Neutrino physics is in the midst of a discovery phase and further progress is guaranteed in the next years if the possible experimental program is pursued. However, many proposed new experiments are expensive and therefore it is highly desirable to coordinate the world wide effort. Such a coordination (or 'road map') is clearly based on current results and understanding, but one should also keep in mind that long term plans may change more or less drastically due to unexpected results. Neutrinos are unique probes of various different physical systems which can be categorized by the sources. Among the sources are the sun, the atmosphere, supernovae, astrophysics, cosmology, the earth, reactors and beams. Neutrinos allow interesting insights into each of these sources which should not be forgotten in a road map. The common denominator of neutrino physics is, however, particle physics and here especially the key question for neutrino masses. There exist in principle four different ways to search for neutrino masses. First neutrino masses may be detected via energy-momentum conservation in the decay kinematics (tritium decay). From a theoretical perspective, Majorana-neutrino masses are considered as the most natural possibility. The second method to detect neutrino masses is therefore to look for the lepton number violating processes which exist for Majorana masses. The third method is to limit (or detect) neutrino masses from their gravitational impact on cosmological structure formation. The last (and in recent years most successful) method is neutrino oscillations. I will limit myself for the rest to the optimization of future neutrino oscillation experiments. This does not mean that other mass determinations or other physics with neutrinos should not be pursued. My attitude is that these other directions are equally important and that they should receive adequate funding in a balanced way. Another aspect which should be kept in mind is that quite frequently neutrino oscillation experiments allow to study other aspects, which adds a certain extra value. Examples are geo-neutrinos in reactor experiments or searches for proton decay in large megaton underground detectors. My discussion of the neutrino oscillation road map assumes that the involved laboratories and research communities are willing to compromise, since the total optimization is not always identical with the optimization from the short term or political perspective of certain laboratories. Such a global optimization aims for synergies between different measurements. At the same time I am convinced that a certain amount of balancing between laboratories and/or regions has to be done, since this is the only way to maintain a health research environment, which includes especially the training of a next generation of physicists. The next main issue is time scales. There exists an impressive set of ideas for new experiments with different levels of sophistication and corresponding technological challenges. Put in positive terms, it implies a healthy and fruitful future for this field with exciting new results. One the other side it is obvious that the resources will be limited. Optimization is therefore mostly the question which project can or should be pursued when and where in a scientifically competitive way, maintaing at the same time a healthy structural balance between the regions. To structure the discussion about time scales it is useful to group the projects into categories: There are 'current projects', i.e. experiments which are already operating or under construction. For these it is obvious that we have to make sure that these projects fulfill their objectives. This sounds trivial, but one should not forget the possibility that some of these current projects encounter technological problems or delays. Assuming that the current generation of experiments fulfills its objectives it makes sense to identify the 'next generation', i.e. those projects which could in principle be built in a few years. JHF-Superkamiokande (now called JPARC) is certainly the most advanced project in this category of future off-axis experiments. The NuMI off-axis project is another experiment of that category. Next a new reactor experiment with a near and a far detector is the third type of experiment which should be included in this discussion. Such a reactor experiment is very important if it works as anticipated. The point is that it could perform a clean (uncorrelated) theta_13 measurement maybe down to values of sin^2 2 theta_13 = 0.01 with reactor anti-neutrinos. The off-axis experiments have a similar or even better over-all precision, but theta_13 is in this case correlated to other parameters, including the leptonic CP phase delta. In the worst case one could cancellations, such that no nu_mu -> nu_e transition is observed in the off-axis experiments, even though theta_13 is finite. A reactor experiment would thus be very valuable, since it would detect in a clean way a finite theta_13 value. Detecting a finite value with a reactor experiment might even allow to set first limits on the leptonic CP-phase in combination with the off-axis experiments. A reactor experiment would also influence the running strategy of the beam experiments, since they would provide at a fraction of the cost anti-neutrino information, allowing the beam experiments to run (at least initially) full time in neutrino mode (larger cross-section) and to collect as much statistics as possible. The objective of the next generation is in any case to establish a finite value of theta_13 down to sin^2 2 theta_13 = 0.01. A value of theta_13 above this value would be the ideal basis for further projects with the aim to measure leptonic CP-violation. There is thus an excellent physics motivation for this next generation. However, it is important to keep in mind that the above projects and the corresponding physics programs are not yet secured. Besides the funding issues it is important to understand the background issues of new reactor experiments to see if the desired sensitivity can be reached. Beyond this next generation is a promising 'next to next generation' of potential oscillation experiments. Given the time scales and the required R&D it is very important to think of this next to next generation, but it is not trivial to know precisely what has been achieved by then. Assuming that the next generation works as anticipated, there are different interesting options, like JHF-HyperKamiokande or a new megaton detector in the Frejus tunnel combined with a SPL at CERN. All these projects require further R&D and the right attitude is to work towards these experiments, but a final decision can only be made when the physics case is clearer and when the technological issues are better known. These projects appear in principle feasible and they have often other physics objectives, but they are more expensive than the next generation. They require therefore probably a consensus on a larger scale. Beyond that there are further projects, like a beta-beam or ultimately a neutrino factory. A neutrino factory is in some sense the ultimate goal, since it would allow very precise measurements of neutrino properties. There are clearly a number of points where significant R&D is required before one can realistically decide if and when a neutrino factory can be built. One nice aspect of the outlined program is that every stage offers an interesting physics program, while the technological steps fit to a large part nicely into the required R&D work for the next generation. In summary, I think that there are two main aspects which have to be considered now. The first priority should be to secure the next generation of oscillation experiments. Ideally it would make sense to have JHF-SuperKamiokande (JPARC), NuMI off-axis and a reactor experiment. If we have to live with less, then a synergy discussion shows that one off-axis experiment in combination with a reactor experiment would be most desirable. The second, but for the future equally important, priority is a strong R&D program for the next to next generation. The aim should be to have such experiments ready for final approval within something like 5 years. Parallel to that a strong R&D program should also be maintained for the projects with longer time scales, since projects on shorter time scales will also benefit from that. A strong R&D program is also important since it may change our road map. An example is given by the reactor experiments discussed above, which change the optimal strategy for the next generation. A final important aspect has to do with the other fields of particle physics, natural sciences in a larger context and with our societies. For a number of reasons particle physics as a whole is loosing ground in the supporting industrialized countries. This stems partly from changes in the political and socio-economical conditions. The other main component is the lack of spectacular discoveries of the whole field. Neutrino physics is here a very positive exemption, but its funding depends to a large extend on the funding level of all of particle physics. The funding for neutrino physics competes here with other well motivated, but even more expensive projects in particle physics. Especially the construction of the Large Hadron Collider (LHC) in combination with the world wide effort to build a linear collider have to be mentioned here. These projects address very important physics questions, but their combined funding would absorb a very big portion of (or even exceed) the resources which are available world wide for particle physics. The slow linear collider decision process has moreover in a number of ways a negative impact on the described neutrino program. I would find it very desirable and important if different interesting directions could be balanced in a better way.