $60 to $80 million for 15 GeV.
Pipkin was not a member of the 1975 Subpanel, but one of McDaniel's correspondents who preferred PEP was.
The Subpanel certainly structured its report so as to make a comparison between PEP and CESR necessary and to justify giving PEP higher priority. The Subpanel set forth a single, national strategy for experimental high-energy physics in the United States: "the three-pronged approach to the highest energies via electron-positron colliding beams, proton-proton colliding beams, and multi-TeV protons colliding with fixed target." Since Isabelle and the Energy Doubler were, respectively, the only proposals for proton-proton colliding beams and higher-energy proton beams for fixed targets, the Subpanel could concentrate on judging their feasibility and state of readiness. Only under the most pessimistic of the four funding scenarios, which assumed flat spending at current levels ($210 million per year of FY 1976 dollars), could both not be built, and the Subpanel, rather than choosing, stressed that such a funding level would cost the U.S.A. its leadership in the field. However, PEP and CESR were lumped together as electron-positron colliders, even though their estimated costs differed by a factor of four, they were to be funded by different agencies, and they were maximized to investigate different energies. With CESR being the second highest in energy and PEP judged capable, with structural reconfiguration, of operating at close to peak luminosity in CESR's energy range, the Subpanel deemed "PEP the only acceptable choice as a single national electron-positron colliding beam facility" and recommended its construction under all scenarios.
While the reasonableness of directly comparing PEP and CESR could be disputed, there was no disputing the results of that comparison. However, the Subpanel went on to conclude "we do not consider the construction of a second electron-positron colliding beam facility as one of our highest priorities" and recommended construction of CESR only under the scenario of optimal funding for the field. Under the second most optimistic funding scenario, the Subpanel dropped CESR and recommended immediate construction of PEP, starting construction of Isabelle in FY 1977, continuing intensive research into the Energy Doubler, and maintaining current programs on existing facilities. Under the third scenario, which differed from the second by $45 million (a 15% reduction), the Subpanel held to the second-level recommendations for new facilities and called for cutbacks in extant facilities. This commitment to new facilities under the third scenario called into question the logic of eliminating CESR from the second scenario. If the new facilities were so important to the high-energy physics community as to be paid for, in the third scenario, by considerable sacrifice of extant programs, then one would expect, under the second scenario, for the Subpanel to call for the sacrifice of a smaller fraction of current programs in order to build the Cornell collider and thereby involve more physicists in experiments that were expected both to be fruitful in the short-run and to typify the future. The Subpanel did, after all, "believe that the proposed device [CESR] would produce important physics."
The response of Cornell physicists and their NSF patrons to the report suggests that they found the Subpanel's deliberations not simply misstructured but illegitimate and the conclusions not simply disappointing but reversible. In December 1975, Abashian prepared both a stick and a carrot to use in an intra-NSF campaign to gain funding for CESR. The stick consisted of his reading of Cornell's future and NSF's role and stature should the collider not be funded. Following a site visit in which he reviewed the synchrotron research, Abashian argued that there were no more exploratory experiments to be done on the synchrotron and that its users were occupied with "very difficult experiments of the type which improve quantitative knowledge about phenomena but which are not likely to result in major breakthroughs." With some members of the Cornell staff considering PEP and Fermilab experiments rather than more synchrotron experiments as a hedge against the collider not being funded, Abashian concluded that "a phase-out of the [synchrotron] facility over the next three years should be made." In the absence of a collider, Cornell's physical plant "would go to waste," the world would lose the "last university based [accelerator] laboratory which runs in the small science mode of operation," and NSF would reduce itself to just a supporter of outside users and "would only be able to respond to the field's needs in one fashion." As Abashian portrayed the situation, NSF executives would have to support the collider if they wished to claim to be champions of university science.
The carrot consisted of renewed efforts to build support for a Cornell collider among high-energy physicists. Also in December, Cornell submitted a revised proposal in which the incremental cost was further lessened by calling for the immediate development of only one of the two possible experiment sites and by promising to end the synchrotron research program in order to dedicate all resources to the collider project. Bardon of NSF presented the proposal to HEPAP at the end of its meeting that December, stressing that "this was a substantially different proposal...than had been submitted for the Subpanel [on New Facilities] and it requires the attention of HEPAP." And Abashian sent the proposal out to a panel of 16 reviewers—previous panels had had four reviewers—with pointed instruction on how to judge the proposal:
The review we are requesting is not intended to have the same emphasis and same perspective as that given at the Woods Hole meeting [of the Subpanel on New Facilities]. Considerations which are normally considered to be important in mail peer reviews should be the primary ones in your evaluation. These include physics potential and merit, competence of the investigators to carry out the proposed research, technical soundness of the proposal, evaluation of validity of cost estimates, and relative priority with other grants which the NSF's Elementary Particle Physics program supports. We do not feel that speculative political factors nor the means by which funds are to be obtained should be of primary concern in your evaluation.
HEPAP's response was as logically cloudy as its Subpanel's report. HEPAP's chairman informed NSF, "We discussed the Cornell proposal in the context of a PEP project that is affirmed as a construction project and proceeding as planned. On this basis we consider the Cornell proposal, from the point of view of physics opportunities, a sensible and valuable redirection of their research program." (In what sense, one wonders, would the Cornell proposal be less sensible and valuable if PEP were not affirmed?) According to Berley, who attended the HEPAP meeting as an NSF representative, the sticking point for HEPAP was the political separability of the PEP and Cornell proposals:
Unknown to the committee is how the Cornell project will influence the decision to construct PEP. It is very bad for the field if the Cornell project were to be considered within the Government as a replacement for PEP or were used as a reason to delay PEP.
Assuming that the HEPAP Subpanel shared this sensibility, Abashian's directions to the NSF reviewers replaced the Subpanel's framework, in which CESR loomed as the cut-rate electron-positron collider that would tempt stingy politicians, with his, in which CESR preserved university-based particle physics by exploring an under-emphasized energy domain. The reviews themselves imply that the Subpanel feared that the Cornell proposal, if deemed meritorious alongside of PEP, would threaten PEP's chances of funding. Two reviewers who identified themselves as members of the Subpanel both rated the Cornell proposal as "excellent" when considering it from within the guidelines Abashian had set; one was particularly glad to be free of "the circumstances under which the subpanel recommended that the Cornell facility not be built" because he thought "this machine [the Cornell collider] is promising enough for me to recommend approval of this proposal even if it means sacrificing some part of the on-going High Energy Physics programs."
In 1976, HEPAP did come around to endorsing CESR. In May, HEPAP chairman Sidney Drell wrote a personal endorsement of the Cornell proposal. He noted that "the SLAC proposal for the construction of PEP now seems assured of favorable congressional action" and that the addition of CESR to U.S. facilities in high-energy physics "will insure that the 4-8 GeV energy range won't be ignored, will permit the running of experiments that would take so long as to be prohibitive at PEP ..., and enable the U.S. to run collider experiments in parallel at different energies." In August, he informed NSF that his May letter "now stands as an expression of HEPAP support." The August letter refers to discussions held at HEPAP's meeting of June 29 through July 1, but the minutes for that meeting do not note any discussion of CESR; apparently, the discussions were held in executive session, and any direct evidence concerning the substance of the discussions will have to be pursued through the memories and records of individual members. This endorsement was too late for Abashian to use in an effort to secure construction funds for CESR in FY 1977, but given the level of negative scrutiny Cornell's proposal had received, he was probably better off waiting another year and allowing Cornell physicists to develop additional evidence of the proposal's feasibility and the community's interest. He did successfully press Cornell's case in the planning for FY 1978.
This saga of Washington-centered efforts to secure support for Cornell's future as a high-energy physics laboratory brings out three issues, which merit extended investigation, concerning science policy-making in the early 1970s. First is the effect of institutional fragmentation on the making of science policy. The conflicting desires for centrally rationalized administration of research funds and for pluralism and autonomy among funding agencies with different positions in the Federal government made Cornell's proposal difficult to judge. To what extent did such conflicts exist for other research fields and were they handled differently or better than high-energy physics was handled between NSF and AEC/ERDA? Second is the role of agency culture in the formation of proposals and their handling by program officers. Bardon's and Abashian's conviction that NSF executives were ill disposed toward "big science" construction projects fanned their enthusiasm for Newman Laboratory proposals that could be deemed an addition to its extant infra-structure and reinforced their custom of seeking HEPAP's endorsement. To what extent did other NSF programs and program officers operate under this assumption? Third is the role of political culture in shaping the evaluation of research proposals. The HEPAP Subpanel and several individual physicists appear to have assumed that public officials outside of the research agencies would be unwilling or unable to differentiate between the PEP and CESR proposals, to the detriment of PEP. By the standards of that time, were they wisely and responsibly setting priorities before others set priorities for them or were they allowing uninformed political speculation to influence professional judgement?
FORMATION OF THE CLEO COLLABORATION AND THE DESIGN OF THE DETECTOR
[Table of Contents]
The Newman Laboratory physicists were not in a position to press HEPAP or to judge the timing of sending their proposal up the chain of reviews within the NSF. But once they knew Abashian's intentions to go forward with the proposal, they operated on the assumption that the proposal would succeed. Their ability to make headway on the basis of that assumption generated more evidence that the proposal should succeed. These efforts were two-pronged: developing more detailed designs for the storage ring and organizing a collaboration that would design and commit itself to building a detector.
The former was an administratively straightforward, intra-Cornell task since accelerator construction and operations were going to be Cornell responsibilities if the proposal were approved. The Newman Laboratory staff promptly threw itself into work on storage ring components. When Abashian arrived for a site visit in April 1976, he found that CESR research and development was diverting Cornell's best people from synchrotron research, and he reported to his supervisor, for his "perspective for FY 78 planning by the Foundation," that within a year Cornell would be more than ready to make quick, effective use of construction funds.
Building a collaboration that would build a detector was a more significant and complex affair—significant because it would demonstrate "grass-roots" enthusiasm for CESR and complex because it involved most of the participating physicists in novel technical and social terrain. McDaniel delegated responsibility for that task to Albert Silverman, one of the Cornell professors who had collaborated closely with Frank Pipkin and the Harvard physicists. Since the storage ring's technical feasibility had never been doubted after Tigner's invention of his injection scheme, the problems of designing and building a detector from which interesting physics could be extracted became the more paramount concern.
The obvious social starting point for an experimental collaboration was the major outside users of the Cornell synchrotron, Rochester University and Harvard University. Rochester's physicists were enthusiastic. They were shifting into higher-energy experiments at more distant laboratories and jumped at the news that CESR was still a viable proposal. Edward Thorndike of Rochester promised Silverman that he and Fred Lobkowicz "will drop out of our approved Fermilab experiment once it is clear that the storage rings will go" and estimated that two or three other Rochester faculty would eventually be drawn in. Pipkin at Harvard was more circumspect. When Cornell had first broached its plans in March 1975, he urged the construction of a larger storage ring, which could support more than two experimental areas, and the retention of the fixed-target program:
To an undesirable extent, the storage rings are a one or two experiment facility and the only way physicists can work is to join together in larger than usual groups. Too much can be done with one good piece of apparatus and one does not have the variety as is available with a conventional accelerator.... The initial impact of the more conventional work may not be as exciting, but the eventual payoff may be considerable.
But nine months later, with Cornell truncating rather than expanding its plans, Pipkin pronounced himself and his circle ready to work on a detector for the collider:
There is still much to be done with the present Cornell synchrotron.... This work, however, is not as immediately important as is further work with the colliding beam machines. The colliding beam machines are answering first order questions to which we need to know the answers before we can properly formulate the problem.... The synchrotron experiments will become more important when the major phenomena are known.
That was enough people to start discussions of what a detector should look like, but not enough to make Thorndike feel as though the venture had a base of support that made success likely. "Somehow," he chided Silverman, "more support must be generated. More specifically, additional prospective users must be identified and gotten interested.... If the proposal [for CESR] goes down, lack of outside support will probably be the reason."
Defining relations between Cornell and outside users became one of Silverman's first administrative tasks. While neither he personally nor Cornell institutionally had long experience with this issue, the reputation of SLAC formed a potent backdrop. The SLAC staff included experimental research groups who were reputed to dominate collaborations by dint of their easy access to the experiment site, freedom from teaching and other university duties, and use of SLAC's machine shops and computers. From the start, the non-Cornell collaborators on CLEO worried that Cornell's physicists would function like a SLAC research group. Pipkin made the point explicitly to McDaniel:
It strikes me that the most sensible user arrangement is one in which the groups are composed in part from Cornell people and in part from outside users with sufficient balance in talent and contribution of apparatus that each needs the others in a very real way. One should avoid the SLAC model in which the inside component always has the upper hand. Needless to say any system requires a wise and sympathetic director if it is to work. A Machiavellian director in conjunction with a judiciously selected program committee can easily give the in-house group the cream of the physics.
Pipkin's worries were probably unfounded. Cornell did not have SLAC's budget, and Cornell was not located in a region whose economy inspired the local population to acquire technical skills. Thus even if the Machiavellian will to dominate had been present, the financial and human means were not.
Nevertheless, even the hint of a possible procedural route to Cornell domination was sufficient to alarm Thorndike. At an April 3, 1976 meeting, Silverman had apparently pressed successfully for organizing CLEO's work by allowing individual collaborators to work on any component they chose. Silverman would be left responsible for cajoling people to take on any components that were receiving too little attention. After a couple of days of reflection, Thorndike saw in that plan not a maximization of individual liberty but a threat to systems rationality and his institutional interests. He argued that inadequate attention would be paid to inter-relations among the parts, especially mechanical design questions, and that "user groups [will] have little chance of having areas of responsibility to themselves, a condition necessary for their making a clearly identifiable contribution." He called for organizing the collaboration in "working groups"—one for components outside the magnet, one for components inside the magnet, and one for the magnet itself. Within the groups, physicists from the institutions interested in designing and building particular components could work out, in conjunction with the designers of neighboring components, the components' contribution to the overall detection strategy, their spatial relations, and their software needs. The work of each working group could then be presented for review and ratification by the collaboration as a whole.
Silverman's summary response—"I like the structure you suggest"—was largely contradicted by his elaboration of particulars. He argued that the bulk of technical disputes over the quality of competing component designs could be settled "without much reference to the other pieces of the detector" and thus without any intermediate social structure between the people working on the component and the collaboration as a whole. And to Thorndike's desire to use institutional lines to define responsibilities, Silverman countered by claiming that such policies in California had led to a state of affairs where, in one collaboration between SLAC and the Lawrence Berkeley Laboratory (LBL), "nobody at SLAC is allowed to work on that part of the detector [being built by LBL]. I consider that a lousy scheme—both humanly and technically." As Silverman saw the situation, Thorndike, in his fear that Cornell could become a SLAC, was in danger of recreating the worst of California.
Underneath the emotions aroused by possible institutional invisibility or possible restrictions on individuals' choices of projects lay more enduring sociological issues about structuring the CLEO collaboration. Silverman, who had mostly done experiments with a handful of Cornell and occasionally Harvard colleagues on the Cornell synchrotron, was assuming that CLEO would best operate on the principle that competent, sensible physicists could know each other and the experiment well enough to sense when issues were sufficiently isolatable and technical to be resolved among those working on that piece of apparatus and when issues were so amorphous and strategic as to require collaboration-wide discussion. The geographic separation of the collaborators in several institutions posed obvious problems to the development of this collegiality, but by having individual collaborators choose what they worked on, Silverman could have hoped that the collaborators would have created enough inter-institutional relationships to foster familiarity among groups with no previous connections. By contrast, Thorndike was far less sanguine about building a many-component detector without the imposition of a middle-management structure that respected institutional boundaries. He believed in a CLEO that coordinated the specialized, dedicated efforts of its constituent institutions to build the components. Not only did Silverman's proposal strike him as risking inadequate attention to coordination of parts, it threatened to spread Cornell's efforts too thinly to be effective.
With the CESR proposal arguably depending on the formation of a collaboration to build a detector on the main experiment site, Silverman wisely compromised on his preference for collaboration-wide management and wisely repressed any desire he may have had to view his position as a license to do the collaboration's strategic planning. CLEO became a federal-style institution that vested certain powers in the collaboration as a whole, reserved others for its constituent institutional members, and left the interface to be handled on a case-by-case basis. Thorndike largely got his way for the construction of the detector. As individual institutions joined the collaboration, each concentrated on building a particular component. Silverman appointed a Cornell physicist to track the development of components outside the magnet and inside the magnet (and later appointed Cornell people to track the development of electronics and software). This framework appears to have worked well in that the collaboration was ready to take data when CESR was ready. However, it did alienate one of the middle managers, who came to feel that he had the pleasures of neither genuine administrative authority nor technical creation. The collaboration eventually lost his services.
Silverman held to his preference for collaboration-wide management when it came to data analysis. However, he did so under terms that obviated Pipkin's fears of a Machiavellian administrator guiding the cream of the physics to the inside group. Any member of the collaboration was able in principle to work on any topic using data from any component (though in practice collaborators may have favored topics that used the components on which they had lavished their craftsmanship and built up their expertise). The collaboration as a whole held the right to decide by vote whether a piece of work was suitable for general dissemination. Thus Silverman eliminated any authority the spokesperson may have claimed for deciding who studied what topic by what method; that remains the system today.
With outside groups knowing they could take responsibility for a component and were welcome to frame their analysis interests, it did not take long for Silverman to gather evidence that implied CESR should be a going concern, especially since U.S. high-energy physicists like to risk understaffing collaborations in order to minimize intra-collaboration administrative burdens and to limit the spread of credit for the anticipated successes. In February 1976, Abashian was reporting that 16 physicists from 11 universities had expressed interest in using the CESR and another 25 from eight universities were SPEAR users who appeared interested in Cornell. From that he concluded, "The problem is not one of attracting sufficient scientific interest of a high caliber [to CESR], it is in convincing one of the need for substantial capital investment." In November, McDaniel reported that 15 physicists from Harvard, Rochester, Syracuse University, and Vanderbilt University were willing to spend some of their grants and dedicate some of their graduate students and postdocs to building a CESR detector and that negotiations were ongoing with 13 more from Rutgers University, the University of Massachusetts, Argonne National Laboratory, and Princeton University. He considered that sufficient user demand for CESR to justify developing the second interaction site. While McDaniel was especially hopeful that the Argonne physicists would join because of the ERDA funds and the expertise in superconducting magnets they would bring, once Rutgers made an acceptable offer, no further long-term institutional collaborators were added until the postdocs and graduate students who first worked on the experiment took faculty positions from which they could organize groups.
Ideally, each added group could be studied to determine what attracted it to CESR, while the superficially interested groups could be studied to see why they did not join. However, one outstanding commonality of Syracuse, Vanderbilt, and Rutgers is that they were all NSF-funded groups. The propensity of NSF-supported groups to turn the CESR proposal into a band-wagon may be explained by speculating on worries over CESR's impact on their funding. If NSF support of university groups that used accelerators were to be squeezed by NSF's desire to preserve one university-based accelerator at Cornell, the last groups likely to feel the pinch would be those whose activities were aimed at making the Cornell accelerator a success. ERDA-supported groups would not have that worry as a motivator. Whether or not NSF had to squeeze accelerator users to construct CESR needs to be studied from higher-level agency documents than have been examined so far. However, those who joined what was later named the CLEO collaboration were rewarded when the CESR proposal, in July 1977, passed the scrutiny of the National Science Board and became part of NSF's budget for FY 1978.
The CLEO collaboration thus came together as a coalition of groups with a common willingness to gamble on the construction of CESR rather than with a common interest in particular physical processes or with a common desire to participate in building a novel detector that someone had designed for the accelerator. There is no evidence of anyone having given thought to detector design or institutional collaborators between March 1975, when McDaniel presented Cornell's plans to interested outsiders, and December, when Abashian sent Cornell's proposal out for intra-NSF peer review. With the exception of those Cornell physicists who had collaborated with the Harvard group, none of these people had worked together, and none had recently worked extensively on the design of an electron-positron collision detector. This common level of inexperience of working within a six-institution collaboration and working on a detector for an electron-positron collider meant that no individual or group had a substantial claim to exercise authority and made Silverman's willingness to run CLEO as a democratic federation all the more appropriate. One person did suggest a novel detector design (as discussed below), which, had it been accepted, acceptance could conceivably have propelled him to intellectual leadership within the collaboration, but he gained no followers. To this day, leadership within the collaboration is kept deliberately diffuse and the importance of the non-Cornell collaborators is overtly stressed. Since Silverman stepped down as spokesperson after completion of the initial construction, the experiment's spokesperson has been elected annually by the collaboration at large, including graduate students, and the spokesperson has more often been someone from outside than inside Cornell.
The federal-style division of authority that CLEO adopted insured that any conflicts over how the design of components affected the overall effectiveness of the detector would be subject to compromise solutions. The situation in which the collaboration found itself insured that such conflicts would arise. As the only builders of a magnetic detector in the 8 GeV on 8 GeV energy region, the CLEO collaborators had no short-term worries over competition for the discoveries and measurements CESR would yield. This condition inspired technical conservatism, since any good data would be significant and a full-scale failure would indefinitely deprive the community of information as well as squander the investment in the accelerator. On the other hand, as builders of careers in a field whose members judged each other in part on the quality and innovativeness of the equipment they built, the CLEO collaborators had longer-term interests in showing their mettle as detector builders. This inspired more technical daring, since an accomplished detector would contribute to experimental craft and improve collaborators' prospects for finding their way into future experiments.
As part of its planning for PEP, SLAC had sponsored "summer studies" in 1974 and 1975 to spur discussions of collider detectors and to stimulate the formation of collaborations to propose experiments. The more daring of the summer-study suggestions to be under active development effectively defined the state of the collider-detector art for CLEO. Two features of possible PEP detectors caught the attention of CLEO collaborators: the use of a superconducting solenoid to bend the paths of charged particles as they passed through a tracking chamber, and the determination of energy lost by charged particles as they traveled through gas by measurement of the ionization in the gas. Both of these techniques were prominent in the "Time Projection Chamber" (TPC), which David Nygren of LBL had conceived to combine high-resolution tracking, momentum analysis, and particle identification within a volume comparable to previous drift chambers.
The dimensions of the magnet were the architectural linchpin of the CLEO detector, for they defined how much space there was for inner components and how much surface area outer components would have to cover. Thus determining the character of the magnet became the collaboration's first order of business. As soon as he had heard that Cornell would actively plan a collider detector, Fred Lobkowicz of Rochester urged McDaniel to have Cornell's magnet experts check on developments at Berkeley and "seriously plan building a superconducting coil" if Berkeley's test magnet reached its advertised goal, with Cornell people "looking for skeletons in their closets." Two weeks later, Karl Berkelman of Cornell presented the collaboration with a "Proposal for a General Experimental Magnet" that called for leaving a three-meter gap in a 6.5-meter-long magnet made from conventional coils.
Berkelman's magnet was a departure from conventional SLAC-based wisdom in that the Mark I detector used to discover the psi, its successor (Mark II), and the TPC all used or planned to use solid solenoids, whether conventional or superconducting. His proposal was the lone recommendation to use CESR as a site for experimenting with the geometry of collider detectors and redefining the trade-offs among the measurements they make. His GEM design sacrificed the uniformity of the magnetic field, thus complicating the analysis of tracks, and increased the length of tracking needed to reach an acceptable standard of momentum resolution, thus increasing the surface area that outer detector components would have to cover. In return, 66% of the solid angle contained no material that could interact with the created particles before they reached the outer detector components. In addition to the clear view his magnet would allow the outer components, Berkelman pointed out that it made for easier access to maintain or upgrade the inner components and argued that it left "maximum freedom of choice in detectors for future experiments, some of which we cannot now anticipate."
Silverman called for a January 31 meeting to discuss magnets, making clear to the collaborators that magnet design had to be set "in order that the other parts of the detector can proceed." He hoped that the discussion would lead to a consensus, but apparently none emerged, for Silverman asked for written reactions to the meeting and suggested that collaborators could clarify the issue by trying to draft "something like a proposal submitted to a program committee" using the various magnets. The results of that exercise did resolve one point: "Though there are several groups who are prepared to make such proposals using a superconducting solenoid,...no one is prepared to propose a detector using the `Berkelman magnet.'"
There is evidence of skepticisms about Berkelman's proposal on technical grounds, but it is also easy to imagine more social and strategic forces at work. Berkelman himself freely acknowledged that the larger radius of his magnet increased the cost of covering the outer surface area with detection components; Edward Thorndike declared that condition as much a constraint on the collaboration's freedom of choice as the open geometry was a creator of choices. He called for basing "our comparison and choice [of magnets] on the things we can anticipate." Anticipating that the collaboration would be concerned with detecting neutral particles, Thorndike pointed out that the use of high-quality crystal detectors outside Berkeleman's magnet would be prohibitively expensive and that cruder, less costly liquid-argon neutral detectors would not benefit from the open geometry because they worked by sampling the interactions of neutral particles with material placed in their path and could use magnet coils for that purpose. Thorndike did not consider issues of additional charged particle detection, but Berkelman himself indirectly did when he began to estimate the sort of hadronic events CLEO should be prepared to detect by extrapolating from SPEAR results to CESR energies. He concluded that CLEO should be prepared for "jets" of hadrons, which would have sufficient momenta not to be frequently impeded by magnet coils. That expectation also undercut the virtues of open geometry. Finally, Berkelman's proposal could also be read as a bid for intellectual preeminence within the collaboration on the strength of creating a distinctive strategy for collider-based detection. At that level, its failure would be expected given the inexperience of CLEO collaborators with collider detectors, their security with the value of any good data they could produce, and their worries about not letting CESR turn into a SLAC-like laboratory dominated by Cornell's physicists.
The collaboration's rejection of Berkelman's novel suggestion meant that CLEO would not propel an individual to prominence and leadership, but the willingness of some collaborators to design a detector around a superconducting solenoid did not mean that the collaboration was collectively comfortable with attempting to build state-of-the-art components. A superconducting solenoid had the obvious virtue of generating far more field for power consumed than a conventional magnet, but it would be expensive to build and carried the potential of catastrophic failure should it not prove possible to stop the propagation of heat quickly enough when some part of the solenoid lost its superconductivity. Throughout the first two-thirds of 1976, Silverman, who himself hoped to build a superconducting solenoid, sent physicists to Berkeley and brought Berkeley and other magnet experts to Ithaca in an effort to build collaboration-wide confidence.
While the evidence so far examined does not indicate who resisted and who pushed for the development of the superconducting solenoid, it is clear that the collaboration was unable to make a clean choice and that Silverman arranged a compromise solution. The collaboration eventually followed the spirit, though not the letter, of a recommendation of Maury Tigner, who responded to the first debates over magnets by asking "Why can we not do the physics we need to do in the first two years using copper coils?" By building a conventional solenoid for immediate use and working more slowly toward a superconducting one, the collaboration could draw on Tigner's crew's expertise in superconductivity (acquired from its work on superconducting radio-frequency cavities) once it had completed the bulk of CESR's design and construction. Furthermore, Tigner argued, a less pressed superconducting solenoid program could benefit from the industrial development of cryogenic systems, which Tigner expected private firms to produce in response to the demands created by LBL and the Fermilab Energy Doubler project. Silverman did not seek to stop collaborators from researching superconducting solenoids while waiting for Tigner to finish building CESR—he had made plain his distaste for administrative measures that blocked experimenters from topics that fired their enthusiasm—but the wisdom of not depending on a superconducting solenoid for initial data-taking did take root. In September 1976, Silverman called on the collaboration to "fix on a particular detector so we can begin such a design" for a complete system on the assumption that the components would fit inside or outside and be used in conjunction with a conventional solenoid three meters long and one meter in radius. This solenoid would be interchangeable with a superconducting version that Silverman expected would not be ready by the October 1979 target date for CESR's start. The superconducting solenoid did eventually prove technically and fiscally feasible, and the collaboration substituted it for the conventional magnet in the summer of 1981.
A similar preference for compromise characterized decisions over the particle-identification components that were placed immediately outside the magnet. Early in 1976, Harvard physicists began developing Cerenkov counters, an established technique for determining the velocity of a particle by the light it emitted if its speed in the medium of the counter were faster than the speed of light in that medium. But when Peter Stein of Cornell visited Berkeley and acquainted himself with the TPC, he returned enthused over particle detection through the use of dE/dX, the determination of energy lost by charged particles as they travel through gas by measurement of the ionization in the gas. A small knot of Cornell physicists began experimenting with the technique independently of the drift chamber to go inside the solenoid (unlike the TPC, which more ambitiously incorporated dE/dX instrumentation in the drift chamber). Their enthusiasm found a less burdened institutional home when they interested physicists from Vanderbilt in trying to build actual chambers.
The TPC proponents ultimately claimed in their proposal to SLAC that dE/dX measurements would be useful in identifying particles whose velocities were too low to trigger Cerenkov radiation, and that dE/dX instrumentation could be segmented far more finely than Cerenkov counters in order to improve the ability to cope with multiple particles that simultaneously passed through the chambers in close spatial proximity. However, to achieve the desired resolution, dE/dX chambers had to sample the ionization several hundred times in order to average out fluctuations in a particle's loss of energy through thin layers of matter. To obtain several hundred ionization samples in a manageable volume of gas, TPC's proponents proposed to pressurize the chamber to 10 atmospheres. That made the construction of the chambers a tricky business requiring a considerable research and development effort; one Harvard physicist recalled thinking of the dE/dX chambers being developed by the Cornell-Vanderbilt alliance as "a bomb...[with] all these little laminates of aluminum all stacked together and then pressurized at a fairly good pressure." Again the collaborators faced an issue of whether an unestablished experimental technique which promised better data was worth the risk given the lack of competition in their energy range. Again the collaboration split and Silverman worked out a compromise rather than handed down a decision. With the region immediately outside the magnet divided into octants, the collaboration set aside two for dE/dX chambers and dedicated the rest to Cerenkov counters. At times, Silverman had to reassure Vanderbilt's physicists of the collaboration's commitment to dE/dX detection, and the problems encountered in its development prompted socially difficult assessments. However, the interested physicists persevered, and in January 1979 an NSF staff member on a site visit to Cornell found, "Even people who have been skeptical about the ability of Vanderbilt, or anyone, to construct the dE/dX system now feel that substantial progress has finally been made." Still, the collaboration would not commit to commissioning six more dE/dX chambers to replace the Cerenkov counters until more experience had been acquired in working with the two extant ones.
In the absence of a spokesperson who wanted and to whom his collaborators had ceded the right to make executive decisions over the research and development directions the collaboration should pursue, the detector's overall design either reflected a widespread consensus over what a collider detector had to do or negotiated compromises among physicists with independent institutional bases. In April 1978, when Silverman commissioned Pipkin, Berkelman, and Tigner to review and assess the collaboration's progress and morale, he learned that the primary complaint collaborators had about himself was "you did not aggressively force important questions to the attention of the group so that they would be discussed and resolved." For obvious reasons, Pipkin et. al. did not name Silverman's critics, but one expects and hopes they were more junior and newer to the collaboration; the more senior, longstanding members had been instrumental in creating a collaboration in which nobody had a firm social foundation for aggressively forceful behavior, and it would have been hypocritical of them to complain about that condition in 1978. It would seem that newer, younger collaborators needed time to grow accustomed to the "Cornell style." If that phrase has any substantial rather than rhetorical meaning, it ought to be that mounting experiments at Cornell put less pressure on faculty and students to cultivate specialized niches and more pressure for them to understand the interfaces between accelerator and detector and among detector components. For better or worse, the ends and means of the CLEO experiment would not be defined and revised through ratification of or rebellion against the views of a leader(s) whose specialty was to fit the experiment into the framework of current detection technique and physical theory. Instead ends and means would depend on the shared sensibilities of and the compromises between the more active physicists.
CLEO AND THE COURSE OF ELEMENTARY PARTICLE PHYSICS
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In May 1977, Abashian included Boris Kayser, a theoretical physicist who administered NSF's theory program, on a site visit to Cornell. After hearing Berkelman discuss the physics areas in which CLEO could make measurements—these included hadronic matter, quantum electrodynamics, leptonic matter, 2-gamma physics, and unexpected physics—Kayser came away feeling that the experimentalists were taking account of the work of the local theorists, and he particularly approved of the ferment within the CLEO collaboration over particle identification techniques: "This is very important because if new physical phenomena are discovered, the exploration of the nature of these new phenomena will depend on being able to tell what kinds of particles they produce." In March 1979, Norman Gelfand of the NSF sat in on a meeting of the CESR Physics Advisory Committee. He reported that the committee "expressed dismay" at the number of different particle-identification systems being built. He himself found the collaboration's plans for experiments so ill defined that he recommended that NSF insist that "opportunities are clearly made available for groups [not in the collaboration] to use CLEO [the detector]. This will include the opportunity to modify or augment the detector as well as information on how to use existing detectors and to analyze CLEO data."
What had changed were not the collaboration's plans but the context for judging them. In June 1977, Leon Lederman announced that the collaboration he was leading in a Fermilab experiment had discovered a new particle of mass 9.5 GeV. He and his colleagues dubbed the particle the upsilon and interpreted it as the bound state of a previously undiscovered quark and its anti-quark, dubbed the bottom quark. By September they had tripled the size of their data set and discerned that the upsilon was a family of resonances with a ground state at 9.4 GeV and excited states at 10.0 and 10.4 GeV.
CESR was obviously going to be the best producer of upsilons. Unlike PEP and PETRA, CESR's high-efficiency energy-range covered the upsilon resonances, and unlike Fermilab, CESR would produce upsilons without the copious backgrounds that arise from collisions involving protons. Thus the CLEO collaboration was positioned to collect an abundance of data on the behavior and properties of the new particle. However, the collaborators had not reassessed their detector designs in light of the new development. By early 1979, approaching two years since the discovery of the upsilon, physicists from outside the collaboration were not pleased to find the collaboration weighing the safety of the Cerenkov counters against the potential performance of the dE/dX chambers instead of debating the best course for elucidating the bottom quark's nuances.
The collaboration's failure to incorporate the upsilon's existence into their plans can be explained in two ways: first, detector plans were too far advanced for revision without sacrificing the timetable for readiness; or second, power within the collaboration was too widely spread for anybody to impress on his collaborators the discipline and obligations upsilon-detection placed on the collaboration. Some collaborators retrospectively opted for the latter explanation; they chided themselves and their colleagues with a collective slowness to appreciate the upsilon's significance for their plans for the detector. This explanation does not require that CLEO collaborators be wiser than was possible, because the intellectual wherewithal for anticipating the problems of studying a new quark certainly existed. The proposers of the Time Projection Chamber, in December 1976, succinctly set forth the relevant considerations:
The new quarks, if they exist, should lead to more new vector meson states above SPEAR energies.... if such states are within the PEP energy scale, their decay chains should provide a fascinating and experimentally challenging maze of kaleidoscopic richness. The ability to track quantum numbers within the set of final long-lived particles is an extremely important asset for this endeavor, as is 4 steradian sensitivity for charged and neutral particles....
New objects are best seen near threshold where the production cross section is usually largest. At PEP energies, conventional hadronic processes, even those involving charm, should be rather jet-like. However, just above a new two-body threshold, the new physics will be rather isotropic and not jet-like at all. Those events displaying high sphericity will be the place to look for new hadrons. Thus the premium is on full solid angle coverage with particle identification over most of 4 steradian.
To capture the decays of a new particle that would emerge with low momentum and decay close to the collision point, the TPC proposers used the ionization of gas molecules within the solenoid for the double purpose of identifying the particles and determining a third dimension of tracking. Another California-centered collaboration, Mark III, which formed in 1977 to continue studies of charm- and down-meson resonances at SPEAR, handled the isotropic physics of these states by squeezing all their more conventional detection apparatus, except the muon detectors, inside a larger-radius magnet. In both cases, these collaborations more than met the desiderata of Karl Berkelman's open-geometry magnet: over a large solid angle, charged particles encountered identification apparatus before any other material with which they were prone to react.
While it clearly would have been possible for CLEO collaborators, in the latter half of 1977, to anticipate the problems of upsilon detection, it is not clear that doing so would have been anything more than a frustration-producing paper exercise. By September 1976, the collaboration had determined to use a magnet with a one-meter radius and to place particle identification components outside the magnet. In April 1977, Silverman was distributing detailed plans for the muon detection system, whose design, as the outermost component, would affect access to the particle identification components. For CLEO to have pursued, in the fall of 1977, either TPC's or Mark III's solution to the study of vector meson decays would have required the sacrifice of substantial amounts of work and the development of new forms of expertise. Furthermore, it was not entirely clear that the CLEO detector, once its superconducting solenoid was ready, would be inefficient at detecting upsilon decays. The superconducting solenoid was thinner than a warm solenoid, giving reason to hope that it would not interact with annoying frequency with the low-momentum products of meson decays. Silverman did not initiate a formal internal review of the collaboration's activities until the summer of 1978, and its purpose was to determine the status of the programs for building the planned components and to recommend a course for obtaining the best possible functioning detector for the planned start of CESR in October 1979. There was no point for the reviewers to consider how the detector should have been designed in light of subsequent discoveries.
When CESR and CLEO both began operating on schedule in October 1979, the CLEO collaborators indeed found that charged particles frequently interacted with the magnet coils before they reached the dE/dX chambers or the Cerenkov counters, and the situation did not greatly improve when the superconducting solenoid replaced the conventional. That may have been a source of regret, embarrassment, or hard-won enlightenment for individual members, but not of suffering. The collaboration had no competition from magnetic detectors in this energy range, and enough particles got through the magnet to yield meaningful data about the properties of resonances that had never been so cleanly and copiously produced. From the data collected on its initial survey of the energy terrain, the collaboration was able to produce a holiday card, "Seasons Greetings from CESR," with a mass plot showing the three known upsilon resonances. More substantially, that spring the collaboration felt ready to go public with evidence giving the first confirmation of the third upsilon resonance; that summer, the collaboration announced the discovery of a fourth resonance. One of CESR's initial detractors, who in 1975 had feared that the cost of CESR's construction would force NSF into supporting too few physicists who would be focussed on too narrow an energy regime, graciously congratulated McDaniel:
It is a great pleasure to send you my congratulations on the highly successful program of experiments in the early phase of the operation at CESR. As Al [Silverman] may tell you, I had some reservations originally about the choice of energy for the machine and about its having only two interaction regions. I'm very glad that Nature has vindicated your choice by her selection of the upsilon masses, and that both interaction regions are turning out high-quality data.
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Out of the politics, technological innovation, and strategic positioning that went into creating CESR has emerged an enduring institution. The CLEO collaboration, much augmented but with the loss only of Rutgers from its original institutions, continues to take data. The intricacies of upsilon decays have not inspired reconsiderations of the theoretical precepts of high-energy physics, but they have yielded the experimentally challenging spectroscopy of kaleidoscopic richness that the TPC proposers hoped to be studying at PEP. The collaboration's federal structure, in which the powers held by the collaboration as a whole are managed on a democratic, egalitarian basis, have created a congenial environment for postdocs and graduate students, who have sought to maintain their affiliation with CLEO when they took permanent positions. This combination of fertile data and retention of ambitious younger physicists, plus the rise of a competing collaboration on an accelerator at DESY, have fueled a reconstruction of the detector to maximize its utility for studies of the bottom quark. Among other changes, the drift chamber was rebuilt with the capacity for dE/dX measurements, like the TPC, and the space immediately outside the magnet, where the dE/dX chambers used to be, is now filled with cesium iodide crystals for detecting neutral particles. These improvements and additions to CLEO, in combination with a string of bad luck at SLAC, have attracted the interest of groups that had primarily been SLAC users.
Data are the currency of experimental high-energy physics, and convenient access to the control of interesting data a greatly desired commodity. Convenience is easily defined in geographic terms, and control in terms of administrative relationships, but interesting data are the product of taste and luck, which cannot be well defined in advance. The history of the CLEO collaboration reveals a healthy interaction between predictable and uncertain factors in the practice of high-energy physics in the United States in the 1970s and 1980s. As physicists politicked and competed in their efforts to keep their work as convenient as possible, they ended up hedging the community's bets on where the interesting data would be found. To have any chance of retaining the convenience of their own accelerator, Cornell physicists knew not to design CESR so that more physicists could take data at the energies covered by the existing or planned colliders but to design it for an intermediate energy that was not easily reached, if at all, by the other accelerators. As collaborators maneuvered to insure themselves a satisfying stake in the production and control of the data, they created a social structure that could renew itself by holding the loyalties of its younger members. Then when CESR's data turned out to be interesting in ways that had not been initially predictable, the collaboration was able to rebuild the detector on the basis of its experience. Both of these interactions were predicated on a political economy that could provide high-energy physicists with choices over the best accelerator for them to use. In the absence of any potential to fund CESR along with PEP, as well as Isabelle at Brookhaven and the Energy Doubler at Fermilab, there would never have been an application to build an 8 GeV on 8 GeV electron-positron collider. In the absence of Cornell's need to please prospective collaborators who could "vote with their feet" on the conditions they faced at various accelerator laboratories, CLEO would not have had its self-renewing federal structure.
RECORDS PERTAINING TO THE ORIGINS OF THE CORNELL ELECTRON STORAGE RING
AND THE CLEO EXPERIMENT
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National Science Foundation
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1. Directorate of Mathematical and Physical Sciences. This Directorate has kept its files on contracts and proposals from Cornell University's Newman Laboratory of Nuclear Science since at least the late 1960s. The current Program Officer in Elementary Particle Physics, Dr. David Berley, has control of the files and is committed to their safekeeping.
These files contain reports of site visits made to the Newman Laboratory by NSF staff, reports of site visits by NSF-commissioned panels of outsiders, written materials prepared for these reviews by Newman Laboratory staff, peer review reports solicited by mail for proposals made by Cornell, correspondence between the Laboratory Director and the NSF Program Officers, letters from high-energy physicists to Foundation officials expressing opinions on Cornell's proposals and programs, and "Diary Notes" of NSF staff concerning developments affecting the Cornell contract. For the period before the winter of 1974-1975, which was when Cornell submitted its first proposal to convert its synchrotron into an injector for an electron-positron collider that would operate at energies in between SLAC's SPEAR collider and SLAC's proposed PEP collider, these files provide valuable, unique materials on how physicists from outside Cornell viewed the research being done at the Cornell synchrotron and how Cornell physicists, before the discovery of the J/psi particle, planned to preserve Cornell as a site for a high-energy physics laboratory. For the period after the winter of 1974-1975, these files are rich in materials related to the problems in building a case for funding the proposed collider and an accompanying detector. Of particular importance are letters from high-energy physicists to Foundation officials expressing opinions on the value of a Cornell, NSF-supported facility in light of the SLAC proposal to build PEP with the support of the Energy Research and Development Administration (now Department of Energy.) These records also contain materials shedding light on the progress of construction of the collider and the development of plans for a magnetic, solenoid detector for the primary interaction region.
2. Historian's Office. The Historian's Office keeps records related to the deliberations of the National Science Board, the other agency-wide administrative offices, and the overall agency budget. These are important to CESR/CLEO history because the construction of the storage ring system and the detector components built by NSF-supported university groups were funded without special Congressional authorization but through the NSF's intra-agency allocation to its Program in Elementary Particle Physics. The intra-agency impact of the Cornell project are best studied through these records.
Department of Energy
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The NSF officials in the Mathematical and Physical Science Directorates deemed the initial Cornell proposal a sufficiently significant addition to the national effort in high-energy physics to warrant review by the Energy Research and Development Administration's (now Department of Energy) High Energy Physics Advisory Panel (HEPAP). HEPAP has been legally required to meet openly and keep minutes. The Department's Division of High Energy Physics has kept files of correspondence between HEPAP and the Department (and its predecessors), and the Division has a nearly complete set of HEPAP minutes at its Germantown, Maryland offices (missing are minutes for HEPAP's 38th meeting, September 8-9, 1974, and for all meetings from 1982 through 1984). A copy of the Division's set of minutes, which lacks minutes for a few meetings, is now in the possession of the Center for History of Physics at the American Institute of Physics. The Public Affairs Room at the Department's headquarters in Washington has copies of HEPAP minutes from 1978 to the present. The minutes recount who reported on which subjects at which meetings with modest amounts of detail on the contents of the reports and the discussions they provoked.
Much of HEPAP's work is carried out by subpanels, which are not required to keep records of their meetings. The Subpanel on New Facilities reviewed Cornell's proposal to build an electron-positron collider, along with Brookhaven's proposal to build a proton collider, Fermilab's proposal for an Energy Doubler system of superconducting magnets, and SLAC's proposal to build PEP, a higher-energy electron-positron collider. No official records of this or other subpanels exist beyond their final reports. This situation is especially unfortunate for this subpanel because the low priority it gave to the Cornell proposal forced the Cornell physicists to scale back their proposal for consideration within the framework of the NSF's internal budget decisions.
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1. Office of the Director, Newman Laboratory. The occupants of the Office of the Director of Newman Laboratory of Nuclear Science from 1968 to the present, Boyce McDaniel and Karl Berkelman, have created office files that include the annual reports to the university president, annual reports to the NSF, copies of grant proposals, and the requisite, routine administrative correspondence. The first of these, which are not to be found away from Cornell, is useful for following Cornell's efforts to upgrade and expand the laboratory's electron synchrotron and attendant facilities and for charting the evolution of internal research groupings in the Cornell department. However, the directors have not been producers or collectors of documents concerning intra-Cornell discussions of present activities or future plans for either accelerators or experiments thereon. The NSF files, with their reports from outside visitors to Cornell, are a better source for clues to intra-Cornell thinking.
2. Wilson Laboratory Conference Room. In October, 1976, the CLEO collaboration set up a system of internal memoranda, dubbed "CBX Notes." 23 documents from 1975 and earlier in 1976 were included at the inauguration of the system. It is still active. One set is in the conference room; Nahmin Horwitz of Syracuse University, the collaboration's principal secretary, also has a set; Giancarlo Moneti of Syracuse also has a set.
The CBX Notes are by far the single most important set of documents for tracing the intellectual and technical history of the CLEO experiment. In principle, anything a collaboration member wishes the collaboration as a whole to consider or be aware of is written up as a CBX Note. Suggestions for overall detector designs, for specific component designs, for software and data-formatting designs, and tentative, initial results of analyses all become CBX Notes. Since 1977, minutes of the monthly collaboration meetings were classified as CBX Notes and included in the collection. (Horwitz has a set of minutes kept independently of his collection of memoranda.) Any historian interested in when certain individuals brought particular topics or ideas to the attention of the whole collaboration should start by searching the memoranda and meeting minutes in the CBX Notes.
3. Papers of Boyce McDaniel. McDaniel, the director of Newman Laboratory when CESR was proposed and built, has not kept many personal records. He does have a collection of letters, which he solicited in the spring and fall of 1975, from prominent physicists who commented on Cornell's initial proposal to build a colliding beam facility. The correspondence occasionally touches on the policy issues created by the submission of a Cornell proposal while SLAC's proposal to build PEP was still pending in Congress. Copies of most, but not all the letters are in the NSF files.
4. Papers of Maury Tigner. Tigner invented the scheme that made the Cornell synchrotron a suitable injector for a colliding beam accelerator. Prior to taking charge of the collider's design, he led Cornell's research in superconducting, radio frequency cavities for the purpose of building more powerful synchrotrons. He has not consistently maintained a Cornell office in recent years; some of his papers he passed on to those who maintain and improve CESR while others, in his absence, are in filing cabinets in the basement of Newman Laboratory. Prompt intervention may be necessary to save them.
5. Papers of Albert Silverman. Silverman was the first spokesperson of the CLEO collaboration. He has saved correspondence and memoranda he wrote and received in that capacity. They are a valuable source of information on the personal and institutional issues faced in the building of a multi-institutional experiment.
6. Papers of Dave Kreinick. Kreinick, a Cornell research associate, is a habitual note-taker, and as a Wilson Laboratory occupant, attends the more frequent, less formal meetings that occur between collaboration meetings. His notes constitute a useful supplement and cross-check to those of Horwitz.
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1. Papers of Edward Thorndike. Thorndike has served as spokesperson for longer than anyone in the collaboration. In particular, he was spokesperson from 1981-1983, during discussions of ways to upgrade or modify the CLEO detector in light of experiences with the old and discoveries made elsewhere.
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1. Papers of Nahmin Horwitz. Horwitz as principal secretary for the CLEO collaboration has tried to maintain a complete set of CBX Notes and of minutes to CLEO collaboration meetings.
2. Papers of Giancarlo Moneti. Moneti, a full professor at Syracuse, is a frequent note-taker and has a set of personal notebooks covering his activities through his whole career, including his work on CLEO.
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1. Papers of Frank Pipkin. Pipkin collaborated with Cornell physicists on experiments on the 12 GeV synchrotron that became the injector for the collider and was a strong supporter of the Cornell proposal to build a colliding beams accelerator. He has kept his incoming and outgoing correspondence, which may shed light on how other physicists from outside Cornell viewed Cornell's proposal.
Ohio State University
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1. Papers of Harris Kagan and Richard Kass. Both Kagan and Kass became faculty at Ohio State after holding postdocs under Thorndike at Rochester: Kagan in September 1981 and Kass in January 1984. Kagan, with Thorndike's support, succeeded in obtaining DOE support for building a new vertex-chamber for CLEO at Ohio State, and Kass' arrival in Columbus insured Ohio State would become a secure institutional base from which to work on CLEO. They are an excellent case of a collaboration "colonizing" a new institution. Both keep personal notebooks and carefully document their efforts to design and build hardware.
SUBCONTRACTING IN HIGH-ENERGY PHYSICS
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The conclusions in this section draw on many of the interviews conducted for the AIP Study of Multi-Institutional Collaborations in High-Energy Physics. Questions on subcontracting were a part of almost all interviews, and in carrying out the probes special attention was given to the role of subcontractors.
It appears that subcontracting was not extensively practiced by the collaborations in the period covered by this study. Many experiments involved no subcontracting at all, and in almost all cases of subcontracting the design was largely worked out by collaboration members, that is, the physicists and engineers at universities or national laboratories.
On the upsilon experiments (Fermilab experiments 70, 288, 494, and 605) there were several subcontracts. Superior Pipe Specialist in Cicero IL bent the coils for the large magnet used in E-605. The tooling was designed by engineers and physicists at Fermilab and built by Superior. One person from Fermilab worked with the subcontractor. The conductor for the coils was manufactured by Arizona Aluminum; again, someone from Fermilab supervised the manufacture. (Jack Jagger said that in several cases, coils made by outside subcontractors had to be redone at Fermilab, and he said that this problem is one of the reasons for the existence of a Conventional Magnet Facility at Fermilab.) A Japanese firm manufactured a scintillator for the calorimeter built by the Japanese physicists. Another Japanese firm manufactured the coils for another magnet used in E-605. A large number of analog-to-digital converters, which were designed by an engineer at CERN, were built by a firm outside CERN. In all of these cases, the design were entirely the work of physicists and engineers who were part of the collaboration.
It appears, however, that subcontracting has played a much larger role in experiments at CERN. In part this is the consequence of a CERN policy to see that money is spent in the various member states.
From the generalization that subcontracts in high-energy physics, at least in the U.S.A., have not involved much research and development away from universities and national laboratories, one might conclude that there was little important research and development for high-energy physics which took place in industry. That conclusion would be erroneous. There are a number of areas in which industry has made technological advances especially for the high-energy physics market but not for subcontracts on high-energy physics experiments. These areas include the manufacture of superconducting magnets, of photomultipliers, of image intensifiers, of lead glass, and of data transfer and data processing devices. For example, DEC's PDP 1 computer was developed for bubble chamber scanning, and SLAC has long served as a test bench for IBM equipment. There are indeed some companies that have catered almost exclusively to high-energy physics but have not, as a rule, undertaken subcontracts on particular experiments. One reason some companies have not undertaken subcontracts is to have clear patent rights to their work.
LeCroy Corporation, which manufactures electronic devices and components, is an example of a company that has catered to high-energy physics. Because LeCroy has been especially innovative, and because its products have been an important part of high-energy physics instrumentation, an investigation of this company's role in high-energy physics was added to the AIP Study of Multi-Institutional Collaborations. The investigation included a site visit to LeCroy, five interviews with four leaders of the company, and discussions of records keeping practices.
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In 1964 the electronics engineer Walter LeCroy, who had been working at Columbia University's Nevis Laboratory, founded a company that specialized in the manufacture of components and instruments for experiments in high energy physics. The company began producing electronics modules, such as logic circuits for receiving photomultiplier pulses, for individual experimenters. The company grew fairly steadily, and in the late 1970s it began producing for markets other than high energy physics. Today LeCroy Corporation employs more than 400 people, and it has sales and service offices in Japan and six European countries, in addition to three offices in the U.S.A..
Walter LeCroy's business strategy was to produce components and devices that could be used in many different experiments. The company worked with the directors of the equipment pools (which maintained stocks of equipment that the experimenters could draw on) at the national laboratories, and established particularly good relations with the Fermilab pool. Brookhaven was a difficult market to break into, as other manufacturers were dominant and their equipment had become de facto standard, but LeCroy eventually established a good relationship with the pool. In the early years LeCroy sold a good deal of equipment to SLAC, but later SLAC came to rely primarily on in-house electronics. Though Fermilab, Brookhaven, and SLAC have been important markets for LeCroy, a greater volume of sales has gone to the many smaller laboratories doing research in high energy physics.
The company did not develop products under subcontract, though it did begin to work with experimental groups. In many cases when a collaboration proposed an experiment, LeCroy physicists and engineers would prepare a description of what electronics LeCroy could provide for the experiment. The description was placed in a red binder, and LeCroy's "red books" became well-known in high energy physics. The experimental proposal would sometimes prompt LeCroy Corporation to design a new product, but with the intention of being able to sell that product later to other experimenters. As Werner Farr, Manager of Research Systems Division at LeCroy, expressed it, the company sought to "put extra features in and keep the flexibility and generality so that we can sell it later on to another experiment." Another reason for providing more than the experimenters asked for was, according to Alan Michalowski, Vice President at LeCroy, "the experimenters always wanted it for $10, and we knew we couldn't do it for $10, so we had to put more features in so we could get the price we had to get for it."
At about the time the company was founded, the National Bureau of Standards defined the Nuclear Instrument Module (NIM) standards. LeCroy was the first large manufacturer to adopt the standards; the existence of the standards helped LeCroy, and, inversely, LeCroy helped in the establishment of the NIM standards. Michael Bedesem, President of LeCroy Corporation, points to the national laboratories as "the strong advocates of standardization, because if they didn't have standardization, they couldn't pool the electronics." LeCroy continued to promote standardization—they were one of the first manufacturers to adopt the CAMAC and FASTBUS standards—and, by expressing their views to committees charged with setting standards, played some part in the defining of standards. According to Walter LeCroy, "the fact that housekeeping activities are taken care of by standardization..." contributes greatly to the long lifetime of many products.
LeCroy Corporation prospered partly because of its expertise in high-bandwidth electronics and in high-speed digital and analog electronics. As a rule the company possessed the latest technology, like the manufacture of hybrid circuits, that were in some cases not available to university or laboratory groups because of the high investment required. (This technological advantage made it, in most cases, unnecessary for LeCroy to patent its products.) The longevity of the product types and the ease in the reuse of individual components were also strengths of the company.
Our interviews indicate that LeCroy is unusual in the large number of Ph.D.s from high-energy physics employed, and the company philosophy has always been to understand not only the electronics technology but also the physics needs of the users. According to Werner Farr, the atmosphere at LeCroy, at least in the engineering and marketing branches, has been very much like that at a university or a national laboratory. One of the reasons for not doing so called "copy contracts" (that is, merely manufacturing a component that has been fully designed by others) is that people want the freedom to do their own designs. The force of the "not invented here" syndrome—the unwillingness to work on something designed elsewhere—is widely acknowledged in the industry.
Changes in high-energy physics experimentation in the last decade or so have made it more difficult for LeCroy. As experiments have become larger, and as the detectors have themselves become major facilities, there has been a tendency to use more special purpose electronics and to be less concerned with establishing standards. Also, when experiments were shorter in duration, there was more value in having products that were general and flexible enough to be reused later. The changes in high-energy physics experimentation have meant that the equipment pools at the laboratories, where LeCroy earlier did a large part of its business, have become less important. LeCroy has suffered in recent years from what they describe as the "too early, too early, too late" phenomenon: when the collaborators finally release information about the design of an experiment, the design is too firmly fixed to consider LeCroy's proposals. According to Farr, LeCroy now feels itself compelled to seek formal subcontracts if it wants to continue to be a major supplier of high-energy physics electronics.
LeCroy's greatest competitor has always been the in house groups. The company leaders argue that that has been an unfair competition because all the costs of in house development and manufacture have not, as a rule, been included in the comparison. Moreover, the advantages of commercial manufacture have often been overlooked; Michalowski points out that electronics developed in house is seldom well documented and can become almost unserviceable when the graduate student responsible for the design has moved elsewhere. Bedesem argues that the physicists at universities and laboratories should have concentrated more on physics and left more of the engineering to companies like LeCroy: "Maybe we would have had a few more Nobel Prizes, in the U.S.A. anyway, and gotten a few more discoveries over the last 15 years, if more emphasis had been placed on the physics and less on the toys of physics."
A related matter is the transfer of technology. Farr argues that there has been a great deal of "reinventing the wheel" because of lack of transfer at the detailed level. Each laboratory, each in house group, and each company wants to do its own design—again, the "not invented here" syndrome. Technology transfer has taken place mainly at a conceptual level. In Farr's words, "...it's really a pity that everyone thinks he has to develop his own preamplifier or his own flash ADC ... or whatever. It's a waste of talent and time...."
LeCroy Corporation has always, according to Walter LeCroy, been interested in the foreign markets because high energy physics has always been international. From almost the very beginning, the company had sales representatives in Europe. Because there was a large measure of international agreement about standards, LeCroy did not have great difficulties in selling electronics to the accelerator laboratories CERN or DESY. This made for a larger and more stable market; according to Michael Bedesem, "By doing 50% of our business overseas, we can offset government budget cycles."
For its first 13 years, LeCroy Corporation concentrated on the high-energy physics market. During this period the company grew at a steady rate, and its leaders believed that continued growth was essential for the health of the company. Since LeCroy had already captured a sizable fraction of the high-energy physics market, and since that market was not itself growing rapidly, the only way to sustain the steady growth was to diversify. Beginning in 1977 LeCroy Corporation began introducing new product lines, such as electronics for fusion research or fiber optic devices. Most successful has been the manufacture of digital oscilloscopes.
The diversification allowed LeCroy to apply advances made for high-energy physics instrumentation to needs of scientists in other fields. Walter LeCroy has described how various aspects of the Model 9400 digital oscilloscope are derived from technologies developed for high -energy physics, such as high speed trigger circuits, real time processing, and analog-to-digital conversion. (The Model 9400 has become an extremely successful product and is now being employed in a wide variety of research areas.)
RECORDS CONCERNING SUBCONTRACTS AND COMMERCIAL RESEARCH AND DEVELOPMENT
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In general, records dealing with a subcontract to an experiment can be found in the papers of the collaboration member overseeing that subcontract. In most cases, this source is richer—from the point of view of the historian of technology—than what the subcontractor possesses, since the latter is likely to include only the final specifications of the component and the administrative records produced in the course of its manufacture. In the few cases (in the period covered by the AIP study) where significant research and development was carried out by the subcontractor, then of course the subcontractor's records are very important.
It is the case that very significant research and development was done at LeCroy Corporation. Here there is almost no record of this work at the universities and national laboratories in the files of the collaboration members, since it was not done under subcontract. Like most companies, LeCroy has not had a carefully worked out records retention policy. The company is careful to keep the records required by the Internal Revenue Service, and the records required for providing service to customers (technical data sheets, circuits diagrams, and design specifications) have also been retained. However with most other records, such as correspondence, memos, and notes, the company has provided little guidance, and such things tend to get thrown away.
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For documenting work done under subcontract, the recommendations here would be largely the same as the recommendations made elsewhere in these AIP reports for the work done at the universities and national laboratories. The main exception is for those cases where significant research and development was carried out by the subcontractor. When such cases have been identified, recommendations similar to those given below, for LeCroy Corporation, might be appropriate. Similar recommendations would be appropriate also in the cases of other companies that have done important research and development for high energy physics, but not under subcontract.
Of the records produced by the employees of LeCroy Corporation, especially valuable are those that show how particular experimental proposals led to the design and manufacture of new products. Therefore all of the "red books" prepared by LeCroy should be retained. There are likely to be other records of the connection between experimental demands and LeCroy's products in the papers of individuals; for example, Alan Michalowski has folders on certain high-energy physics experiments. Other valuable records are those that document LeCroy's products, such as circuit diagrams and data sheets. Summary sales records showing when particular products were made, in what quantities, and what laboratories bought them also could be quite valuable to a historian.
Speaking generally, one can say that important records do get preserved when scholars make use of them. But this happens only when the historian or sociologist learns of the records and gains access to them before they are lost or discarded. What makes this mechanism of preservation even less effective is the paucity of scholars studying modern science and technology in relation to the extent and pace of contemporary research and development. More effective would be to alert the producer of the documents to their potential value, and this can be done by fostering an interest in history of science and technology. This is part of the mission of both the AIP Center for History of Physics and the IEEE Center for the History of Electrical Engineering (which serves the community of electrical, electronics, and computer engineers). LeCroy Corporation had already begun a project to write a company history, but, according to the President of LeCroy, the visit by Nebeker as part of the AIP study may spark new activity in the area of records retention.
Cf., Mark Bodnarczuk, "The Social Structure of Experimental Strings at Fermilab; A Physics and Detector Driven Model," Fermilab-Pub-91/63, March 1990.
This perspective could possibly be inferred from the documentary record by comparing the experiment's proposal with the collaboration's publication record. Direct evidence, if it exists, would be in correspondence between this physicist and others in the collaboration.
Cf. Sharon Traweek, Beamtimes and Lifetimes: The World of High Energy Physics, (Cambridge: Harvard University Press, 1988), 126-156.
For evidence of continuing difficulties between Europeans and Americans over the management of collaborations, see David P. Hamilton, "Showdown at the Waxahachie Corral," Science 252 (17 May 1991), 908-910.
For a description of the role of physicists in accelerator building in Lawrence's laboratory at Berkeley before the war, and the contrast with the individualism of research see, in particular, Wilson (1972), p. 471. See also Heilbron and Seidel (1989) Crozon (1987) provides a readable general introduction to the evolution of high-energy physics. Pickering (1984) is a sociological study of developments in physics during the period covered by this paper.
The data is from Pestre (1990), p. 480. For the difference between a bubble chamber experiment and an experiment using electronic or "logic" methods of detection, see Galison (1990).
For data of this kind one can use the so -called CERN Grey Books, produced annually since 1975, and entitled Experiments at CERN. These books list, for each current experiment, the names and (since 1976) the institutional affiliations of the physicists involved. Though containing inaccuracies, the books are a useful general guide to the composition and evolution of collaborations at the laboratory.
The locus classicus of the early research is Swatez (1970), which was based on work done at the Radiation Laboratory of the University of California from 1963 to 1965. See also, for example, Hagstrom (1964), Kowarski (1965) and Weinberg (1972).
For the 1970s see, for example, Wilson (1972) and Morrison (1978), both of whom are physicists. For the 1980s, see Galison (1985), (1987), (1988), (1990), Pestre (1990), chapter 8 and Traweek (1988), especially chapters 4 and 5. Pestre also studies in detail the strains which arise between the host laboratory staff and the outside physicists who collaborate with them at a facility. For more on this see Kowarski (1964) and Krige (1990a), (1992).
See NSF (1985) and HEPAP (1988). See also, for example, the study by Heusch (1984).
For example, Galison (1985) and (1990), and Swatez (1970).
On nostalgia see, for example, Blume's piece in Bud and Cozzens (1992), pp. 87-101.
 Quoted in Galison (1985), p. 316.
From Galison (1988), pp. 86-87.
See Wilson (1972). For Wilson's role in the founding of Fermilab, see Westfall (1989).
The interviews were conducted within the framework of a project to study multi-institutional collaborations in high-energy physics, which was initiated by the Center for History of Physics of the American Institute of Physics. Funding for my part of the work, which was devoted to interviewing some 40 physicists on 5 experiments at CERN, and to identifying important collections of relevant documents, was provided by the Andrew W. Mellon Foundation. The tapes and rough transcripts of these interviews have been deposited in the AIP Niels Bohr Library Archive in New York and in the CERN archive in Geneva.
Many of the documents used for UA1 were from private collections kept by David Dallman (which is very extensive) and by Alan Norton. Both are at CERN. I would like to thank Kyoung Paik for help with sorting through the documents, and for making rough transcripts of the interviews.
For the announcement of the study week see the circular by Rubbia in File DGR21298-CERN archives. The note prepared afterwards for the CERN management and entitled Conclusions of the study on the detectors is in (DGE21576-CERN).
There is a selection of these p-pbar notes in (JBA22633-CERN), for example.
The minutes of this meeting are in the Dallman papers (see note 13). Unless otherwise stated all of the following material dealing with the setting up of UA1 is from this collection. The documents are headed SPS p-pbar Project. Summary of the meeting.... or Minutes of the meeting held on... From about 8 March 1977 they were headed SPS p-pbar P92 collaboration.
A collection of the papers of the SPSC are in the CERN archive.
The early negative reactions to the Vienna group joining were mentioned in several interviews. I have also seen this in a document which I cannot now retrieve.
Minutes of the meeting of the SPS p-pbar project held on 13 December 1977 (Dallman papers).
For the visit to the RHEL as also being a propaganda exercise, see the Minutes of the SPS p-pbar project meeting held on 15 November 1977 (Dallman papers). For the report by the CERN management on the attitude of UK physicists see the memo by F. Bonaudi dated 18 October 1977 (DGE21576-CERN).
Letter Thirring to Van Hove, 10/3/78 (DGR21298-CERN). For the extent of the contribution made by larger Member States to UA1 see also Table 1 below.
For more on UA2 and the competition between Darriulat's proposal and Ting's see Taubes (1986), chapter 5. Taubes quotes Rubbia (at p. 59) as saying that "There was a strong French push essentially, and the man in charge, the director of research, was also French. He had a great sympathy for those people." As well as for UA1, its spokesman may have added, given the early and important commitment of French groups to that experiment as well.
For the importance of this kind of legitimation see Krige and Pestre (1986), especially section 5.
Cf. Morrison (1978), p. 353.
HEPAP (1988), p. 31.
For a useful technical description of the UA1 detector see Watkins (1986), chapter 9.
The "Agreement on the Sharing of Responsibilities Amongst the Participants in the Experimental Program based on a 4pi-solid Angle Detector for the SPS used as a Proton-Antiproton Collider at the Centre of Mass Energy of 540 GeV" dated 31/10/78 is in (DGR21298-CERN).
Columns 2-4 are from Annex 1 to the "Agreement" cited in the previous note. Column 6 is from paragraph 9 in the same document. The cost data in Column 5 are from letter Falk -Vairant to Yoccoz at IN2P3, 14/12/78 (DGR21298-CERN).
The list of meetings was collected together in the UA1 List of Publications prepared annually by Denis Linglin (Dallman and Norton papers).
We do not have a copy of the minutes of every Technical Committee meeting, and so we need to be cautious in our formulations. For the three years mentioned here we have the minutes of about 25 meetings, so around 50% of those that were held.
On the importance of how offices were arranged in UA1—a point mentioned frequently in interviews—see also Traweek (1988), chapter 1.
One interviewee mentioned that at one of the LEP detectors at which he now works there were 13 different physics topics distributed between some 400 physicists. All of them sign every paper produced even if they are working on a different topic.
Morrison (1978) at p. 359 writes that "authorship is one of the few areas where there can be serious friction and real unhappiness" in a collaboration.
This point is developed more extensively in the following section.
Taubes (1986) at p. 220 attributes these words to Rubbia, after the UA1 spokesman had been told that UA1 would present its results the day after UA2 at an important physics meeting: "If this is not changed," he allegedly told one of the organizers, "I do not think we go. This program makes us look like a spare wheel on a car.... Either we get basic symmetry of UA1 and UA2 in these subjects or we boycott the program. I don't see any other choice."
Cf. Traweek (1988), who (at p. 117) writes "Oral communication is fundamental to the operation of the particle physics community and successful senior physicists are masters of the form."
Wilson (1972), p. 468.
See Hagstrom (1964), p. 241.
See HEPAP (1988), p. vii.
For the importance of constantly discussing one's results see Taubes (1986) Book II, and Traweek (1988), p. 117 et seq.
The remarks about CCD devices are from P. Davies, B. Hallgren and H. Verweij, Short Study of the Charge Coupled Device CCD 321, p-pbar Note 31, 5/9/77 (JBA22633-RN).
Pestre (1990), chapter 13.6, which contains a general discussion of the difference between the American and European ways of doing physics in the early 1960s. See also Pestre & Krige (1988).
Cf. previous note.
Forman (1989). For other interesting remarks on how the postwar transformation of the field has changed the attitudes of physicists, see Holton (1985).
The importance of early education on gender stereotypes of academic ability is discussed in Hall, Roberta, The Classroom Climate: A Chilly One for Women? (Project on the Status and Education of Women, Association of American Colleges, 1982), p. 5.
This contradicts findings discussed in Hall, A Chilly Climate, p. 10, where women were found to experience increased discrimination in graduate school.
This is a form of sexual discrimination recognized in more extensive studies of women in science. (Discussion with Beverly Porter, Director of Education and Employment Statistics Division, American Institute of Physics, October 18, 1991.)
The small size of this sample does not allow us to take into account variability among European countries. Other sources show that while the number of women in physics is higher than that in the U.S.A. for some European countries, it is lower than the U.S.A. in others. (Discussion with Beverly Porter, October 18, 1991.)
"Overattention" to women in traditionally masculine fields is discussed in Hall, A Chilly Climate, p. 11.
One of the reviewers of this report has suggested that pursuing the meaning of "feminism" to the women we interview may itself be an interesting question to explore in the project's next phase and should better help us interpret the responses we received in the interviews discussed here.
See AIP Study of Multi-Institutional Collaborations, Phase I: High-Energy Physics, Report No. 2: Documenting Collaborations in High-Energy Physics and Report No. 3: Catalog of Selected Historical Materials (New York: American Institute of Physics, 1992).
For an illustrative study of a related background problem, see Peter Galison, How Experiments End (Chicago: Chicago University Press, 1987), especially chapters 4, 5, and 6.
Elizabeth Paris, "The Building of the Stanford Positron-Electron Asymmetric Ring: How Science Happens," unpublished typescript, August 1991. A copy is available from the Niels Bohr Library of the AIP Center for History of Physics.
Lynn White, Technology and Social Change (Oxford: Oxford University Press, 1962), chapter 1.
Paris, op. cit.
Galison, op. cit.
See report by Roxanne Nilan in Part C, Report No. 2: Documenting Collaborations in High-Energy Physics, AIP Study of Multi-Institutional Collaborations, Phase I: High-Energy Physics (New York: American Institute of Physics, 1992).
The name "CLEO" is a bit of whimsy. Because CESR, the acronym for Cornell Electron Storage Ring, is pronounced "Caesar," the detector that envelops CESR's beam pipe is appropriately nicknamed CLEO.
CESR also serves the Cornell High Energy Synchrotron Source, an NSF-supported facility that provides synchrotron radiation for a variety of experiments.
The interviews are with Alexander Abashian, Sajjad Alam, Chris Bebek, Karl Berkelman, David Berley, Dave Besson, Bernard Gittelman, Jan Guida, Nahmin Horwitz, Harris Kagan, Richard Kass, Boyce McDaniel, David Miller, Giancarlo Moneti, Rollin Morrison, Robert Panvini, Frank Pipkin, Albert Silverman, James Smith, Sheldon Stone, Ryszard Stoynowski, Edward Thorndike, Maury Tigner, and Paul Tipton.
Annual Report: Laboratory of Nuclear Studies, 1 July 1968 through 30 June 1969.
Annual Report: Laboratory of Nuclear Studies, 1 July 1971 through 30 June 1972.
One small group worked on experiments at Brookhaven and Fermilab in collaboration with other institutions.
Annual Report: Laboratory of Nuclear Studies, 1 July 1968 through 30 June 1969. Harvard University, State University of New York at Binghampton, and Ithaca College were also listed as outside users, but only the University of Rochester submitted plans for ongoing measurements.
Annual Report: Laboratory of Nuclear Studies, 1 July 1970 through 30 June 1971.
Annual Report: Laboratory of Nuclear Studies, 1 July 1972 through 30 June 1973 and 1 July 1973 to 30 June 1974.
Annual Report: Laboratory of Nuclear Studies, 1 July 1969 through 30 June 1970.
Annual Report: Laboratory of Nuclear Studies, 1 July 1970 through 30 June 1971.
Annual Report: Laboratory of Nuclear Studies, 1 July 1969 through 30 June 1970.
Annual Report: Laboratory of Nuclear Studies, 1 July 1973 through 30 June 1974.
"Long Range Plans for the Cornell Synchrotron Facility," Appendix 4 to "Report of Cornell Site Visit Review Committee, October 28-29, 1974." NSF/MPS 7509721
Boyce McDaniel to Alexander Abashian, 12 February 1975 attaching appendix by Tigner describing his injection scheme. NSF/MPS PHY7615423.
NSF and DoE employ different terminology: what is "elementary particle physics" at NSF is "high-energy physics" at DoE. The different terminology is of symbolic significance. NSF's term refers to what is being studied, as befits a "science agency," while DoE's term refers to the technique of study, as befits a research division of a mission agency. However, there is no functional difference associated with the different terminology.
Minutes of HEPAP Meeting, 12-13 January 1970. Copies in Niels Bohr Library, American Institute of Physics.
Ibid., 17-18 April 1970.
Bardon to Edward Todd, Deputy Assistant Director for Research, 12 May 1970. NSF/MPS, Cornell PO25958-000.
HEPAP Minutes, 24-25 May 1970.
Victor Weisskopf to Ed Creutz, 14 July 1970, and Weisskopf to William McElroy, 6 November 1970. NSF/MPS PO25958-000.
HEPAP Minutes, 3-4 January 1973.
See "Cornell Electron Accelerator Development Program," attached to McDaniel to Abashian, 31 January 1973. NSF/MPS P2P3518-000.
A group from DESY also worked at Cornell with Cornell physicists.
"Report of Cornell Site Visit Review Committee," 28-29 October 1974. NSF/MPS 7509721.
Anonymous reviews, circa 15 February 1974. NSF/MPS P4P2385-000.
Abashian, "Diary Note," 22 February 1974, and Abashian to Creutz, 18 October 1974. Both in NSF/MPS P4P2385-000.
David Berley, "Diary Note," 31 January 1975. NSF/MPS 7509721.
McDaniel to Abashian, 12 February 1975. NSF/MPS PHY7615423.
McDaniel to Abashian, 27 February 1975, NSF/MPS PHY7615423.
No list of participants, agenda, or minutes have been found.
"Electron-Positron Colliding Beam Facility at Cornell: A Compilation of Letters of Comment from some Prospective Users," May 1975. Copy in possession of Boyce McDaniel, Newman Laboratory, Cornell University.
Minutes of HEPAP Meetings of 21-22 February 1975 and 16-17 May 1975.
NSF/MPS 7509721. Other items in this file date from late 1974 and early 1975, which was when the FY 1976 budget would have been under discussion.
Frank Pipkin to Boyce McDaniel, 26 March 1975, part of "Electron-Positron Colliding Beam Facility at Cornell." Because McDaniel did not pass on the two negative impressions to the NSF, I am not identifying their authors. See handwritten, unsigned, undated note, [Albert Silverman] to McDaniel giving Silverman's understanding of a third party's negative reaction to a Cornell collider; and a signed letter to McDaniel, 25 April 1975. All material cited in this note is in the possession of Boyce McDaniel.
Report of the 1975 Subpanel on New Facilities of the High-Energy Physics Advisory Panel to the Energy Research and Development Administration, Government Printing Office (July, 1975), 4
The Subpanel anticipated that Isabelle would be ready for construction in FY 1977 after further research and development in FY 1976 and deferred judgement on constructing the Energy Doubler pending more research and development. PEP, by contrast, was deemed ready for construction without further research and development.
Alexander Abashian and David Berley, "Cornell University Site Visit Report, December 18-19, 1975." NSF/MPS PHY7615423.
"Minutes of the HEPAP Meeting," 8-9 December 1975.
Abashian to reviewers, 17 December 1975, emphasis added. NSF/MPS PHY 7615423, Folder 2.
Sidney Drell, HEPAP Chairman, to Edward Creutz, NSF Assistant Director, 12 December 1975, NSF/MPS, unnumbered file labeled "Cornell Electron Positron Colliding Beams, 1975-1979."
Berley to Edward Creutz, 16 December 1975, NSF/MPS, unnumbered file labeled "Cornell Electron Positron Colliding Beams, 1975-1979."
Given the number of reviewers, the size of the high-energy physics community, and Abashian's desire to reverse the impression of the Subpanel's report, it would seem inevitable and appropriate for Abashian to include at least some of the Subpanelists among the NSF reviewers.
Reviews are in NSF/MPS PHY7615423.
Sidney Drell to Edward Creutz, Assistant Director of NSF, 6 May 1976 and 3 August 1976. NSF/MPS PHY7615423.
In February, 1976, Cornell did receive permission to use increments of its synchrotron funding to develop prototypes of CESR components. See the next section for a discussion of Cornell-centered efforts to build the case for CESR.
See "First CESR Progress Report, January 1976 through April 1976," NSF/MPS PHY7615423.
Several commenters on Cornell's plans urged that time and funds continue to be made available for Cornell's research into superconducting cavities. That research did continue with significant results for accelerator technique.
Abashian to Creutz, 12 May 1976 and attached "Site Visit Report for April 15-16, 1976," NSF/MPS PHY7615423.
Thorndike to Silverman, 24 December 1975. Silverman Papers, Newman Laboratory, Cornell University, Miscellaneous Communication Folder.
Pipkin to McDaniel, 26 March 1975.
Pipkin to Marcel Bardon, 31 December 1975. NSF/MPS Cornell Electron Positron Colliding Beams, 1975-1979.
Thorndike to Silverman, 24 December 1975.
Pipkin to McDaniel, 26 March 1975, McDaniel papers.
Thorndike to Silverman, 6 April 1976, Silverman papers. Emphasis in original.
Silverman to Thorndike, 12 April 1976, Silverman papers.
[Name withheld] to Silverman, May 1978, Silverman papers.
This generalization is based on my reading of the interviews conducted for the study of 19 collaborations.
Abashian to William Wright, 24 February 1976. NSF/MPS Cornell Electron Positron Colliding Beams, 1975-1979
Vanderbilt, Rutgers and Argonne were on neither of Abashian's lists, which included 11 universities that neither joined CLEO nor made a proposal for the second experiment site. That is testimony to how easy it can be to express interest without commitment.
Cornell was able to stretch the funding it received for CESR to prepare the second site.
As were Columbia and Stony Brook, which collaborated for more than ten years on an experiment on the second site.
Lobkowicz to McDaniel, 29 December 1975, Silverman papers.
Karl Berkelman, "Proposal for a General Experimental Magnet for the Cornell Storage Ring," 13 January 1976. Copy in possession of Karl Berkelman.
Silverman to Experimentalists, 15 January 1976. Silverman papers.
Silverman to Experimenters, 19 March 1976. Silverman papers.
The momentum of a charged particle can be determined from the curvature of its track in a known magnetic field. But to disaggregate the contributions of mass and velocity to momentum, and thus identify the particle, a second measurement is needed.
"First CESR Progress Report," January to April 1976. NSF/MPS PHY7615423.
Ibid., as well as the "Second Progress Report." See also Lobkowicz to Silverman 5 April 1976 and Silverman to Lobkowicz 12 April 1976 plus other examples in the Silverman papers where the feasibility of superconducting solenoids is discussed.
Tigner to Silverman, 31 January 1976. Silverman papers.
Silverman to Experimenters, 3 September 1976. Silverman papers.
"Second CESR Progress Report," NSF/MPS PHY7615423.
D. R. Nygren, et. al., "Proposal for a PEP Facility based on the Time Projection Chamber," 30 December 1976, 22-25.
Silverman to Robert Panvini, January 1978. Silverman papers.
See Richard Talman to Panvini, Silverman, and McDaniel, 4 November 1978. Silverman papers. Talman, a Cornell professor, argued that problems with the dE/dX chambers stemmed from how Cornell personnel were bolting them into the octants and not with how Vanderbilt personnel were assembling them.
Norman Gelfand, "Report of Site Visit to Cornell," 6 January 1979. NSF/MPS Cornell Electron Positron Colliding Beams, 1975-1979.
Pipkin, Berkelman, and Tigner to Silverman, 21 June 1978. Silverman papers.
"Site Visit Reports," 23-24 May 1977. NSF/MPS PHY772659.
"Proposal for a PEP Facility based on the Time Projection Chamber," 30 December 1976, 9-11.
D. Andrews, et al., "Observation of Three Upsilon States," Physical Review Letters, 44 (28 April 1980), 1108-1110; idem., "Observation of a Fourth Upsilon State in Electron-Positron Annihilations," Physical Review Letters, 45 (28 July 1980), 219-221.