Last time this blog was active, particle physics was entering a sharp curve. That the infamous 750 GeV resonance had petered out was not a big deal in itself - one expects these things to happen every now and then. But the lack of any new physics at the LHC when it had already collected a significant chunk of data was a reason to worry. We know that we don't know everything yet about the fundamental interactions, and that there is a deeper layer of reality that needs to be uncovered (at least to explain dark matter, neutrino masses, baryogenesis, inflation, and physics at energies above the Planck scale). For a hundred years, increasing the energy of particle collisions has been the best way to increase our understanding of the basic constituents of nature. However, with nothing at the LHC and the next higher energy collider decades away, a feeling was growing that the progress might stall.In this respect, nothing much has changed during the time when the blog was dormant, except that these sentiments are now firmly established. Crisis is no longer a whispered word, but it's openly discussed in corridors, on blogs , on arXiv , and in color magazines . The clear message from the LHC is that the dominant paradigms about the physics at the weak scale were completely misguided. The Standard Model seems to be a perfect effective theory at least up to a few TeV, and there is no indication at what energy scale new particles have to show up. While everyone goes through the five stages of grief at their own pace, my impression is that most are already well past the denial. The open question is what should be the next steps to make sure that exploration of fundamental interactions will not halt.One possible reaction to a crisis is. Historically, such an approach has often been efficient, for example it worked for a long time in the case of the Soviet economy. In our case one could easily go on with more models, more epicycles, more parameter space, more speculations. But the driving force for all these SusyWarpedCompositeStringBlackHairyHole enterprise has always been the (small but still) possibility of being vindicated by the LHC. Without serious prospects of experimental verification, model building is reduced to intellectual gymnastics that can hardly stir imagination. Thus the business-as-usual is not an option in the long run: it couldn't elicit any enthusiasm among the physicists or the public, it wouldn't attract new bright students, and thus it would be a straight path to irrelevance.So, particle physics has to change. On the experimental side we will inevitably see, just for economical reasons, less focus on high-energy colliders and more on smaller experiments. Theoretical particle physics will also have to evolve to remain relevant. Certainly, the emphasis needs to be shifted away from empty speculations in favor of more solid research. I don't pretend to know all the answers or have a clear vision of the optimal strategy, but I seepromising directions.One is astrophysics where there are much better prospects of experimental progress. The cosmos is a natural collider that is constantly testing fundamental interactions independently of current fashions or funding agencies. This gives us an opportunity to learn more about dark matter and neutrinos, and also about various hypothetical particles like axions or milli-charged matter. The most recent story of the 21cm absorption signal shows that there are still treasure troves of data waiting for us out there. Moreover, new observational windows keep opening up, as recently illustrated by the nascent gravitational wave astronomy. This avenue is of course a non-brainer, already explored since a long time by particle theorists, but I expect it will further gain in importance in the coming years.Another direction is precision physics. This, also, has been an integral part of particle physics research for quite some time, but it should grow in relevance. The point is that one can probe very heavy particles, often beyond the reach of present colliders, by precisely measuring low-energy observables. In the most spectacular example, studying proton decay may give insight into new particles with masses of order 10^16 GeV - unlikely to be ever attainable directly. There is a whole array of observables that can probe new physics well beyond the direct LHC reach: a myriad of rare flavor processes, electric dipole moments of the electron and neutron, atomic parity violation, neutrino scattering, and so on. This road may be long and tedious but it is bound to succeed: at some point some experiment somewhere must observe a phenomenon that does not fit into the Standard Model. If we're very lucky, it may be that the anomalies currently observed by the LHCb in certain rare B-meson decays are already the first harbingers of a breakdown of the Standard Model at higher energies.Finally, I should mention formal theoretical developments. The naturalness problem of the cosmological constant and of the Higgs mass may suggest some fundamental misunderstanding of quantum field theory on our part. Perhaps this should not be too surprising. In many ways we have reached an amazing proficiency in QFT when applied to certain precision observables or even to LHC processes. Yet at the same time QFT is often used and taught in the same way as magic in Hogwarts: mechanically, blindly following prescriptions from old dusty books, without a deeper understanding of the sense and meaning. Recent years have seen a brisk development of alternative approaches: a revival of the old S-matrix techniques, new amplitude calculation methods based on recursion relations, but also complete reformulations of the QFT basics demoting the sacred cows like fields, Lagrangians, and gauge symmetry. Theory alone rarely leads to progress, but it may help to make more sense of the data we already have. Could better understanding or complete reformulating of QFT bring new answers to the old questions? I think that is not impossible.All in all, there are good reasons to worry, but also tons of new data in store and lots of fascinating questions to answer. How will the B-meson anomalies pan out? What shall we do after we hit the neutrino floor? Will the 21cm observations allow us to understand what dark matter is? Will China build a 100 TeV collider? Or maybe a radio telescope on the Moon instead? Are experimentalists still needed now that we have machine learning? How will physics change with the centre of gravity moving to Asia? I will tell you my take on such and other questions and highlight old and new ideas that could help us understand the nature better. Let's see how far I'll get this time ;)