For over two decades we have understood that the likely route to progress in particle physics is to understand how the electroweak symmetry of the Standard Model is broken, in order to accommodate mass in the theory. The electroweak symmetry cannot be broken from within the SM itself, so how it is broken points to how the SM is extended to the next level of our understanding of nature.

To make progress we must have data about the Higgs sector of the theory. We must learn whether there is a light Higgs boson. If there is we must learn how it interacts with fermions and gauge bosons. If there is not a light Higgs boson we must study the interaction of the longitudinal W and Z bosons with each other and with fermions, particularly the top quark, and we must get even better precision data that is sensitive to virtual Higgs sector effects.

What have we learned recently that will help us see how to proceed? From LEP, SLC, Fermilab, rare decays and so on we have discovered two major clues. We might have been lucky and found a Higgs boson or even superpartners, in which case a decision on what facility to build next would not require insight or leadership, but we have not. Fortunately, however, enough has been learned that we can proceed with confidence whatever our view of the underlying physics.

The first thing that has been learned is that a complete description of the Z production and decay data requires a contribution equivalent to that which a virtual Higgs boson of mass less than about 200 GeV would give (the precise numerical value is not important for us). Second, we have learned that no confirmed experiment shows any significant deviation from the SM.

The first of these provides the crucial information that tells us how to proceed. An upper limit does not of course imply that there is a state below the upper limit. But unless one wants to claim that the LEP and SLC data or their analysis are just wrong, it does provide compelling information to those who examine it carefully. Basically it says that if one imagines a space whose axes are the variables describing the precision measurements then one has to be inside a certain region in that space. In a SM analysis, which can be done even if the theory is to be extended because one can translate the results into any framework, all the parameters are measured except the Higgs mass M. One can calculate where the theory ends up in that space for any given value of M, with the result that if M is larger than about 200 GeV one is outside that region. But it could happen that there is a conspiracy and some other kind of physics is also present with just the properties that its contribution moves the theory back into the allowed region. Anyone who says there is not a Higgs boson below about 200 GeV is claiming that there is such a conspiracy.

How far can we go outside the region? There are constraints on what can conspire. The resulting theory must be consistent and unitary, and there must be no observable effects from the added physics elsewhere. That turns out to imply that the largest value for M is about 450 GeV. Thus in this worst case we learn that a lepton collider of total energy at most 600 GeV and sufficient luminosity can find the Higgs state even if it is well above the upper limit of about 200 GeV.

Further, whatever conspires with the heavier Higgs state if there is not simply a light Higgs boson will itself have effects that are detectable either at the lepton collider itself, or at LHC, or with improved precision data from a giga-Z factory, so the combination of these facilities will let us unravel the underlying physics.

Of course the basic planning should be for the most likely situation, which is a light Higgs, rather than for the unlikely worst case. Then an initial collider of 500 GeV will be fine, and allow us to study the Higgs physics thoroughly. Any collider is extendable by 20-30% in energy so if no light Higgs is found the energy can be increased to find the heavier state.

Several features strengthen this conclusion. The conclusion does not depend on them, but one should always examine related information to see if it points the same way as the basic information and in this case it does. One is the second result from the past decade that no deviations from the SM were found. That is what is expected if the origin of the electroweak symmetry breaking is a weakly coupled sector, with a perturbative breaking, rather than a strongly interacting sector. That in turn implies a light Higgs boson, as in supersymmetry. Another is that the supersymmetric extension of the SM explains several significant results, such as the gauge coupling unification and the large top mass, and naturally leads to small deviations from SM since the superpartners only enter is quantum corrections. The point is not that we are relying on supersymmetry, which we are not, but that all that we know reinforces the result that a 500 GeV collider is sufficient to do crucial new physics. When planning for the future of a field we should assume the most likely situation holds rather than betting on an unlikely one. Indeed, some alternative points of view are probably excluded but it is hard to prove they are excluded so they continue to be considered.

Let us examine a number of questions that are sometimes asked about this result and its implications.

** What if nothing is found at all at a lepton collider? It is sometimes argued that that would be fatal for our field, both scientifically and politically.

In fact, if nothing were found the lepton collider would be more crucial than if a light Higgs were found. In the default case with a light Higgs and superpartners the lepton collider will play an essential role in providing data to formulate the basic theory (more below on this). But if the default were wrong the lepton collider would be crucial to learn what nature's actual path was. We must then study the WWW and WWZ and WWgamma vertices for longitudinal W and Z bosons that contain the Higgs sector physics. Such a polarization analysis is extremely difficult at a hadron collider, but entirely feasible at the lepton collider. We must improve the precision measurements at the same time. We know that at sufficient precision the SM must show deviations that can point the way to the correct approach. Further, if no Higgs boson exists below about 190 GeV (to state a safe upper limit) we know that weak scale supersymmetry is not the explanation for electroweak symmetry breaking, and that is huge progress --- disproving a main paradigm is one of the ways science moves forward. In this case it would refocus the work of many people. Not building a 500 GeV linear collider could be far more damaging for our field than building one at which only subtle deviations were found.

** What if only a light Higgs boson were found but no other states, no superpartners and no other Higgs states?

The answer is basically the same as the previous question. Again the lepton collider would be more important than if the default world were found. We must study if the Higgs state is pointlike in its couplings to W,Z, fermions and if it couples proportional to mass. We must check how it couples to up-type and down-type fermions (since the tree level coupling to b's and tau's is the same because they occupy the same place in SU(2) doublets) and that is probably not possible at hadron colliders. We must improve the precision data.

** Why do we need a lepton collider after the LHC has run for some time?

First suppose nothing new is found at all at LHC, or only a light Higgs. Then the answer is as above, the high luminosity lepton collider can make a precision study of the interactions of the longitudinal W,Z states while that is very hard for the hadron collider. The lepton collider may be essential to progress. Or, suppose superpartners are found, and a light Higgs. Then there are three major reasons the lepton collider is needed even long after LHC has run. The first has been well examined in studies: the lepton collider, with polarized beams, can separate the superpartner states and measure their properties well. It can demonstrate what is found is indeed supersymmetry. That is very difficult at LHC.

The second reason is more important, and has not been discussed previously in studies. Experimenters measure masses of mass eigenstates, and differential cross sections times branching ratios. None of these quantities appear in the Lagrangians that theorists study. There is a real barrier between what is measured and what is needed to help formulate the theory--anyone who doubts that has not examined the issue. For example, the important quantity tanß that is essential for almost all supersymmetry predictions cannot in general be measured at a hadron collider. That is because it is related to observables through equations that contain more unknowns than can be independently measured at hadron colliders. (When people discuss measuring it they always make a number of assumptions that need not be true about other parameters, so they are really not talking about a measurement.) But at a lepton collider above the threshold to produce a few superpartners (e.g. the lightest chargino and the two lighter neutralinos and perhaps the light stop) there are additional equations. That is because the cross sections can be measured with polarized beams, effectively doubling the number of equations. And running at two energies almost doubles again the number of equations. In practice it is a little more complicated but the basic point is correct. Thus the lepton collider will be essential to learning what we need to know to formulate the next stage of progress. It will not be enough to know that superpartners exist and to know their masses --- we must learn the pattern of the Lagrangian. To not plan for that would be like never having run LEP for the Standard Model.

The third reason is based on one of the most important possible consequences of supersymmetry, that the lightest superpartner (LSP) may be the cold dark matter (CDM) of the universe. It would be extraordinarily exciting if we could identify in the laboratory the actual particle that constitutes most of the matter of the Universe. To do that requires more than just detecting LSP's. Even if LSP's are observed in both direct detection experiments and at hadron colliders, and their mass accurately measured, one can demonstrate that we can not know if LSP's are indeed the CDM. To learn that it is necessary to actually calculate the LSP relic density. To do that calculation it is necessary to measure tanß and all the relevant parameters. It is impossible to measure those parameters at hadron colliders. A Linear Collider above the threshold for few superpatners can measure the relevant parameters.

** How do we know there will be some superpartners in the energy region of the lepton collider?

We can't be absolutely sure of that until their masses are found, of course,but if supersymmetry is indeed observed (which is given if we are in this branch of the logic) then it is extremely likely that the charginos and neutralinos are light. If they were not the explanation of electroweak symmetry breaking would be very contrived and fine-tuned. So the argument here is not that supersymmetry must exist, but that if it does exist then it probably is the explanation of the electroweak symmetry breaking and then the charginos and neutralinos are probably fairly light. Examination of models implies that it is very likely the masses and cross sections for the first chargino and the first two neutralinos are in the range of a 600 GeV collider, and of course it is even more likely if the energy is higher. That is enough to do the crucial measurements. Within a year it is possible that the g-2 experiment will strengthen this argument.

** Why not wait until superpartners are actually detected before going ahead with a lepton collider?

This is of course a different kind of question from the above. If events take their natural course in the U.S. and if nothing is done in Germany, then as spending winds down on LHC here DoE will approve proceeding with a linear collider, beginning in about 2007, and taking 10 years before producing data. In order to move faster than that some new factor has to enter, such as effective leadership.

Germany is moving ahead. Their Science Council will decide in 2002 whether to proceed with TESLA. Then funding has to be arranged. In the best of situations it could produce data in about 10 years.

Historically, physics has often progressed by the leadership and strength of personality of a few people. We know now that a linear collider of 500 GeV is about as certain to produce powerful science as we can ever know in physics. Technically we could proceed. To do that we would have to agree to state to the world without qualification the remarkable scientific importance of such a collider, as outlined above. Whatever the outcome it will lead to major progress in our search for understanding the laws of nature. If we proceed now in a single minded manner, we could have a collider start taking data in perhaps 9 years.

Can we afford that? These are not zero-sum games. For nearly a decade we have not been definitive and clear about what the field needed. Of course we do not get better funding. If we state clearly what we want and why, we can get more funding. It is essential to run the Tevatron at high luminosity because superpartners and a Higgs boson may be found there and their study begun. That will focus theoretical and experimental activities and greatly increase our progress. We must run the b-factory to study CP violation and rare decays, which can contribute in an essential way to untangling the basic theory. We must pursue neutrino mass studies, search for dark matter, and study rare decays and rare processes. If we state strongly what is important and why, we may get it. If we don't we will know we were turned down instead of not even trying as hard as possible. We have repeatedly been told by people experienced in government funding, and by people in other successful fields of science, that we need to decide what we want and say so --- if we don't we surely will not get it. We could have gone ahead with a linear collider some time ago. We should do it now.

Gordy Kane