ASTR 511 (O'Connell) Lecture Notes


Here are some tips, which I think would be echoed by most of my colleagues, for graduate students on how to approach research in astronomy.

A. Ask the right questions.

  • Learn to rank issues for overall importance to the field and for novelty.

B. Learn to assess solvability
  • You must learn to determine which problems are ripe for progress

  • Solvability is a function both of the state of current knowledge and available instrumentation.

  • Many "interesting" problems are not ripe for solution.

  • Evaluate signal-to-noise issues

  • Also assess the interests & strengths of competing groups & their potential for beating you to a result.

C. Plan to take quick advantage of new observational capabilities.

  • These are often the source of important new discoveries.

  • A "new capability" can be as simple as large amounts of observing time on an existing facility or a small upgrade such as a new type of imaging filter or a higher dispersion grating in a spectrometer.

D. Develop a healthily skeptical outlook.

  • Cultivated skepticism is the cornerstone of science:

      "He believed in the primacy of doubt, not as a blemish upon our ability to know but as the essence of knowing."
                ----- J. Gleick, writing about physicist Richard Feynman.

  • Apply to: established results, new results, and especially your results

      Be self-critical: make "reality check" your mantra

E. Know the background thoroughly:

  • Learn to critically dissect the literature, based on original, not secondary, sources.

      Read the more important papers from hardcopy; annotate them or make written summaries of key findings, strengths & weaknesses. It helps to keep copies of related papers together in a binder.

  • For longer term projects (e.g. a thesis) it is important to learn the entire history of your field. Among other benefits, there are many excellent insights that remain unexploited in the older literature

  • It is just as important to become familiar with the wrong ideas and why they were wrong as it is to know the currently accepted "right" ideas. There are many more wrong ideas than right ones.

  • Beware of the "emperor's new clothes." Always bring fresh eyes to any subject.

F. Develop skill with ROMPs & SWAGs

G. Understand your instruments well

  • This will take a minimum of 2-3 observing runs with a given instrument.

  • Learn their limits and how to push the envelope

H. Understand analysis techniques well

  • It is doubtful that your early reductions/analysis for a given problem will be acceptable in the long run. Plan for iterations.

  • Test techniques on synthetic data sets where you know the answer.

I. Track your own progress

  • Set milestones and regularly review your progress towards them; are you converging towards answering the main questions?

  • Keep a regular journal of your ideas (good & bad)

J. Dealing with computers

  • Computers are tools, not science

  • Despite appearances, computers have not increased the capacity of the human brain to absorb and process information

  • Don't trust and always verify

  • You will almost certainly have to become a capable computer programmer, not merely a user of pre-packaged software

  • If it's important, read it from paper

K. Dealing with advisors

  • Most advice comes from long experience; don't disregard it lightly. In troublesome areas, seek advice from several senior people.

  • Look at any research project, no matter how outwardly routine, as an opportunity to grow as a scientist beyond the nominal boundaries. You may well have new insights or see new avenues to exploit that your overloaded advisor has missed or ignored.

  • In the course of a PhD project, you are expected to become independent of your advisor and at least as knowledgeable as he/she is on that subject. You should know what is the "next step" before being told.

L. Dealing with groups

    A glance at the ApJ will demonstrate the growing dominance of group science.

    The rise of groups is a natural consequence of the increasing scope and complexity of modern astronomical research. New instruments are usually shepherded by groups, so they constitute a key avenue to new observational capabilities. Group work is also an increasingly important mechanism for marshalling existing resources to do new science (e.g. the supernova surveys).

    Successful groups are based on complementary strengths, not mutual weaknesses. Therefore, ...

    • Bring a unique expertise, skill

    • Produce; be responsible

    • Think for yourself

    • ...but learn how to interact with other members cordially and constructively

    • Lead by example

    • Be sure you develop a reputation/expertise that distinguishes you from other group members. In practice that implies, at a minimum, being lead author on some of the group's publications.

    Consult the history of "big physics" (accelerators, etc) for group sociology.

    • E.g.: larger groups breed institutional imperatives for publicizing results, which is why the media often mistake incremental results for fundamental ones.

M. Publishing

  • A good goal by PhD time is to have published in the major journals one paper for every year you've been in graduate school. You should be lead author of some of these.

  • Learn to write good, clear, concise scientific prose. Most entering graduate students cannot do this.

    • Consult style guides for tips, e.g. the Guide to Science Writing from the Journal of Young Investigators and The Elements of Style by Strunk & White.

    • Write up for yourself brief reviews of the literature or summaries of interim results in full journal style. These serve as good writing practice, as drafts for polished versions or presentations, and to place your accomplishments in the context of the main issues you are trying to address. Ask other students to read and critique your work.

  • Be aware of the ``reader pyramid'': few people will read the whole paper; more will read the introduction and conclusion; many more will skim/read the abstract.

    • Be sure the abstract contains all the key points.

    • Be sure the Intro/Conclusion are clear and complete; the conclusion should emphasize what is new or unique about the work.

  • Set high standards for yourself (and your co-authors) in writing. Reputations are based on the number of good papers one produces, not the total number of papers.

N. Presentations

  • Learn to give interesting and effective presentations on all time scales from 5 minutes to an hour. Analyze and emulate others who do this well. Real-time rehearsals are the only way to prepare well for your early ventures in this arena.

  • Unfortunately, you will need to learn PowerPoint or the equivalent. Just bear in mind that PowerPoint is the messenger, not the message.

O. Observing Proposals

  • Success rates for proposals on important facilities are small: in the range 20-40%.

  • A compelling proposal must be clearly, persuasively, and concisely written and must demonstrate:

    1. That the questions you are asking are important/interesting;
    2. That the program is technically feasible;
    3. That it will provide a definitive answer to the questions posed.

  • Write for harried TAC members who have only a few minutes to read each proposal and who are looking for reasons to reject

  • Write for people who are generally well informed but who are not specialists in the field. Clearly explain the main issues. Place in the larger context. Make sure claims for importance/uniqueness are defensible; don't exaggerate.

  • Keep it short and clear: use subheadings, short paragraphs, topic sentences, large fonts; don't crowd text

  • Put key points up front

  • Don't waffle: where ambiguities exist, state clearcut choices and how you intend to resolve the issues involved

  • Illustrations can quickly clarify issues for the reader; they add interest and can substitute for lengthy text

  • Essential: proofread line-by-line from paper, not a computer screen; always spell-check.

P. Scientific Discovery, Scientific Careers

The list of tips above constitutes tactics; but what about strategy? What is the best path to scientific discovery or a good scientific career?

Discovery first. Broadly, there are two kinds of discovery: recognition of something new or a definitive interpretation of known phenomena. The former is easier for young people. For the latter, you usually need greater exposure to the field. Although many "interpretational" discoveries are theoretical, others are observational (e.g. Hubble's discovery of Cepheid variables in M31, which instantly resolved the "island universe" controversy; or the identification of gamma-ray bursts with distant galaxies).

Scientific discoveries emerge from some combination of "the prepared mind," resources, opportunity, and, inevitably, luck. There is probably about equal weight to those four components, and there's no way to successfully engineer them. But follow the chain in order. The better prepared you are---the more you know and have produced---the more likely it is that the good resources you seek will be available to you. Opportunity may follow. You have to wait for luck. Whatever form that takes, it's essential that you be able to recognize a favorable coincidence of opportunity and luck, which means that you must actively cultivate an alertness for them.

You obviously can't discover something if you aren't looking, so discovery depends also on effort and persistence.

Careers? You need a plan, and you need to think actively about it.

Training in most graduate programs is "T-shaped". You are expected to become acquainted with the basics of many subfields of astronomy (the crossbar) while acquiring deep knowledge in at least one (the upright). The whole "T" is important. The narrow/deep component is necessary if you are to understand how scientific research actually progresses; but from a career standpoint you must also develop a broad understanding of the field and versatile skills that are transferable to other research areas.

Your immediate aim by PhD time should be to become one of the leading authorities on some area of significant current interest. It is expected that this area will usually be of modest scope, but when conference organizers are picking the most knowledgeable younger speakers for review talks, you want your name to be on the short list. This means that you must not only have important expertise but that others must know you have it. [Hint: publish and talk to as many outsiders as you can.]

Research topics? Paradoxically, it is not necessarily best to get into the currently "hot" subject areas. Those may be where the money is and where your mentors are; but these areas tend to overproduce PhDs, and there will be tough competition from experienced scientists. Ideally, you want to be at the leading edge of a new wave of research that peaks about ten years from now. But, obviously, it's not easy to figure out what that might be. No matter how promising the field you choose to work in, keep developing those transferable skills and interests; keep looking around the corner.

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Last modified June 2010 by rwo

Text copyright © 2000-2010 Robert W. O'Connell. All rights reserved. These notes are intended for the private, noncommercial use of students enrolled in Astronomy 511 at the University of Virginia.