Of course there has been magnificent progress, such as the discovery of the Higgs using the Large Hadron Collider. But this success has had a peculiar reverse effect on the morale of our community, what if the community cannot top this accomplishment?  Compare this reverse morale effect in particle physics with the great boost given to morale in cosmology  by the discovery of the dark energy phenomenon.

At the practical level, there is the serious worry that our governments are not willing to fund major new particle physics, such as a very high energy linear electron-positron collider, or if feasible, a circular muon-muon collider. The next very high energy facility will not be built within the next decade, perhaps not within the next two decades. The remaining working lifetime of older physicists, such yours truly, is a few decades.

References to, and discussions of, these worries are recounted in Peter Woit’s fine blog “Not Even Wrong”, posted on January 14, 2013. Incidentally, I first learned from Peter’s blog of the CERN Briefing Book, a most useful compendium of high energy physics information.

The worries of middle age and older particle physicists as to will we learn anything new before we die, leads to what I call if only  particle physics theories. These if only theories could be tested if only experimenters and observers had instruments not presently existing. These instruments not existing at present because of the expense or more likely we don’t know how to build these instruments or even more likely we cannot even conceive of these instruments.

A splendid example is the problem of building an instrument to detect individual, zero mass, gravitons – first discussed by Dyson in the New York Review of Books, May 13 issue (2004). Rothman and Boughn have treated this problem in more detail [Found.  Phys. 36, 1801-1825 (2006)]. Their abstract reads in part: Freeman Dyson has questioned whether any conceivable experiment in the real universe can detect a single graviton. If not, is it meaningful to talk about gravitons as physical entities? We attempt to answer Dyson’s question and find it is possible concoct an idealized thought experiment capable of detecting one graviton; however, when anything remotely resembling realistic physics is taken into account, detection becomes impossible.

The Fundamental Physics Prize Award

I see the worries of middle-aged and older particle physicists, particularly theorists, as a major cause of the spectacular rise in prestige of the Fundamental Physics Prize Award.  These honors are awarded by the Fundamental Physics Prize Foundation. The monetary size of this prize can be as large as three times the Nobel Prize. About a dozen Fundamental Physics Prizes have been distributed by the Foundation as well some number of prizes of lesser monetary value.

The conditions for receiving the Fundamental Physics Prize differ in one fundamental way from the conditions for receiving the Nobel Prize. The physics work leading to the  award of the Fundamental Physics Prize must be advanced, fundamental, penetrating and exciting as is generally  required for the Nobel Prize; but the work need not be proven correct by experiment or observation. Citations for awarded Fundamental Physics Prize include work on string theory, large dimensions, and multiuniverses. The Fundamental Physics Prize does not apply the iron rule of the Nobel Prize – prove the work is correct in the natural world by experiment or observation. Only one awarded Fundamental Physics Prize fits the iron rule – the discovery of the Higgs boson.

My experience in physics leads me to want the iron rule to be applied to all research based prizes in science. In the 1960s the Regge theory of strong interactions with its trajectories, poles and cuts would have been a candidate for the Fundamental Physics Prize. Proton-proton and pion-proton elastic scattering partially validated Regge theory. Some of these experiments were carried out by C. C. Ting, L. Jones and I in the 1960s [Phys. Rev. Lett. 9, 468–471 (1962)] using optical spark chambers at the Bevatron.  A bit of particle physics nostalgia here: the experiment required the three of us and a marvelous  mechanic, Orman Hays; and the data was acquired in a few weeks. But now we know that QCD, not Regge theory, is the fundamental theory for strong interactions. The iron rule must be applied with patience as well as severity.

Physics for a New Century: Papers Presented at the 1904 St. Louis Congress of Arts and Science

I recently found a volume of physics papers from the week-long 1904 St. Louis Congress of Arts and Science. Hundreds of talks were presented covering the intellectual achievements of nineteenth century in all fields of the arts and sciences. About a dozen papers on physics were given by Boltzmann, Langevin, Kimball, Newcomb, Ostwald, Poincare, and Rutherford, and lesser known physicists. These papers have been assembled by Katherine Sopka into Volume 5 of the History of Modern Physics (American Inst. Phys., Tomash Publishers, 1986).

A paper by C. Barus of Brown University summarizes nineteenth century progress in physics   in the time-honored classical classifications of dynamics, heat, light and optics. Other papers introduce the emerging areas of alpha rays, beta rays, gamma rays, X-ray, radioactivity, the theories of the electron, and pre-Einstein relativity. Nineteenth century progress in physics was tremendous.

However there were substantial theoretical and conceptual mistakes in nineteenth century  physics. There was Lord Kelvin‘s vortex theory of atoms, there were the arguments of the Energeticists such as Ostwald against the kinetic theory of gases, and of course the mechanical models of the ether. If the Fundamental Physics Prize had been available in the nineteenth century, some of these mistakes would have received the Prize. It took half a century or more to correct these mistakes.

The time scale for physics progress is a century not a decade. There are no decade scale solutions to worries about the rate of progress of fundamental physics knowledge.  My advice is (a) study calculus and machine shop in high school and (b) have a long life as advised in the old song by buttoning up your overcoat and eating an apple every day.

On the hand, occasional scanning of the obituaries in the New York Times indicates that financiers live longer than physicists, so perhaps start a hedge fund in high school.

The nature of creativity in physics, other sciences and engineering has always fascinated me. This essay contains my observations on some aspects of creativity: the constraints on creativity in science and engineering, what helps creativity, the unavoidable occurrence of bad ideas, helpful and not helpful colleagues, the art of obsession in research, and new technology. In this essay I include examples in other sciences and engineering.

What are your thoughts  on creativity in science and engineering?

Constraints on Creativity in Science and Engineering

Creativity is sought everywhere: in the arts, business, mathematics, as well as in science and engineering. Common elements of creativity are originality and imagination. Creativity is intertwined with the freedom to design, to invent and to dream. In engineering and science a creative idea is useful only if it meets three conditions: the constraint of the natural laws, the constraint of cost, and the constraint of technical feasibility.

The Constraint of Natural Laws

A creative idea in science or engineering must conform to the natural laws. An inventor who thinks that she or he knows how to violate these laws will have to disprove a vast amount of previous experiments and accepted theory. The burden is particularly tremendous on a scientist to prove the violation of a known law. This is illustrated by the present debate about the correctness of the finding by the OPERA Collaboration that neutrinos can travel faster than light. [Reflections on Physics, Oct. 29, 2011 posting]

Of course the temptation and the dilemma for the researcher is that the highest form of creativity is proving a violation of a known law.

The Constraint of Cost

Cost constraint is obvious whether the creative idea requires a new experiment or new technology. It is obvious in the industrial and commercial and military world when the new idea is a new device or a new process. Sometimes the cost cannot be clearly determined, particularly if the implementation takes many years. An example is the implementation of practical and cost competitive power from nuclear fusion, either the magnetic confinement method or the inertial confinement method. There are many creative ideas in the field of fusion power but the final costs are not known.

The Constraint of Feasible Technology

The implementation of creative ideas requires the existence of feasible technology or the ability to develop the required technology. An example of an idea that is certainly creative, but does not have a feasible technology is the nuclear powered X-ray laser first proposed by Edward Teller.

To Be Creative

Here are some qualities that I believe are needed to be creative in science and engineering.

Competency in Mathematics

You don’t have to be a mathematical genius. There are fields where mathematics is secondary. Nonetheless, it is good to be competent in mathematics.

Visualization

In engineering and scientific work it is crucial to be able to visualize how the work can be accomplished. The intended work might be the invention of a mechanical or electronic device, the synthesis of a complicated molecule, the design of an experiment to evaluate the efficacy of a new drug, or the modeling of how proteins fold and unfold.

Different kinds of work require different kinds of visualization. Spread sheets or flow charts may work best in some cases. Drawings might be more suitable in others. Whatever the project, the value of visualization is in finding the best way to proceed while avoiding mistakes and perhaps even finding alternative solutions or interesting related ideas. Visualization is crucial for creativity in engineering and science!

Imagination

Imagination is another crucial ability required to be creative in engineering and science. Begin with the far reaches of your imagination at the science fiction level, then gradually apply constraints such as known physical laws, observation, experimentation, feasibility and practicality.

Evaluate Your Skills – Pure and Applied Experimental Research

Evaluate the extent of your experimental skills to find the areas in which you can be creative. Are you good at working with tools, at building equipment, at running equipment – electronics, microscopes, telescopes…? This is my strength. I am an experimenter in physics because I like to work on equipment, am mechanically handy and get great pleasure when an experiment works. But hands-on skills do not have to be your strength. Isidor Rabi, my doctoral research supervisor at Columbia University in the 1950’s, had little laboratory skill. Yet Rabi won a Nobel Prize for advancing experimental atomic physics by inspiring and depending on his colleagues and students.

Evaluate Your Skills – Theoretical Research

I have not done theoretical work and I know nothing directly about the criteria for success. I would value readers comments on this subject greatly.

Getting Good Ideas

Imagination and obsession

Imagination and obsession are the keys to getting a good idea. To help your imagination keep your eyes and ears open. Avoid the “not invented here prejudice”. Remember you can learn from many different people and fields.

When we were looking for fractional charge particles in meteoritic materials, we used colloidal suspensions of the finely ground meteorite, a mixture of mineral and metal powders. We learned how to make such suspensions not from the theory of colloids but from the technology of gasoline engine lubrication; engine oil must suspend mineral and metal powders until the filter is reached. [http://arxiv.org/abs/hep-ex/0204003]

Expect Bad Ideas

For every good idea, expect to have five, ten, twenty wrong or useless ideas. You cannot avoid the bad ideas if you keep your imagination free. There is no spam filter for bad ideas. Even great engineers and scientists have bad ideas as well as good ideas. Nikola Tesla was the inventor of alternating current technology and a pioneer in the development of wireless. For his time he knew a great deal about electromagnetic waves. Yet he thought that substantial amounts of electromagnetic energy could be transmitted around the world by ordinary low frequency radio waves.

Sorting Out Good & Bad Ideas

You may turn a bad idea into a good idea — don’t kill the bad idea prematurely. A bad idea can evolve into a good idea.

Find Colleagues Who are Smart  and Know Other Fields

I always look for colleagues who are smart, and who know a lot in many fields. The obvious advantage is that she or he may be able to solve the problem that has produced trouble in your work. Also smart and knowledgeable colleagues can save you time, and are interesting and inspiring!

Avoid Colleagues Who Tend to be Dismissive of New Ideas

The best colleagues are those who will think about your ideas, who will talk with you and offer insight, constructive criticism. No one needs to be crushed for having a new idea.

Obsession

When you are imagining and visualizing an idea that you expect to be fruitful it is important to be obsessed with the idea. Think about the idea as much as possible—even to the extent of neglecting friends and family. Obsession, immersing yourself in the problem, will enable you to focus and thoroughly explore all the aspects of the idea: what has been done on related ideas, compatibility with physical laws and mathematics and logic, feasibility, practicality, extensions, variations.

But, if in the course of the work you find that you have run out of money, someone else has a better idea, or your idea has a serious flaw give up the obsession immediately and move on.

Technology

The new idea may use old technology or require new technology or the new idea itself may be technological. In any case you must be interested in – perhaps even enchanted by – some of the technology. Then the bad days are not so bad. Another advantage of being enchanted by your technology is that you will be more likely to think of improvements and variations. You should be fond of the technology but not so much in love that you are blind to the possibility that there may be better technology. In many cases your selection and use of the technology will determine your success. Pay a great deal of attention to technology.

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Examples: I start with a simple example. Recall that our Universe started with the Big Bang and the observations that it is 13.7 billion years old and has a visible radius of 5 x 10¹⁰ light years. Our presently accepted view is that space is approximately flat and infinite in extent. We think of our Universe as occupying all of space.

But suppose that our Universe does not occupy all of space.  Then there could be a second Universe in another part of space. Of course the mathematical-physical description of space containing two universes would have to be different and more complicated than the general relativity description of our Universe. The ultimate question for an astronomical observer in one universe is whether evidence can be found for the existence of the second universe.

Now we can add variations. We can suppose that there are many universes. We can suppose that since space is infinite in extent, that universes are being created all the time, and there is always room for more. Going further there is no need to suppose that the physical constants in the different universes are the same, the charge of the electron or the velocity of light might be different. And further still, the physical laws might themselves be different, no Maxwell’s equation, no quarks in a neighboring universe. This raises the thought that two universes could coincide but not be able to detect each other.

Some References: In the large literature on multiple universes I have some specific recommendations. Max Tegmark [arXiv:0905.1283] presents a fascinating and intriguing classification of different  levels of universes. Leonard Susskind in his book The Cosmic Landscape [Little, Brown and Company, New York, 2005] discusses multiple universes from the string theory viewpoint and also argues against various teleological and “intelligent design” theses that have permeated this subject. Andre Linde, a leader in multiverse theory, has a website [http://www.stanford.edu/~alinde/]. The term multiverse is often used to denote a world containing many universes.

On the other hand, for an example of withering criticisms of multiple universe ideas, see one of my favorite blogs Not Even Wrong written by Peter Woit. See for example his Nov. 28 posting [http://www.math.columbia.edu/~woit/wordpress].

Finally, an historical overview of multiple universes and much else is given in the excellent book Higher Speculations by Helge Kragh [Oxford University Press, New York, 2011]. The Amazon price for the book is $48 and it is well worth it. Higher Speculations has been reviewed in the July 8, 2011 posting of Not Even Wrong.

Much Interest and Sophisticated Work: In part of the professional physics and astronomy communities there is much interest in, and sophisticated theoretical work on, multiple universes; in spite of the usually acknowledged impossibility of experimenters and observers testing most of these theories. Indeed it is a long tradition in the science world to develop explanations and world views that go beyond the possibility of experimental or observational verification. A nice example of a theory that could not be verified is the Victorian model of vortex atoms as described in chapter 2 of Higher Speculations. In this speculative model, the vortexes were supposed to occur in a universal fluid, perhaps the ether. But neither the universal fluid or its vortices had been discovered.

Unlike many experimenter and theoretical colleagues I am not bothered by the nature of the professional work on multiple universes, and as a professional physicist I am not concerned whether it is called physics or metaphysics or philosophy or mathematics.

The Public: There are concerns by some scientists and educators about the impact on the interested public of multiple universe theory as presented in popular science books, websites and television. Does this public distinguish between the validity of theories requiring verification by experiment or observation and the validity of theories being based on their beauty or their mathematical perfection? And how does one know the boundary between the work of the professional physicist and the work of the crank and quack physicists? Of course, some of the public following physics and astronomy understand the two different types of validity and can detect crank and quack physics, but not everyone.

I do not believe that the research and teaching communities can do anything about this. We are a small part of an enormous media world permeated by astrology and homeopathic medicine and psychic phenomenon and creationism and claims for infinite amounts of energy available from the quantum mechanical zero-point energy of the vacuum. (See the Wikipedia article entitled Zero-point energy.)

The public interest in multiple universe ideas is that the ideas are often fascinating and spectacular. The development and exposition of new ideas can move quickly, particularly with the use of the Internet. Contrast this situation with the pace of extraction of experimental results from the Large Hadron Collider (LHC). A powerful, beautiful proton-proton collider giving the highest energy collisions ever obtained, powerful experimental groups with wonderful particle physics detectors, yet Nature holds its secrets closely.

Experimental and Observational Research

My training and my research over the years leads me to restrict scientific reality to ideas, models, laws, and theories that have been confirmed by experimental or observation research. The multiple universe world does not meet my criterion for scientific reality. But I like to think occasionally about multiple universes as a way of stimulating my search for new research technology ideas. Will a new technology be found for searching for evidence for multiple universes? Of course I don’t know what it would be, but I don’t see this technology goal as surely hopeless.

An example of a search for effects of a multiple universe model is the paper First Observational Tests of Eternal Inflation by S. M. Feeney et al [arXiv:1012.1995v3]. They find no evidence for the existence or non-existence of a particular type of multiple universe proposed by Linde. It is interesting to look at their search method, looking for anomalies such unexpected symmetries and boundaries in WMAP data. This search used existing technology for studying the cosmic microwave background.

I end this blog with a fable. It is 1910 and the mass, charge and low energy behavior of the electron has been elucidated. A kindly twenty first century physicist sends back a message though time – congratulations on the electron and by the way there is a particle related to the electron that has zero charge and a much smaller mass, we call it an electron neutrino. But the 1910 physicists cannot do anything about this kindly hint, the message is incomprehensible. The technology to look for the neutrino did not exist.

It was not until the early 1950s that Clive Cowan and Fredrick Reines detected reactor neutrinos. [Wikipedia Cowan–Reines neutrino experiment.]

The Current Situation in High-Energy Physics

After wandering in the speculative physics of multiple universes I end this blog recommending the summary talk  of Michael Peskin at the 2011 Lepton-Photon conference [arxiv.org/abs/arXiv:1110.3805]. He gives his perspective on the current situation in high-energy physics.

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As has been publicized everywhere, in newspapers, in blogs and via scientific electronic publishing, on September 23, 2011 researchers from the OPERA experiment announced the astonishing possibility that muon neutrinos may acquire velocities larger than c, the velocity of light. [arXiv:1109.4897v1]

The layout of the OPERA experiment.

The production of the muon neutrino beam at CERN [arXiv:1109.4897v1]

The OPERA detector in the underground Gran Sasso Laboratory.

Their abstract summarizes the experiment and result simply.“The OPERA neutrino experiment at the underground Gran Sasso Laboratory has measured the velocity of neutrinos from the CERN CNGS beam over a baseline of about 730 km with much higher accuracy than previous studies conducted with accelerator neutrinos. The measurement is based on high statistics data taken by OPERA in the years 2009, 2010 and 2011. Dedicated upgrades of the CNGS timing system and of the OPERA detector, as well as a high precision geodesy campaign for the measurement of the neutrino baseline, allowed reaching comparable systematic and statistical accuracies. An early arrival time of CNGS muon neutrinos with respect to the one computed assuming the speed of light in vacuum of (60.7 ± 6.9 (stat.) ± 7.4 (sys.)) ns was measured. This anomaly corresponds to a relative difference of the muon neutrino velocity with respect to the speed of light (v-c)/c = (2.48 ± 0.28 (stat.) ±0.30 (sys.)) ×10-5.”

Incidentally, I have a soft spot in my heart for this experiment because its first purpose was to detect the oscillation of muon neutrinos into tau neutrinos. This has been accomplished. [arXiv:1107.2594]

The OPERA paper also summarizes previous measurements of neutrino velocity. “With a baseline analogous to that of OPERA but at lower neutrino energies (Eν peaking at ~3 GeV with a tail extending above 100 GeV), the MINOS experiment reported a measurement of (v-c)/c = 5.1 ± 2.9×10-5 [MINOS Collaboration, P. Adamson at al., Phys. Rev. D 76 (2007) 072005.]. At much lower energy, in the 10 MeV range, a stringent limit of |v-c|/c < 2×10-9 was set by the observation of (anti) neutrinos emitted by the SN1987A supernova [K. Hirata et al., Phys. Rev. Lett. 58 (1987) 1490; R. M. Bionta et al., Phys. Rev. Lett. 58 (1987) 1494; M. J. Longo, Phys. Rev. D 36 (1987) 3276].

Since then there have been a great number of papers and blog comments on the result. Some recent papers take this result as new physics and connect it with known or speculative phenomena such as : violation of Lorentz invariance, dark energy, dark sector neutrinos and so forth. Other papers present arguments against the possibility of the measurement being correct, for example “New Constraints on Neutrino Velocities” by Cohen and Glashow, arXiv:1109.6562v1.

Some blog comments present analysis showing where the OPERA experimenters may have made a mistake. But the result is statistically strong and if the conclusion is wrong it must be due to an error or errors in the experimental method: perhaps in the timing measurement method or in determining the 730 km baseline. My experience is that it is often difficult for outside researchers to find errors in a well designed experiment exhaustively studied by the inside experimenters. One example of a possible error pointed out by an outsider is a special relativity correction to the GPS timing, discussed by van Elburg [arXiv:1110.2685v2]. Another problem in finding errors in the research results of others is that sometimes the suspicious result comes from a number of errors.

My piecemeal and anecdotal survey of opinion in the physics community is that the consensus of interested physicists is that the OPERA result is mistaken, there is no consensus as to where the mistake or mistakes lie. But as my Ph.D. advisor, Isadore Rabi, said “Physics is an experimental science”. The great number of papers on the internet do not replace more experiments.

However as of this posting, October 29, 2011, we have only one additional experimental result, that from the ICARUS experiment. [arXiv:1110.3763]. The ICARUS experiment is a large liquid argon Time Projection Chamber in the Gran Sasso Laboratories that sits in the same muon neutrino beam as OPERA. The ICARUS experiment measures the energy of neutrinos that interact in the liquid argon and also records a ‘picture’ of the interaction. It does not measure the travel time of the neutrino from CERN. If one applies the theoretical deductions of Cohen and Glashow to the ICARUS results there are no faster-than-light neutrinos in the beam. A strong but indirect argument against the OPERA result.

We would all like to see a speedy settlement of the question- is the OPERA result correct? How rapidly can the question be settled? What about the OPERA experimenters repeating their experiment. Since the statistical situation is so strong, a repeat would have to involve physical changes in the apparatus. For example a large change in the mean neutrino energy or a different neutrino detector timing system or a major change in the neutrino beam. It will take time for the OPERA experimenters to make such changes and study the
results,  even if the actual new running time is short. Probably a month or more. We should be patient.

An obvious settlement path is repeating the experiment using the other long baseline neutrino apparatus, MINOS [The MINOS Experiment and NuMI Beamline] with a 734 km baseline and T2K with a 300 km baseline. The MINOS experimenters at Fermilab have discussed two directions for doing this. One direction is to go through old data trying to improve the timing information . This is worth doing but I am skeptical as to how much clarity this will provide. The other MINOS direction is to upgrade their timing system and take new data. But this will take of the order of a years or more. The experiment must be carried out, the data analyzed and the MINOS experimenters be sure they are right.

The T2K experiment [arXiv:1106.1238v2] in Japan can also look at old data and upgrade their timing and detection systems for their next runs. The latter direction will also take a year or more.

Thus we are in the midst of a dichotomy between (a) the short times- hours to days- required for us to think and calculate and then to report on the Internet and (b) the long times-years- required to carry out an experiment, analyze it, and be sure the result is right. The Internet gives us the illusion of speed in physics research.

It would be marvelous if the OPERA physicists in the end are correct. Their result would produce a revolution in our understanding of the relativistic world, equal to the revolution produced by quantum mechanics in the classical world. If the result is wrong then the superluminal muon neutrino concept will fade away. The fading process will be similar to what happened to the gravitational fifth force experiments and theories of the late 1980’s [E. Fischbach and C. Talmadge, Nature 356, 207 (1992)], the excitement, the puzzles, the mistakes to be remembered by old-timers such as myself. An odd sidelight is that a recent paper by Dvali and Vikman [arXiv:1109.5685v1] discusses superluminal neutrinos in connection with a gravitational fifth force.

November 20, 2011 Update

The OPERA experimenters  have submitted their paper “Measurement of the neutrino velocity with the OPERA detector in the CNGS beam” to the on-line, referred Journal of High Energy Physics (JHEP). The conclusion remains about the  same,  relative difference of the muon neutrino velocity with respect to the speed of light (v-c)/c = (2.37 ± 0.32 (stat.) +0.34 (sys.) -0.24(sys) ×10-5. There is an important addition: the results of of a small data, low proton beam  intensity run show that the beam time structure is understood. This new paper is   arXiv:1109.4897v2.

This new paper and its submission to a referred journal appears to have changed few minds, most concerned physicists remain skeptical. But I am puzzled, the very experienced and competent OPERA experimenters have had time to consider the dozens of suggestions, mostly on blogs, as to why the results are wrong; suggestions ranging from GPS problems to timing problems to relativity problems.  There are  numerous comments that the next step is to wait for results from other experiments to be done, particularly from MINOS.

But I remain puzzled and patient and fascinated. I will continue to  follow this fascinating physics on this post.