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An Evaluation of the Ninth SOSP Submissions
or How (and How Not) to Write a Good Systems Paper
Roy Levin and David D. Redell
Ninth SOSP Program Committee Co-chairmen
On March 21, 1983, the program committee for the 9th Symposium on
Operating System Principles, having read the eighty-three papers
submitted, selected sixteen for presentation at the symposium. This
acceptance ratio of about one in five approximates those of past
SOSPs, although the number of submissions was somewhat lower than in
recent years. Several members of the program committee found it
surprisingly easy to separate the good papers from the bad ones;
indeed, the ten committee members quickly agreed on the disposition of
over 80% of the papers. As the acceptance ratio indicates, most of
these were rejections.
After the committee had completed its selection process, several
members expressed disappointment in the overall quality of the
submissions. Many of the rejected papers exhibited similar weaknesses,
weaknesses that the committee felt should have been evident to the
authors. In the hope of raising the quality of future SOSP
submissions, and systems papers generally, the committee decided to
describe the criteria used in evaluating the papers it received. This
article combines the criteria used by all of the members of the
committee, not just the authors.
To try to avoid sounding preachy or pedagogic, we have cast this
presentation in the first and second person and adopted a light,
occasionally humorous style. Nevertheless, the intent is serious: to
point out the common problems that appear repeatedly in technical
papers in a way that will make it easier for future authors to avoid
them. As you read this article, then, suppose yourself to be a
prospective author for the 10th SOSP or for TOCS. You've done some
work you would like to publish, so you sit down to write a paper. What
questions should you be asking yourself as you write? These are also
the questions that we, the reviewers of your paper, will be asking to
determine its suitability for publication.
Classes of Papers
Your paper will probably fall naturally into one of three
- It presents a real system, either by a global survey of an
entire system or by a selective examination of specific themes
embodied in the system.
- It presents a system that is unimplemented but utilizes ideas or
techniques that you feel the technical community should know.
- It addresses a topic in the theoretical areas, for example,
performance modelling or security verification.
Obviously, a single set of evaluation criteria cannot be applied
uniformly across these categories; nevertheless, many criteria apply
equally well to all three. As we describe each one below, we will try
to emphasize the classes of papers to which it applies. Often it will
be evident from context.
Criteria for Evaluation of Submissions
Are the ideas in the paper new? There is no point in submitting a
paper to a conference or journal concerned with original work unless
the paper contains at least one new idea.
How do you know? You must be familiar with the state of the art
and current research in the area covered by your paper in order to
know that your work is original. Perhaps the most common failing among
the submissions in the first category (real systems) was an absence of
new ideas; the systems described were frequently isomorphic to one of
a small number of pioneering systems well-documented in the
Can you state the new idea concisely? If your paper is to advance
the state of knowledge, your reader must be able to find the new ideas
and understand them. Try writing each idea down in a paragraph that
someone generally versed in the relevant area can understand. If you
can't, consider the possibility that you don't really understand the
idea yourself. When you have the paragraphs, use them in the abstract
for the paper.
What exactly is the problem being solved? Your reader cannot be
expected to guess the problem you faced given only a description of
the solution. Be specific. Be sure to explain why your problem
couldn't be solved just as well by previously published techniques.
Are the ideas significant enough to justify a paper? Frequently,
papers describing real systems contain one or two small enhancements
of established techniques. The new idea(s) can be described in a few
paragraphs; a twenty-page paper is unnecessary and often obscures the
actual innovation. Since construction of a real system is a lot of
work, the author of the paper sometimes unconsciously confuses the
total effort with the work that is actually new. ("My team worked on
this system for two years and we're finally done. Let's tell the world
how wonderful it is.") If the innovation is small, a small paper or
technical note in a suitable journal is more appropriate than an SOSP
Is the work described significantly different from existing
related work? An obvious extension to a previously published
algorithm, technique, or system, does not generally warrant
publication. Of course, the label "obvious" must be applied
carefully. (Remember the story of Columbus demonstrating how to make
an egg stand on end (by gently crushing it): "it's obvious once I've
shown you how".) You must show that your work represents a significant
departure from the state of the art. If you can't, you should ask
yourself why you are writing the paper and why anyone except your
mother should want to read it.
Is all related work referenced, and have you actually read the
cited material? You will have difficulty convincing the skeptical
reader of the originality of your efforts unless you specifically
distinguish it from previously published work. This requires
citation. Furthermore, you will find it harder to convince your reader
of the superiority of your approach if he has read the cited works and
Are comparisons with previous work clear and explicit? You cannot
simply say: "Our approach differs somewhat from that adopted in the
BagOfBits system ." Be specific: "Our virtual memory management
approach uses magnetic media rather than punched paper tape as in the
BagOfBits system , with the expected improvements in transfer rate
and janitorial costs."
Does the work comprise a significant extension, validation, or
repudiation of earlier but unproven ideas? Implementation experiences
supporting or contradicting a previously published paper design are
extremely valuable and worthy candidates for publication. Designs are
cheap, but implementations (particularly those based on unsound
designs) are expensive.
What is the oldest paper you referenced? The newest? Have you
referenced similar work at another institution? Have you referenced
technical reports, unpublished memoranda, personal communications?
The answers to these questions help alert you to blind spots in your
knowledge or understanding. Frequently, papers with only venerable
references repeat recently published work of which the author is
unaware. Papers with only recent references often "rediscover"
(through ignorance) old ideas. Papers that cite only unpublished or
unrefereed material tend to suffer from narrowness and
parochialism. Remember that citations not only acknowledge a debt to
others, but also serve as an abbreviation mechanism to spare your
reader a complete development from first principles. If the reader
needs to acquire some of that development, however, he must be able to
convert your citations into source material he can read. Personal
communications and internal memoranda fail this test. Technical
reports are frequently published in limited quantities, out-of-print,
and difficult to obtain. Consequently, such citations as source
material should be avoided wherever possible.
Does the paper describe something that has actually been
implemented? Quite a few of the SOSP submissions proceeded for
fifteen pages in the present tense before revealing, in a concluding
section (if at all), that the foregoing description was of a
hypothetical system for which implementation was just beginning or
being contemplated. This is unacceptable. Your reader has a right to
know at the outset whether the system under discussion is real or not.
If the system has been implemented, how has it been used, and what
has this usage shown about the practical importance of the ideas? Once
again, a multiple man-year implementation effort does not of itself
justify publication of a paper. If the implemented system contains new
ideas, it is important to explain how they worked out in practice. A
seemingly good idea that didn't pan out is at least as interesting as
one that did. It is important to be specific and precise. "Our weather
prediction system is up and running and no one has complained about
its occasional inaccurate forecasts" is much less convincing than
"everytime we fail to forecast rain, the users hang their wet shirts
over the tape drives to dry". In the latter case, at least we know
that people are using and depending on the system.
If the system hasn't been implemented, do the ideas justify
publication now? This can be a difficult question for an author to
answer dispassionately, yet any reviewer of the paper will make this
judgment. It is always tempting to write a design paper describing a
new system, then follow it up in a year or two with an "experience"
paper. The successful papers of this genre nearly always include
initial experience in the closing sections of the design paper. The
subsequent experience paper then deals with the lessons learned from
longer-term use of the system, frequently in unanticipated
ways. Reviewers are very skeptical of design-only papers unless there
are new ideas of obviously high quality.
What have you learned from the work? If you didn't learn anything,
it is a reasonable bet that your readers won't either, and you've
simply wasted their time and a few trees by publishing your paper.
What should the reader learn from the paper? Spell out the lessons
clearly. Many people repeat the mistakes of history because they
didn't understand the history book.
How generally applicable are these lessons? Be sure to state
clearly the assumptions on which your conclusions rest. Be careful of
generalizations based on lack of knowledge or experience. A
particularly common problem in "real system" papers is generalization
from a single example, e.g., assuming that all file system directories
are implemented by storing the directory in a single file and
searching it linearly. When stating your conclusions, it helps to
state the assumptions again. The reader may not have seen them for
fifteen pages and may have forgotten them. You may have also.
What were the alternatives considered at various points, and why
were the choices made the way they were? A good paper doesn't just
describe, it explains. Telling your readers what you did doesn't give
them any idea how carefully considered your choices were. You want to
save future researchers from following the same blind alleys. You also
want to record potentially interesting side-streets you didn't happen
to explore. Make sure to state clearly which is which.
Did the choices turn out to be right, and, if so, was it for the
reasons that motivated them in the first place? If not, what lessons
have you learned from the experience? How often have you found
yourself saying "this works, but for the wrong reason"? Such a
pronouncement represents wisdom (at least a small amount) that may
benefit your reader. Many papers present a rational argument from
initial assumptions all the way to the finished result when, in fact,
the result was obtained by an entirely different path and the
deductive argument fashioned later. This kind of "revisionist history"
borders on dishonesty and prevents your readers from understanding how
research really works.
What are the assumptions on which the work is based? The skeptical
reader is unlikely to accept your arguments unless their premises are
stated. Make sure you get them all; it's easy to overlook implicit
Are they realistic? For "unimplemented systems" papers, this
amounts to asking whether the assumptions of the design can hope to
support a successful implementation. Many paper designs are naive
about the real characteristics of components they treat abstractly,
e.g., communication networks or humans typing on terminals. For
theoretical studies, it must be clear how the assumptions reflect
reality, e.g., failure modes in reliability modelling, classes of
security threats in security verification, arrival distributions in
How sensitive is the work to perturbations of these assumptions?
If your result is delicately poised on a tall tower of fragile
assumptions, it will be less useful to a reader than one that rests on
a broader and firmer foundation.
If a formal model is presented, does it give new information and
insights? Simply defining a model for its own sake is not very
useful. One deep theorem is worth a thousand definitions.
Does the introductory material contain excess baggage not needed
for your main development? "Real system" papers are particularly
guilty of irrelevant description. If your subject is distributed file
systems, the physical characteristics of the connection between
computer and communication network are probably not germane. Avoid the
temptation to describe all major characteristics of your system at the
same level of depth. Concentrate instead on the novel or unusual ones
that (presumably) will be the focus of the original technical content
of the paper.
Do you include just enough material from previously published
works to enable your reader to follow your thread of argument? Do not
assume that the reader has read every referenced paper within the last
week and has them at his fingertips for instant reference. If you want
your reader to get past page three, avoid introductory sentences of
the form "We adopt the definition of transactions from Brown ,
layering it onto files as described by Green [7, 18], with the notions
of record and database introduced by Black  and White  and
later modified by Gray ". On the other hand, don't burden your
reader unnecessarily with lengthy extracts or paraphrases from cited
Are the ideas organized and presented in a clear and logical way?
Are terms defined before they are used?
Are forward references kept to a minimum? Readers get annoyed when
they repeatedly encounter statements like "Each file consists of a
sequence of items, which will be described in detail in a later
section". The reader has to remember the technical term "item", but
the term has no semantics yet. It's all right to ask him to do this
once or twice, but only when absolutely necessary. Even if you can't
afford the digression to explain "item" at this point, give the reader
enough information to attach some meaning to the term: "Each file
consists of a sequence of items, variable-sized, self-identifying bit
sequences whose detailed interpretation will be discussed below under
'Multi-media Files'." Your reader may not yet understand your concept
of files completely, but at least he has some glimpse of the direction
in which you are leading him.
Have alternate organizations been considered? Theoretical papers,
particularly of a mathematical character, are generally easier to
organize than papers describing systems. The expected sequence of
definition, lemma, theorem, example, corollary works well for
deductive argument, but poorly for description. In "real system"
papers, much depends on the intent: global survey or selective
treatment. Frequently, difficulties in organization result from the
author's unwillingness to commit to either approach. Decide whether
you are surveying your system or focusing on a specific aspect and
structure the paper accordingly.
Was an abstract written first? Does it communicate the important
ideas of the paper? Abstracts in papers describing systems are sorely
abused. The abstract is more often a prose table of contents than a
precis of the technical content of the paper. It tends to come out
something like this: "A system based on Keysworth's conceptualization
of user interaction  has been designed and implemented. Some
preliminary results are presented and directions for future work
considered." No reader skimming a journal is likely to keep reading
after that. Avoid the passive voice (despite tradition) and include a
simple statement of assumptions and results. "We designed and
implemented a user interface following the ideas of Keysworth and
discovered that converting the space bar to a toe pedal
increases typing speed by 15%. However, accuracy decreased
dramatically when we piped rock music instead of Muzak (tm) into the
office." Leave discussion and argument for the paper. It helps to
write the abstract before the paper (despite tradition) and even the
outline, since it focusses your attention on the main ideas you wants
Is the paper finished? Reviewers can often help you to improve
your paper, but they can't write it for you. Moreover, they can't be
expected to interpolate in sections marked "to be included in the
final draft". In a mathematical paper, a reviewer regards the
statement of a theorem without proof with suspicion, and, if the
theorem is intended to culminate prior development, with intolerance.
Similarly, in a paper describing a system, a reviewer cannot tolerate
the omission of important explanation or justification. Omitting
sections with a promise to fill them in later is generally
Is the writing clear and concise?
Are words spelled and used correctly?
Are the sentences complete and grammatically correct?
Are ambiguity, slang, and cuteness avoided?
If you don't have sufficient concern for your material to correct
errors in grammar, spelling, and usage before submitting it for
publication, why should you expect a reviewer to read the paper
carefully? Some reviewers feel that this kind of carelessness is
unlikely to be confined to the presentation, and will reject the paper
at the first inkling of technical incoherence. Remember that you are
asking a favor of your reviewers: "Please let me convince you that I
have done interesting, publishable work." A reviewer is more favorably
disposed toward you if he receives a clean, clear, carefully corrected
manuscript than if it arrives on odd-sized paper after ten trips
through a photocopier and looking like it was composed by a
grade-school dropout. Even if you aren't particularly concerned with
precise exposition, there is certain to be someone in your
organization who is. Give your manuscript to this conscientious soul
and heed the resulting suggestions.
These thirty-odd questions can help you write a better technical
paper. Consult them often as you organize your presentation, write
your first draft, and refine your manuscript into its final form.
Some of these questions address specific problems in "systems" papers;
others apply to technical papers in general. Writing a good paper is
hard work, but you will be rewarded by a broader distribution and
greater understanding of your ideas within the community of journal
and proceedings readers.