Interview with Kip Thorne

0:00 So, it's the 25th of March at a quarter past four in the afternoon, and I'm speaking with Kip Thawne. So, well, let me see. Where should I start? Well, I spent the last two or three days talking to various people in the group and others sort of connected with it in various ways. And one of the things that people were saying is that I know, of course, that Ben and Scott are just finishing off and have done a lot of their work in data analysis methods and so on. But I gather, to some extent, from the level I've heard that the younger students that are coming on are not necessarily doing data analysis problems. And not at the present time, except for, well, Teviatt Creighton, who's been in the group for about a year and a half or so, maybe two years. And if all goes well, we'll finish next year from now. So Teviot is doing some major data analysis stuff. The other students are really just barely beginning. And one of them doesn't have any project at all, it's just looking around. The other two have projects, but they're just very preliminary projects. So I expect that they will all or most of them do something related to data analysis, but I also think that the mix of things that will be going on in the group in the next three or four years will be less heavily weighted toward data analysis than they have been in the last four years. the reason being that there are a bunch of other groups getting into the data analysis business we worked in my group quite hard largely because there was a vacuum that needed to be filled and I wanted to make sure that when the data analysis was done that it involved a close tie to

2:30 the community that was working on sources and this community that had the power to compute waveforms off off the ground that way which I think we've done and now with Bruce Allen and a rather large group he's building in Milwaukee with Sam Finn and a group that he will likely build at Penn State where he's going to go yes and with Tom Prince building up a big effort at Caltech like the need for me and my group to work in that field is much reduced. It's not an area that I have any particular expertise in. And so I think we will likely pull back to some degree from it and focus much more on sources and on interfacing source issues to data analysis. What areas of interest would you identify in sources that are of most need for the larger? Well, one that we are just beginning to push Patrick Brady and Julian Creighton and I is this IBBH problem, an immediate binary black hole problem, that Sam, Finn, and I set up a workshop to brainstorm on a year ago last July. But nobody except us thought about much after that. And so Julian and Patrick and I have a paper that we have written that we have circulated to a number of people in numerical relativity for comment. And there are a number of people who are getting excited and we'll likely start pushing it, at least in part along the lines that we've suggested. So that's the problem of computing the waveforms in the gap between where the post-Newtonian approximation fails and where the merger begins, and where the conventional numerical relativity can begin. How much of that will be done in Caltech really depends on how much people want to do, because, again, it's something where having identified the problem and having done initial explorations of various techniques,

5:00 we can lay it out, and the rest of the community, as it looks like, will jump on it and run with it. And if Jolian and Patrick or someone else at Caltech wants to do that, great but they don't see any need for us to do it but part of what I see is one of as a major role for my group is to try to identify holes missing holes and do enough on them to get the community started working on them so that's a prototypical example of it we haven't yet submitted the paper for publication we have circulated it to half a dozen of the pundits in numerical relativity and gotten back from each of them something like three pages of comments and from several of them enthusiasm to get started right away so that is one another is the direction that Fenton Ryan pioneered on the problem of how that's more relevant Lisa than DeLigo of how to space-time geometry of a massive central body from the waveforms that are emitted by an object spiraling in. So Fenton sketched out Fenton showed that it should be possible in principle at least in the idealized case of an axisymmetric body in an spiraling particle that is in the equatorial plane with circular orbit. restrictive case. And I would like to see that pushed in much more realistic ways now over the next five to ten years so that it becomes a major aspect of LISA data analysis when Lisa flies, which could be as little as 10 years from now. You presumably know that there's a mission definition team now for Lisa and Sterl. Yeah, Sterl was trying to be a bit better. Although I gathered from him that there was a date that had been

7:30 muted for the launch was like 2017. That was an ESA date at one time. The NASA has talked about, well, Roger Blanford chaired an advanced planning committee for NASA for priorities of things to develop between now and 2008, something like that, and for flight in that time frame. And his committee for NASA, this was a year ago, identified LISA as something that they should be pushing the technology for in the next 10 years for flight sometime in the following 10 years. That is, flight could be as early as 2008. an age. And the mission definition team, the sterile, is set up then as a result of Rogers Committee's recommendation. And I was unable to attend the meeting of the mission definition team. I was only invited to be on it very, very late. Because of a misunderstanding, I had no interest, and I was already committed with my research group to be in Gold Beach then. So I don't know what happened. I've not talked to Sterl yet since that. That was just last week, a week ago. But my impression was that any NASA mission is just wide open as to when it would be in the time frame between 2008 and, say, 2018. that's probably what I thought. But I picked my brother. But anyway, so my interests are in both missions and the point of view of the science they can do and laying foundations for it. And so the things that Fenton was doing, There's a long-range aspect of that. But it's not an aspect that anyone else is paying any attention to at this stage, which is fine.

10:00 It's very early, and it's one of the more difficult things to do. But there are foundations to be laid for it. The key foundation is to be able to compute the orbits and then compute the waves. Computing the orbits requires really having a practical method to compute the radiation reaction, the evolution of the orbit under radiation reaction. And the first step is to have a practical method to do it in Kerr. So I see that as something that the community is pretty much aware of, and some people are working at a relatively low level now, I think, because neither Wald and Quinn nor the people in Japan are really pushing on it nor is Omosori those are the three groups who have proposed methods Dustin Lawrence is getting interested in getting back into research I have encouraged him to do a first step which is to try to actually evolve the orbits, compute the waves and evolve the orbits for the case of circular orbits where we have all the tools. Since thanks to you and others, we know the circular goes to circular. So we just need to know how the energy and angular momentum of the orbit evolves. And so the first step in what I see as a long sequence of things to see how the orbits evolve and the waves evolve. The second issue is to try to get a real practical way of computing the evolution of the Carter constant. The third issue is to get a real practical way of computing the evolution of the orbit in non-KER geometries. and then in the non-cur geometries there becomes the problem of computing the waves because you don't have separation of variables and Fenton did a first cut of that with scalar waves that's a very complex and difficult problem as well so I see all of those as issues

12:30 I would like to I think it would be useful to push the next few years. The waves, of course, from the black hole merger are really quite crucial, particularly on a much shorter time scale. So I've been working more from a propagandistic approach and trying to do whatever I can to Tribute to that being done on a fast enough time scale for the first LIGO searches. I don't think it's going to happen, but it's turned out to be too hard. But Dyke has made a number of phone calls and emails to Rich Isaacson and Art Comar trying to convince them this needs to be kept as a high priority. and that when the Grand Challenge project funding ends, which is this coming December, that they continue to put substantial money into that problem. Doing that is not easy because there's a perception abroad in the community that the Grand Challenge was a failure because it promised to bring waveforms on the timescale of the project and they didn't bring waveforms on that timescale. And it's far more complex than that. And I think in some respects it did not live up to its promise. In other respects it did very well and the problem turned out to be harder than it was. There's a picture abroad that all they did was fight with each other and they did more than fight with each other. They actually collaborated in serious sorts of ways as well. But from a political, sociological point of view, one, having substantial NSF funding continue for that and having the community continue to focus on that, that's not easy. It's a present situation. It was not handled terribly well within the Grand Challenge. should have redefined their goals in the middle of the project

15:00 when it began to be evident that they were not going to be able to reach the original goals and so forth. But anyway, I've continued to push that in private discussions with people at NSF and with all the people in the field of numerical relativity. and Anna and Scott's two papers on the subject of what you can get out of black hole mergers I think is having some impact. In our IBBH paper that we will submit shortly, there is just a little bit about the arguments that this has a very good possibility to be the first source of the scene. I've been pushing that at conferences like the Gravity Rate Data Analysis Conference in Paris. So I see myself as partly in a role of a propagandist to push particular things like that, even when in that case it's not something that is likely to be done in my own group because that's not where our expertise lies. Has the role of propagandist become easier as Lago gets closer to realization? Yeah, it's easier previously it had to be a role of convincing the community that they should spend huge amounts of money on this now it's much more pleasant and much easier The NSF, Congress are sold on it. Substantial portions of the astronomy community that used to be very skeptical are much more supportive, not all of this astronomy community by any means, but there's substantial support there. and there is a great deal of enthusiasm from people who are close to the field and enthusiasm in terms of them actually getting into the field and starting to work the problems. So it's really quite easy at this point

17:30 by comparison with what it was 15 years ago or 10 years ago or even 5 years ago. And the character of it has changed. It's also much more pleasant an issue of trying to identify what I think ought to be the priorities and job-loading some of the people about them, rather than trying to convince people that this is something that ought to be, a field that ought to be pushed and the money ought to be spent. So the larger picture? For the moment, at least. When they turn on and don't see anything for the first couple of years, have to do a heavy-selling job. But the strategy was, and I hope that it works out, to not over-promise, to make very clear that it's reasonably likely we won't see anything in the beginning. I think people will remember that. So I'm hopeful that if in the first search nothing is seen, I'm pretty hopeful that that will not present problems. I think another reason why it wouldn't present problems is that Bearish has been so, is being so effective of it building the scientific collaboration in terms of its size, enthusiasm, and broad geographical base, that that will help maintain the momentum and will be very effective at maintaining the momentum if the first searches don't see anything. The scientific collaboration consists of both theorists and experiments. The tentative dividing line or boundary for scientific collaboration is that things that involve development of data analysis algorithms and implementation of them are inside the collaboration. Things that involve computing waveforms for use in templates are outside the collaboration. We'll see it may shake out a little differently as time goes on

20:00 but I would, but I think that's a natural dividing line. It's one that Barish and I discussed a year or so ago and I think is more or less agreed on by the community although it's not been discussed very explicitly within the collaboration itself at these first two meetings I have stated at these first two meetings that that is where I see the boundary there's been no debate about that vision and ultimately the reason for a fairly sharp boundary is that if you're in the collaboration those pieces of one's work that are in the collaboration are subject to the rules of the collaboration and the rules of the collaboration are somewhat restrictive in terms of publication procedures and setting of priorities and so forth. Certainly people can work on topics that are defined to be within the collaboration. They can work on it without being part of the collaboration. But it may be harder to get funding, presumably will be, if I wanted to work on the development of certain data analysis algorithms three years from now. And the collaboration had set its priorities, and this was not a priority of the collaboration. And it also wasn't a new idea, it was an old idea. Then I expect I will have trouble getting money to do it. so given that that's how it's likely to fall out the priorities will be set within the collaboration and NSF funding will be significantly influenced by the priorities I think it's important to keep outside the collaboration all those things that don't require close coordination because the sociology of the theory community is not a sociology that is very amenable to operating within this collaborative kind of a structure

22:30 where priorities are set and people are expected to work within what is mutually agreed. How would the priorities be set within the structure? Who would be chiefly responsible? Well, I think it's a little bit unclear as yet, but I presume that the priorities will, well, a first cut of the priorities will almost certainly be made by the people who are within the working groups inside the collaboration. How it will be carried from there, I don't know. And I've not looked closely at the charter, which is just beginning to be debated to see to what extent that's defined within the charter. I need to spend a little time going over it. Myself, I don't like operating in that kind of an environment. I understand that it's necessary for major pieces of the field to go forward. personally to reduce my own efforts in areas that are defined within the collaboration but this is not something that I have yet said publicly and not something that it is something that I need to discuss in the context of the definition in the definition of the publication policies and so forth. There are others like Sam Finn and Prince and Bruce Allen, I think, are quite satisfied working within those kinds of rules. And they, for them, the benefits outweigh, I believe, the constraints. For me, since after Robbie Volk took over as director, I always kept my group independent.

25:00 Well, I always kept, even when I was chairman of the steering committee at LIGO, I kept it independent. But once I was out of the steering committee, I kept myself independent, my group independent, in part for those kinds of reasons. It's just not a style of cooperation that I like. It's a style that is necessary. I'm thankful that there are large numbers of talented people who can work very effectively and happily in that way. but for me it's not a terribly happy way to operate so what was the example of the constraints on publication well the way the publication policies are currently being discussed if you do research on a topic that has been discussed in collaboration meetings you have to before submitting it for publication you have to circulate it to the collaboration and not only invite comment but also invite requests to be co-authors on the basis of people think that they have contributed something substantive to this paper in collaboration meetings or discussions and so you're no longer to a significantly lesser degree than to a significant degree one gives up control of the publication of one's own research a group discussion Now, fortunately, most everybody in our field is very collegial, and I don't anticipate there will be major problems, but for me to operate within that kind of a system is a little grating. It's not that I challenge the rules. I would like to see the rules maybe reformulated a little bit, but I don't challenge the need for these kinds of things. in areas such as the actual implementation of data analysis algorithms

27:30 or the development of techniques to control thermal noise or what have you, where there has to be coordination, where there has to be things have to come together in the end on a well-defined time scale in a predefined manner to the extent that you can I don't want to operate that way myself if I can avoid it Yeah. Thank you. Thank you. Thank you. Thank you. Oh, yeah. So the style of management, as I've heard of, within the Lago science community, you were saying, of course, that within relativity people, in relativity theory, people aren't used to the style of this way of doing things. Does this come from the experience of some people in collaboration from other fields, or is it something that's sort of grown organically for the needs of them? No, it's experience in other fields. A number of people who are involved in LIGO, perhaps most significantly Ray Weiss in this case, have a lot of experience in other fields. and Ray Weiss' experience in the Colby Project has led to much of how they are trying to define things at the present time. and Barry Barry's experience in high energy physics. I think people are really quite, many people are really quite happy to accept this as being a useful tool

30:00 that everybody desperately wants to make happen and being quite acceptable. And I feel that way in principle. I think one wants to do what one can to make it, give people as much independence as one can while still making it work and work effectively. So I think there's some tweaking to be done on these things. but I certainly agree this is how things need to be done but he just has our own scientific personalities and mine is not very happy being there I felt the same way about the project as a whole I was very happy to pull out of being an integral part of it when Robbie came on board So the theorists who would be involved in the agro-science collaboration would be principally involved, would be basically involved with the data now. Well, that's not entirely true. There's a lot of other stuff that's going on in my group and that I expect to have continued. it also falls within the LSC Yuri Levin has been doing some beautiful work on thermal noise which I think has radically changed how people think about thermal noise right at the front of exploiting this that would fall within the collaboration has to on the other hand The kind of work that he has done could readily be done outside the collaboration by a theorist and offered the collaboration, but I could not commend significant funding for it, probably three years from now, if it's not defined to be inside the collaboration. the design of quantum non-demolition interferometers which I think is going to be crucial likely to be crucial in the late 2000s which Yuri and I are working on with Bruginsky

32:30 that falls clearly within the collaboration as well But we, Caltech has just submitted a proposal for a NSF, Science and Technology Center, for quantum metrology. And I guess that's what it's called, I forgot whether it's quantum information science, I guess. and I'm part of that proposal it's an 18 million dollar proposal the stuff on quantum non-demolition that I would like to do is in there and I could well believe if that gets funded that I'll just pull off and do the quantum non-demolition stuff that's related to LIGO funded through that and I will not be beholden to my NSF grant and to LIGO funds for doing that. But it will enable me, in that particular case, to do it outside the collaboration. But that also, that is an example of the kind of thing that I prefer to do anyway. Nobody else except Bruginsky thinks this is particularly important. I mean, what I enjoy doing is identifying something that other people don't think is particularly important and working it in my own happy time and carrying it to the point that the foundations are laid and I can convince other people they ought to work on it and then go leave it. and so I can do that there for a while because others have their hands full doing other things and they haven't really accepted that this is going to be crucial and so we'll see how it works out But those kinds of things that may be formally defined within the collaboration, I may be able to work outside the collaboration just by virtue of the fact

35:00 that nobody else is working or recognizes their importance at the stage when I'm really wanting to dig into them. But we'll see. It's early on. Well, to my personal curiosity, I'm tempted to ask, but this is probably a difficult question to answer. I'm interested in your impression of your strike rate, as it were, in getting people, the community, more interested in the problem that you decide to take up. Because in my experience, of course, where one has the first influence of Lago, it certainly seems as if the directions that your group has taken have, to a great extent, been taken up by the community. I think that that's been true in recent years. the thing I put a lot of effort to in the 1980s with the membrane paradigm for black holes has been very spotty it certainly was nowhere near a home run I'm not sure if there was a first base or not but it is interesting to see eminent particle theorists trying to use it in the analysis of quantum properties of black holes or quantum gravity, which I never imagined it being used in. There still is an occasional paper written by an astrophysicist using it. But I would say that that was not nearly as successful as I had imagined it would be or as I thought a lot for me. But these things related to gravitational waves I think have been reasonably successful. Well, the quantum non-demolition did not take off in the hands of the community that I thought it would. It has taken off in other communities. It has not taken off in gravity waves. because it hasn't really been needed yet and it has been slow but it has now taken off pretty strongly in the quantum optics community and it now really is

37:30 sort of in much modified and augmented form being incorporated into quantum computation much of the spirit of the concept But I'd say my record is, in some areas, is mediocre to medium, and others have been very successful. One of the things I'm obviously very interested in is the interface between theorists and experimentalists. And it seems interesting in the case of the LIGO scientific collaboration that there's what seems, as far as I can tell, a complex boundary with perhaps, I wonder if you agree, some kind of unusual relationships in that the theorists are so strongly involved in data analysis issues and even, as you commented, in issues which are basically related to the texture design. First of all, I suppose the question is, is it your impression that that is somewhat unusual? And then, I suppose, secondly, does that create, or are there obvious tensions between experimentalists and theorists over their respective roles? It's somewhat unusual, but not all that unusual. In Kobe, which I know mostly through Ray Weiss, a key person in the data analysis was a theorist. I think it's at UCLA whose name is escaping me at the moment. There was a precedent in Kobe. If somebody who was a theorist was not involved in the design or planning of the experiment, that came in moderately late, but really knew how to formulate much of the data analysis and became a major player. There was one individual, Ned Wright. That's his name, Ned Wright. As I say, I know of this only three great wives. So that's the one example that I'm aware of. within Virgo there has been a strong attitude on the part of the people like Michel Davier who is

40:00 in some sense in charge of data analysis that the theorists should be kept out of it and in internal discussions between Virgo and Ligo between Davier and Beresh a year and a half ago this idea was pushed very strongly by that group of experimenters in Virgo and was completely rejected by Barish so there is a piece of the community within Virgo that has strong views on about this is not the appropriate province for theorists. I don't think that that view extends to the leadership of Virgo, to Briere and Giazodo, both of whom I think have real recognition of and respect for what a theorist has to bring. And within Virgo, there is somebody named Jean-Yves Vinay, who has been involved right from the beginning, whom I would really recognize as a theorist, and who does just the same kinds of things, many of the same things as I and my group have been doing in non-data analysis stuff, design of baffles, for example. I don't, but within Virgo, the data analysis, how data analysis is to be done is, well, Virgo has internal problems, severe internal problems. I'm not up to date on how things are developing but they had to as part of the price of getting the project going and getting enough political support to get it approved they had to in some sense give various aspects of the Virgo project to various institutes and groups in order for those institutes to sign on and so data analysis I gather basically given to D'Avier and his group and institute. I know this third-hand. I know first-hand, I know details third-hand,

42:30 I know the basic picture is right, more or less first-hand from talking to Brié. And so they had, one consequence is that Brea and Giazoto have far less power within Virgo than Beresh has within LIGO. And so they can't just basically dictate that you are going to allow the theorists to play a major role in the way that Beresh can if there is resistance. Just dictate that. Virgo is a far more closed operation than LIGO is. is in much more serious danger of failure as a result. Part of the situation in LIGO is that the people involved up until now have been stretched so thin that there was nobody within the LIGO team who could really devote any significant amount of effort to data analysis. and as I mentioned before I saw that as a vacuum a serious vacuum and that's why I got into it and my getting into it I think it played a major role in getting Bruce Allen into it and Bruce came and spent time at Caltech and interacted with us and so forth. It more or less is an outgrowth of discussions with me and then later with Bearish. Sam Finn would almost certainly have gotten into it on his own. But LIGO being open to it, I think, is in some significant measure because it is a vacuum that needed to be filled. And I think Bernie Schutz, having gotten into data analysis right from the beginning with the GEO project, also had a very big influence. That influenced me, too. And when I decided that we needed to start pushing in that direction, I went and spent a hunk of time with Bernie and his group in Cardiff.

45:00 and then Barish is a very open person he really, I think he's a master scientific manager and strategist and he has a very inclusive sort of approach to things anybody that's interested in working in this area who has talent regardless of background, he welcomes and tries to find some way for them to contribute. So those are some of the factors, I think, that surround the question you ask. So I guess, following on from that, there's, well, a couple of issues that I wanted to follow on from that. One would be the question of how the data will sort of be handled. From a practical point of view, the data starts off in the hands of the experimentalists. And I understand that already in your group, you've had some access to... We've had access to the data for a year and a half or so. access to the data to prototype data is by memorandum of understanding with the LIGO project so that for example Jolie and Creighton used those data a year ago to explore to do prototyping tests of matched filler techniques for looking for waves from black hole ring down. But before he could even present any results on that project at a conference, even just verbally, he had to do a run-through presentation for the LIGO team in Barish, who then made comments, suggestions, complaints, and so forth, and he had to get Barish's approval to go talk at a conference about this

47:30 since he had used LIGO's data. And then when he wrote up his conference proceedings, his article for conference proceedings, he had to get it approved by Barish before it could be sent in. And those procedures had to be followed and spelled out in the memorandum of understanding between my group and LIGO for the use of 40 meter data. There will be similar, rather strict rules tied up in MOUs on the use of the LIGO data itself from the big instruments. the details of which are yet to be determined the other question that I had was I was inspired somewhat by something Sam Finn said I was talking to him yesterday concerning And the question of whether the theorists can expect to handle the data in the same way or with the same knowledge that an experimentalist who is actually working on the instrument could. And so if it turns out, then the theorists, because of the manpower problems or whatever, are chiefly responsible for the data analysis in the real detector, do you think there's likely to be a problem in that they won't have the same insight? I think that they will not be allowed to have the major responsibility in the sense that I'm quite sure it will be defined that any project involving data analysis on those data, at least in the early years, will have to involve people who have worked with the instrument itself being full participants. Partly from the point of view that they need to participate in reaping the scientific benefits, but also partly from the point of view that somebody who is not intimately familiar

50:00 familiar with the instrument and its vagaries is not likely to be able to handle the data with wisdom. So I think the answer is it just won't happen if theorists can go off and work with the data by themselves. At least not in the early age. so in that context I wonder if you have a sense of what types of methods of data analysis that people have looked into so far are likely to be the most used when the instrument comes along, for instance I've heard people say but only perhaps so far commenting at second hand and so on that some experimentalists with match filtering methods? Yeah, I don't know the right... Well, first of all, I know this only second-hand. I'm not really disgusted, particularly with people who are said to be unhappy. I think the word unhappy is not the correct one. I think it's more skepticism. and I think these are issues that are going to have to be debated my own guess at the present time is that match filtering will be one of the major tools but that there will also be a lot of effort put into things to the kinds that Ana Flanagan proposes for looking for black hole mergers in his first paper with Scott, or maybe it's his second paper, where you basically take a stretch of data from the two or three interferometers. you filter it to remove everything that would not look like a conceivable signal then you cross correlate the data from the two instruments that kind of

52:30 technique can't begin to compete with matched filtering in the case where you know something about know the signals well enough to do match filtering when there are a large number of cycles. When there are a modest number of cycles, it can even be competitive with match filtering, but a modest number may be you start to lose significantly at something like a half a dozen cycles. thing shorter than a half a dozen cycles, I think match filtering is not particularly needed except to try to understand maybe a really helpful understanding what you saw. So that kind of thing that does not rely at all on match filtering, I think is going to be a major approach that's used. And then Fourier, the kind of things that are being developed Patrick and Tevye for periodic sources I think with stat searches the way that Maria Alessandra Papa is doing it bar data and developing for geo of tract searches where you basically do A foray transform for some period of time, the Formigo might be a day, and then another day, and then another day. And instead of stacking, you just lay them out one after another and search for patterns of peaks. You see a peak here, you see peaks there, you see peaks there, and see if you can see a pattern that wanders in frequency. Those kinds of things, either stacked searches or tracked searches with Fourier transform data of finite duration or maybe both stacked and tracked I think are likely to be a major part of it. I think the experimenters who are skeptical really have in mind

55:00 that Aina has been talking about where you don't put in any preconceived notions. But that, as you say, that hurts you somewhat or significantly if you have a lot of signals that you could be looking at. And again, obviously in general, having a lot of cycles is obviously good in terms of building up signal to noise. So presumably that'll play a role in the question of whether one sees anything in the early stages. And I guess this ties into another question that I wanted to bring up. Talking to Patrick, he was telling me that at the LSE meeting there was a certain amount of discussion over the question of how you quarter the criteria that would make you convinced that you've actually seen something. And so I was wondering if there's any emerging consensus as to what kind of thing. I think the discussion of that has just barely begun. It was triggered by Ray Weiss, who wanted to introduce it as a topic that the LSC Council needs to really chew on, and wanted to get it introduced now at the beginning. but I don't think it's something that you are going to wind up with any resolution on or anything approaching a resolution until about the time the first searches are getting started. Ray has introduced it because he went through this with Colby, where they had the evidence, some evidence for anisopery of the cosmic background distribution on the sky fairly early on when they had the data. But there were enormous differences of opinion among the Covey experimenters as to what would be required for them to be able to lay claim that they'd really seen it. did lay a claim, it still was sufficiently marginal that there was some amount of skepticism

57:30 in some quarters. It has since been very clearly confirmed by other experiments. But that was an example. It was very hard because the signal was marginal and was terribly important. It was a little stronger than marginal, but not a lot stronger than marginal. And the the LIG will be similar. So you really need to think that issue through hard. So I think the discussion of that issue has just barely begun, and the people within the LSC are extremely ignorant as yet of the facets of it that are going to be central to ultimately reaching some resolution. I'm just going to turn on the heat. I know that you love living at low temperature. I hope I'll be fine. Actually, a good southerner likes it. Fortunately, I'm okay. so I suppose given that there's given that there's some sense of concern over well obviously concern over how you that you want to be very convinced by the result that you get that means to a certain extent Mentally, people within LIBOR are prepared not to find anything for a reasonable period of time. Oh, yeah. I think very prepared. Maybe over-prepared. Which is, I think, a result of the combined effects of the skepticism in the astronomy community in the way that, in the beginning, I insisted on selling this at NSF. Are there, how much of a factor is the history of the field of gravitational wave protection?

1:00:00 Of course there were major controversies. I think that's less of a factor now than it has been in the past. because LIGO scientific community is now really coming to be dominated by people whose roots are not in this field and who are maybe even relatively unaware and surely relatively insensitive to the history of the bar business. Certainly for those of us whose roots are in this field been a significant issue. But I think it's of ever-decreasing importance as the field grows, it grows in strength, it grows in confidence, and it gets peopled by people whose roots are elsewhere. So it's just a lack of people being influenced by experiences in other areas? I think so. So I guess I wanted to ask you about, for your opinion on the relationship, the likely evolution of relationships between different methods of gravitational wave detection. I was just talking to Frank Estorup about Doppler tracking methods and he was saying that after Cassini that they are not considering any future progress in that area. Then one has LIGO and of course there are possible space-based detectors. And then in addition a little bit unclear at the moment than the current status of bar detector projects like the Taiga project. Where exactly do they stand at present? Large bars are being pursued vigorously in Italy and in the Netherlands, the large spherical bars. I think in the United States they are very unlikely to take off because

1:02:30 the Ashdakar panel a year ago gave them a black eye I haven't looked at the Ashdakar panel's report to tell me the truth I believe it's on the web I only had heard of it I ought to read it you ought to read it but I think it was very influential in NSF's decision not to fund work toward large tortigas. I'm not convinced that was the right decision. I'm not convinced it was the wrong decision. It's not an issue that I had to struggle with. I think it is an issue that I know more about than the people who wrote that report, probably. And in my view at the present time, it's not obvious what the right decision is. But I'm pleased that the groups in the Netherlands and Italy are pushing them. Scott is in the late stages of writing a manuscript on the uses of narrow-banded instruments to search for equation state information, neutral historical essences. I think that kind of application is likely to be very important in the long run. And I think it's not obvious at all which is going to be better at it, the interferometers and the bars. If I had to lay bets, it would be on the interferometers, but on a bang-for-the-buck basis. If you were to spend a comparable amount on bars to what you would spend simply on narrowbanding the interferometers, set aside any other money that goes into interferometers but perfecting and building narrow banded interferometers I'm not sure that in itself I would bet over the log haul is tens of millions

1:05:00 of dollars if you spend tens of millions of dollars on bars which they may well do in Italy and the Netherlands they may come out to just as well or better I don't know so I think there's a good chance that there's a place for the bars in that niche at high frequencies where the shot noise is so bad and interferometers and where you may need to narrow band in order to go after small amounts of very valuable information. The interferometric detectors, laser interferometric detectors in space, I'm virtually sure are going to fly and that they will have a far easier time of it getting funded and approved than LIGO had. The sources are, when you compare the source strengths with what the projected technology can do, they're in a much better shape than LIGO was at the time we were proposing LIGO. they can surely see binary stars they can surely see neutron star binaries not in the merger phase but things that have say a thousand, a hundred thousand, a million years to go until they merge with their galaxy Martin Rees with Stein Sigurdsson has written a paper arguing strongly that they have a near-guaranteed source in the waves from white dwarfs and neutron stars spiraling into massive black holes in galactic nuclei, with the event rates of some per year. Since the signal lasts... in a sense you would presumably integrate up a signal over a time of a year that means seeing a number of them simultaneously all the time sort of in the late face of it's about.

1:07:30 Correspondingly the perception among people like Martin Rees who have been somewhat skeptical of ground based interferometers is generally rather more favorable toward Lisa. And I think getting Stirl to chair the mission definition team was a masterstroke. This now becomes something that is well-based in the conventional astronomy community, being that headed up by somebody who is a card-carrying theoretical astrophysicist compared by contrast with me who has sometimes accepted theoretical astrophysicists. And, you know, both Roger and Peter played major roles in making this thing begin to take off and neither of them consulted with me in the least about it. Which was interesting to me and very pleasing to me to see them doing that. So I think the momentum for Lisa or something like Lisa is strong and gathering strength, and it's almost bound to happen, and I think sooner rather than later, sooner being in the earlier part of 2008 to 2018, but we'll see. unless there are technology difficulties that I'm unaware of in terms of the amount of technology to be developed. The Doppler tracking has always been much more pessimistic in terms when compared to the sources either LIGO is at least something like LISA but it was never all that expensive of all the technologies that were being done that were being flown on the spacecraft anyway for other reasons a typical add-on cost for each mission of a few million dollars

1:10:00 tens or hundreds of millions. So it was well worth pursuing. But as the momentum grows for Lisa, I think the interest in Doppler tracking is going to decrease. I would have hoped that there would be some follow-on to Cassini, and I'm a little surprised that Frank is thinking there might not be. There are not explicit plans for it, I think they, I gather they could pick up another order of magnitude or so with a differently-configured mission, but I've not paid a lot of attention to it. Well, I think he said that they certainly might continue to try to get on missions, but the one problem was that he didn't see much room for continuing to improve their sensitivity. as I say I could be wrong I thought that there was some room as they went to still higher frequency bands and flew several different frequencies and with an onboard clock which they may want to do for other reasons he's not been one to really push that as much as maybe John Armstrong. Have you talked with John? You ought to talk to John. Did you talk to Hugo Walquist? Hugo's less involved now, I think. maybe the most useful person to talk to besides Frank is John Armstrong. maybe he would go after that. So, would you say that there's still room for a race between the different methods as to which would be the first to detect gravitational waves or just like a similar ground-based interferometer is clearly involved with it? Well, I think the odds are very high that it, are rather high that it will be the ground-based interferometers. It remains conceivable that the bars will see waves first,

1:12:30 though not very likely. It is conceivable that the pulsar timing will come out with convincing evidence before LIGO does. and it's conceivable that it will be shown that the anisoterapies in the microwave background are in part due to gravitational waves. But I think that convincing cases coming from any of those other approaches are rather less likely than that will first come off of the interferometers. But we'll see, particularly with the pulsar timing, now that they're getting to be more millisecond pulsars, you can time a handful of them that are relatively clean and quiet and look for correlated changes in their frequencies, which I think would be a very compelling case if you saw correlated changes in the frequencies of five different pulsars at five different locations on the sky. It would be hard to believe it was anything except gravitational waves passing over the Earth. And I guess my personal view is that if something were to beat us to the waves, beat the interferometers to the first detection, it would be more likely to be that. Particularly since the interferometer first detections could well be delayed to the 2003, 4, or 5, or 6 time frame. And the pulsar timing business is developing at a reasonable pace. And is that the fact that the ground base could be divided by significant interactions

1:15:00 put the space base at all in the running? I don't think so. I don't think there's much chance at all of the space base flying 2000s. It would be very surprising if LIGO wasn't seeing things in the mid-2000s. Who is mostly working on the Pulsar time? Well, of course, the people who've pioneered that have been the people in Joe Taylor's group. I don't know who is really pursuing it vigorously now, aside from Joe and whoever is currently in his group. His group is sort of like mine. It is very talented people who come in and just grab hold and do things and then move on to other institutions. So since I don't follow that field closely, I don't know who those key people are. It's presumably not Joe. The last time I looked seriously, it was a guy named Dan Steinbring, or elsewhere that was a young guy in Joe's group for a handful of years in the late 80s, I think. But there could well be other groups now pursuing it, though to really do long... You've got to collect data quite regularly over a period of a few years and very good timing data and I don't know whether any I don't really know whether any place has the possibility to do that aside from Arecibo and I don't know whether anybody besides Joe at Arecibo is really pushing it a guy named Cordes at Cornell has done some anyway I'm just not up to date and I think that people in working on LIGO are virtually totally uninformed about it I sort of see this as something that could come out of the blue and just really surprise the interferometer people

1:17:30 something else that people were talking about during the week that interested me Scott and Ben, for instance, who were up at the City of Elves Gravity meeting, were saying that there was a discussion inspired by Jim Hartle about directions within the field and that some of the people there express fears or worries that funding would become increasingly directed towards library topics and away from the subjects that they were interested in. So I was interested in this because, of course, it used to be that the most notable opposition to fears in that respect for instance, from a strabler, so it's interesting to see it within the relativity community. In what kind of areas do you think those worries lie? What kind of subject? I haven't talked with people who have those kinds of worries, so I'm not sure where they're coming from, but I have been aware that there have been worries of that sort for a long time also within the relativity community, not just within the astrophysics community. though I think the great majority of the relativity community have been enthusiastic and they've actually been willing to belt tight in order for LIGA to go forward but nevertheless there has been anxiety and there have been years in which early on there have been years in which people were told that they were being taxed to some degree theorists in order to provide enough money for LIGO that it would continue moving forward. That's not been true in recent years because LIGO's been so enormous that the amount of money you could get out of that kind of a tax on gravity theorists would have no influence. But that was the case in the 80s when we were just barely starting felt a little bit of pinch occasionally. I think these concerns may arise to some degree

1:20:00 now because LIGO has been a line item outside the physics division, outside the gravity program, and LIGO now will become, the operating budget and the R&D budgets will become items within the gravity budget. So it's going to look quite different in an organizational sense. And I think there are genuine concerns, causes for concern, as to how that shakes out in terms of internal organization and prioritization within NSF. I think it's perfectly reasonable for people to be concerned and I think these things need to be debated that some wisdom has to be exercised in setting up the structure of the budgeting process within NSF in this new era. But I'm sure that that will be done. Isaacson, Burley, Parrish, and NSF's advisors, people like Ashdakar, aware of the issue and I've not been involved in discussions about it at all so I'm just giving you a background of my understanding of those things to set it in context the total theory budget in gravity I don't know what it is annually but I would guess it's five million dollars I guess. Maybe you know. No, I don't. I guess I've ordered $5 or $6 million. It might be more. operating budget $20 some odd million a year. LIGO R&D budget will be somewhere a year. So theory, suddenly the gravity program, if you include LIGO, becomes much bigger than

1:22:30 it was, and theory is explicitly a smaller component, a significantly smaller component. can understand why there might be some causes for concern but this is an issue of major influx of new monies into the into the gravitation budget that has been carefully planned in advance and there's no way that if they shut down all the theorists they couldn't begin to cover the operating costs and they would only at most barely begin to cover the R&D costs. gather that there's sort of NSF money which is said earmarked is that true for LIGO scientific collaboration or she's somewhat connected I don't know precisely how this works, I think I know but I don't know that's a warning there is money that is earmarked for LIGO R&D proposals that want to tap that money get sent to the LIGO Program Advisory Committee, which advises Barry Barish on LIGO planning, get sent to the LIGO Program Advisory Committee for review, and then to Barish for review. and those comments go to NSF in parallel with the regular male reviewers' comments. And NSF makes the decision in light of the reviews that come both from the Program Advisory Committee and from the male reviewers. Whereas money, if you're proposing for stuff that is not within the scientific collaboration,

1:25:00 then you just have the normal mail review process. But they are different colors of money. There is this rather large pot that's set aside for LIGO scientific collaboration or LIGO R&D, which is, as I say, I think it may be like $6 million in the coming year, but I'm not sure on that number. and so presumably that performs considerable attraction for people to work on library projects assuming they don't mind working That's right but as we discussed before library-related projects means at the present time nothing more theoretical than data analysis and so there has to be The stuff on computing waveforms from mid-spiraling binaries, for example, post-betonium computations, that will continue, I presume, to be funded out of regular gravitation funds and not from the special R&D funds. Correspondingly, the people who work in that kind of an area or in numerical relativity will continue to have real independence from the LIGO scientific community, from the LIGO structure and LIGO prioritization procedures and so forth. Well, obviously... This is my personal view. This is more or less what I have begun I stated it very explicitly at the LSC meeting within the data analysis subgroup, but there's been no debate of it. It's the way I expect it to shake out. We'll see. Obviously, you, both your own work and that of the group as a whole, has been very closely tied to LIGO and gravitation and detection issues for some time.

1:27:30 How, I suppose in terms of the path, how do you see the, how do you see it impacting your work and your group's work once LIGO is a success and you have detections coming in? I mean, we sort of discussed these issues of who's going to be doing data analysis what will be the main I don't know yet you know my group is really nothing but me and of course it's the brilliant postdocs and graduate students who do all the great work but I do have the power to define the overall direction in some sense though I try to give people as much freedom as I can. And I don't know. It's very unclear to me what my level of participation, my group's level of participation will be. It really depends on what looks interesting to me in that time frame. I could well believe that although it's very exciting science coming out and it's the fruition of something that I've worked very hard for for a long time that I will personally find other things more interesting to be working on or I will be put off by the style of work in the field to a degree that I'll choose to work in other areas. It's also conceivable to me I'll be in the thick of the fray and I will be urging people in my group to do nothing else library related work, I don't know we'll see how things go over the next several years, in some sense I'll have to make some degree of decision I have to submit a proposal to NSF for my physics grant this autumn so that I generally not only decide try to decide the character of the research to be done submission time but I also can decide the duration of the grant the last grant which ends one year from now I made it for four years

1:30:00 because it looked to me like four years is about the period of time that my group would need to be deeply involved in data analysis algorithm development in order for that to take off and that about now, when I have to start contemplating the renewal, it would be a reasonable time to be rethinking what the directions. And fortunately, I was pretty much right on with regard to timing. And so over the next six months, I will be trying to make some tentative decisions about the balance of research, research directions for a period yet to be determined, which I'll have to also decide in October, or by October 1, when I need to send the proposal. At the moment, I would guess that I will decide for the period that would be then 99, 2000, 2001. and maybe 2002, which would get me up to where I would have to be proposing about the time the first searches are beginning, that I would make a decision that we might be doing a third data analysis stuff, and a third data analysis stuff, a third stuff on other technical aspects of LIGO, like quantum ion demolition interferometers and the third stuff from NSF physics funding on sources and source simulations. That's quite a contrast from the way it's been the last four years or the last three years where the NSF physics support for the group has been entirely data analysis stuff plus a moderate amount of stuff like QND interferometers and thermal noise baffle design and so forth, with zero component of source, the modest amount of source work has been supported by other, by NSF astronomy. And the big, big support for the ground is NSF physics. I, so that's sort of the direction I'm thinking now, and would imagine that I would totally rethink things about the time the first searches are beginning, and at that point, I will understand much more clearly what it means to work in the field with the

1:32:30 new structures, and I will also have had more opportunity to see what other directions might be interesting to pursue. And so by the time the first searches are beginning, I could wholesale jump in completely, or I could just pull out completely, and I could just as soon when that time comes. It's a luxury I have, and I've maintained, by maintaining my independence, the luxury I have that the experimenters working on LIGO don't have, of being able to make a major change along the way. Do you think it likely that the other questions you might get interested in would be outside the radiation altogether? Oh, I think it's reasonably likely. I could return to issues in close time like curves, issues that touch on quantum gravity. I could wind up pushing hard into quantum information science as outgrowth of quantum non-demolition stuff and of rubbing shoulders with people like Preskill and Carl Caves Jeff Kimmel in the new Science and Technology Center if we get the funding for it. I might decide I want to go write novels. I don't know. Well, I've been asking difficult questions about other people and about the future, so here's a question about both other people and the future. It's sort of awkward. How can I best frame it? so do you think there's likelihood or a possibility that this sort of presumably when gravitational waves strongly is born and we have lots of

1:35:00 going beyond the civil protections to allow more information about new astrophysical entities do you see the people being involved in the analysis what these sources are and how to explain them as being more astrophysical type people I mean will it sort of likely move away from being with the pure I don't know I think so I think it's bound to be the people like Finney and Ladford Martin Rees people of the character of Jerry Ostreicher except I think he's pretty much decided it's going to become a university But real astrophysicists of that sort will be the major players in interpreting what's going on. Just as this community worked strictly on trying to understand optical objects when all we had was optical astronomy, and then they moved as soon as you had radio data. that community started working with radio data and x-ray data they're the ones who really have built up a deep understanding of asterisical processes I think they will play a big role when that time comes with among the people who are currently involved in LIGO, there are only a small number who will be, who have the background to be major players. Ray Weiss, if he's still active, and Stan Wickham, whose roots are actually in infrared astronomy and astrophysics, who is deeply interested in science. And Tom Prince, and likely Ken Liebrecht. But, though Ken, well, and Ken, both Prince and Liebrecht are,

1:37:30 they are experimenters, but they are both also who've done a considerable amount of theory related to astrophysical systems that they've worked on. with the sun, and prints with x-ray sources, largely. And they really have strong connections into the astrophysics community. Barish may learn enough astrophysics to be a major player. I don't know. he learns he's very quick but most of the people who are really working on LIGO I think will not be major players in exploiting the science among the theorists there may be a few who are Sam Finn will surely be some of the people who come from the relativity side side, just never have learned and never will learn enough astrophysical phenomenology to, I think, be major players in exploiting science. They will play the kinds of roles that relativists have often played of developing techniques to solve Einstein's equations and doing rather idealized but complex analyses of relativistic systems to build up understanding of the astrophysicists and then lean back and rely on and then interpreting the data. I think the bulk of the exploitation will be by people like Finney and Laniperd. So within the relativity community gravitational architectures are a great success in which they'll continue to, or these are the ways that we still have a major impact on what relatives do? Well, I think, I mean, there are several areas. Numerical relativity will probably be a major tool for understanding sources.

1:40:00 But there's going to have to be some strong intellectual interaction between the numerical relativists who largely don't talk to each other at the present time. I mean, gutsy after business. and there may well still be need for people who can do high order perturbation theory in understanding waveforms. There are likely to be surprises and the surprises are likely a lot more strong gravity than you've had in conventional astrophysics until now. But I wouldn't be surprised if what happens then is simply that the new generation of conventional astrophysicists just has to learn relativity much more deeply than they do to fully exploit the science that people will have to know a lot more astrophysical phenomenology than all of us generally know. And it could wind up that the people whose roots are in relativity are not the major players, even though a huge amount of relativity is involved. The major players are people in the Blandford Finney type who simply have been forced to learn a lot more relativity than they used to previously have to know, but who have all of this additional knowledge I'm sure all of this generally doesn't get the vast physical biology, but well we'll see. So, from the point of view of younger graduates of the postdocs such as you have here, over, well I suppose it's a a reasonably long time period, let's say 10 years or so you may find that the experimentalists will become more involved in the data analysis side I think that's likely to happen and that the astrophysicists will become much more interested in looking at the kind of relativistic sources I think that's true as well and I suppose of course numerical relativity is likely to become more and more important Are there other arenas in which the people with a background in relativity are allowed to be able to make their niche?

1:42:30 Or will they move off into other areas like quantum gravity? You know, relativity is already largely bifurcated relativity theory into quantum gravity and its ties to particle theory on one hand. astrophysical aspects of relativity, on the other hand. And I think that vibrication is just going to grow stronger and stronger. It's almost not the same community, almost two independent communities by now. And there are very few people who work in both. Yet there are intellectual problems that are common, where there really are astrophysical aspects to it. But by and large, I think there has been, over the last 20 years, a redefinition of the boundaries of fields, the structures of fields, so that you almost should regard quantum gravity as a different field from classical relativity. classical relativity as a subject in and of itself is largely a dead subject there is a very small handful of superb practitioners who are doing interesting things that become foundations for numerical relativity say or for quantum gravity people like some of Ashdakar's work people like Helmut Friedrich and Berk Schmidt, and Jimmy York. There are very few of those. And so if you set them aside, you've got the quantum types, and you've got the astrophysical relevance. LIGO is part and parcel of the astrophysical relativity. And those astrophysical relevance are, in some sense, I think, going to become more and more tied to conventional astrophysics. Those who, and there will be many of them who still identify themselves as relativists who don't know all that much phenomenology but do interesting relevant problems

1:45:00 and relevant to LIGO, and then there will be those who are well enough tied to conventional phenomenology that astrophysicists recognize them as one of their own as I have been at times in my career. and who will be major exploiters of the law of LIGO, I think. But it will be more shades of gradation in a spectrum of relativists like Cliff Will, say, at one end, who I don't know all that much phenomenology, but are superb in doing relevant computations about astrophysical systems to people like Igor Novikov on the other end who know a great deal of relativity and use it but are really closely tied to phenomenology. And quantum gravity is just going to be a separate, really very separate field, I suspect. I think people in your generation, except for having been exposed to quantum gravity, going to Pacific Coast gravity meetings, you don't regard it as the same field as you worked in. No, that's true. Whereas people in my generation do, but I think it's for historical reasons. We just turn on some lights. No, I agree, that's true, yes. You've only encountered, as you say, a PCG. That's something almost a little bit from another part. Yeah. So the numerical relativity people then who, in my person to some extent, are the inheritors of the more classical relativity mantle, would they, you feel, under the impact perhaps of LIGO, some of the things that would be moving more into the astrophysical kind? Related to it or ancillary to it? Yeah, although it's possible that there will be deep issues of principle in relativity to be solved. The work that I heard from people who went to PCGM by Jim Eisenberg and Beverly Berger on understanding the generic singularity structure and basically tentative verifications that the BKL singularity is the structure that you get.

1:47:30 But that kind of thing, I think, is going to become more and more important, or the kind of thing that Matthew Choptuik pioneered of discovering critical behavior in gravitational collapse. There may well be a number of new discoveries that come out in American relativity that revitalize the effort of understanding general relativity itself the subject in and of itself and might could even rejuvenate a classical relativity as a subject independent of astrophysics. We will see what comes out. There are these two examples now that critical behavior and collapse and the study of generic singularities that smell like they might rejuvenate the field as an independent field. But for the moment, I'd say classical relativity as an independent field is almost dead. except for people very influential and very good productive people like York who are having impact their impacts are on are not on other classical relevance, their impacts are on numerical relevance and on people who are working the interfaces with other fields not people who are within the confines relatively Well, I think it's different. I don't have a question for the minute. Thanks very much, Kitna. Well, you've triggered me to think about things that I haven't thought much about for a long time. Okay, good. Well, I hope you enjoyed it, because I have to say I felt guilty after asking all these difficult questions. What do other people think, and what's going to happen in the future? I'm probably way off the mark, but then so is everybody else I expect.