Why We Need an Explicit
Forum for Negative Results
Announcement of the
Forum for Negative Results (FNR)
Universität Karlsruhe, Germany
Abstract: Current Computer Science (CS) research is primarily
focused on solving engineering problems. Often though, promising attempts
for solving a particular problem fail for non-avoidable reasons. This is
what I call a negative result: something that should have worked does not.
Due to the current CS publication climate such negative results today are
usually camouflaged as positive results by non-evaluating or mis-evaluating
the research or by redefining the problem to fit the solution.
Such publication behavior hampers progress in CS by suppressing some
valuable insights, producing spurious understanding, and misleading further
research efforts. Specific examples given below illustrate and back up
This paper is the announcement of a (partial) remedy: a permanent publication
forum explicitly for negative CS research results, called the Forum
for Negative Results, FNR. FNR will be a regular part of J.UCS.
Key Words: FNR, forum, negative results, failures, research culture,
Category: A.m, K.7.m, K.4.m, I.2.7 speech recognition, I.2.6
learning, C.1.3 data flow architectures, B.6.3 verification.
1 Current Computer Science research culture
Almost all Computer Scientists agree that Computer Science (CS) has
a strong engineering problem-solving component: most of it ultimately aims
at building useful systems and making them ever better and cheaper. This
excludes only some parts of the theoretical CS research.
As a result, we tend to judge research contributions by their short
or mid-term application usefulness: Those contributions are considered
best that very successfully solve an important engineering problem. Contributions
that solve only a small fraction of their problem are considered less good
and contributions that entirely fail to solve their problem are often not
considered research contributions at all. Consequently, most researchers
strive for problem-solving successes, where the problems to be solved are
selected from an engineering point of view.
On the other hand, most CS researchers also agree that CS needs a firm
scientific base on which to build new engineering solutions. Such a base
is provided when research emphasizes understanding more than engineering
solutions. In this case, obvious practical applicability needs not be
a research quality attribute.
Note that the discrimination between problem-solving research and research
for understanding is not a sharp one, it is only a matter of emphasis;
see also the article of Fred Brooks in the March 1996 issue of CACM [Brooks
1996] and the responses in the July issue.
Looking at actual CS research contributions, a large majority of them
makes claims that clearly belong to engineering problem-solving; a study
conducted in 1994 found about 75 percent of all articles in a random CS
article sample to be of this type [Tichy et al. 1995]
Thus, our emphasis in non-theoretical CS as a whole is quite clearly
on engineering (which is not necessarily harmful) and our judgement of
what constitutes good research is consequently biased (which is harmful).
The following sections will discuss how this bias slows down progress
in CS and why a forum for negative results might help; I will give specific
examples to illustrate my point. Then I will present the structure of the
new Forum for Negative Results and finally discuss the most important
objections against it, before concluding the paper with a call for comments.
2 Why and how it hurts CS
The CS research culture described above has negative impact on our discipline
as a whole in three different ways: First, results that could contribute
to understanding may be suppressed; second, results may be presented in
misleading ways; and third, research may be misguided towards less fruitful
directions. I will discuss these problems in order and intersperse specific
examples for illustration. These examples are authentic reports of actual
research; for sake of brevity and clarity of argument, their technical
content was somewhat simplified.
2.1 Lost insights
If a failure is not published at all, obviously nobody else can learn
from it. However, non-publication does not seem to be frequent in CS. More
often, and more seriously, failures are published in a clouded, hidden
form: Either the problem is redefined appropriately as to fit the solution
obtained, or the ``solution'' is evaluated using only selected examples
where it works well. Sometimes the solution is hardly evaluated at all.
In all of these cases, the reasons for the failure are not analyzed and
our understanding is improved less than it could have been.
2.2 Example 1: Estimating speaking rate
This example of non-publication I heard from members of a world-class
speech recognition research group that wish to remain anonymous. It exemplifies
the loss of an insight due to the complete suppression of a negative result.
Problem: Every speech recognition system expects a certain speaking
rate. If a speaker speaks very fast, the error rate increases; the system
only works well for roughly the speaking rate for which it was built -
an important limitation that must be overcome. However, several separate
subsystems can be built for
different speaking rates. Then it becomes necessary to estimate the
speaking rate before the actual speech recognition in order to select
the appropriate subsystem.
Idea: The basic layer of a speech recognition system is the set
of phoneme models: There is one module for each of, say, 40 different phonemes
and at each time each of these modules m estimates the probability
that the current speech input represents m's phoneme. During a phoneme,
the corresponding module is high and the others are low. During a transition
from one phoneme to the next, all modules are low and therefore the entropy
of the module signals is higher. The local maxima of the entropy time series
should thus indicate the phoneme transitions, the frequency of which is
a direct measure of speaking rate.
Result: The idea was implemented and tried with various sorts
of phoneme models and for various speaking rates. Speaking rates were estimated
for 2-second long blocks of speech. The correlation between estimated and
actual speaking rate was between -0:15 (sic!) and 0.26, typically 0.12.
The idea does not work at all; it is essentially useless.
Insight: The idea does not work because the output of the individual
phoneme models is too unreliable; there are many spurious maxima in the
entropy time series. This is true although the given phoneme models are
among the best available world-wide. The accuracy of speech recognition
systems mostly stems from the integration of other knowledge sources such
as phoneme pair frequency distributions and dictionaries.
Handling: The idea, results, and analysis have not been and will
not be published.
Effect: The maxima-counting idea is so appealing, even for somebody
who knows about the unreliability of the individual phoneme models, that
other speech recognition research groups will most probably steer into
the same blind alley again once they find it.
2.3 Spurious insights
Spurious insights occur in one of three forms:
- Sometimes dressed-up or distorted evaluations as mentioned above make
the reader believe something that is not there. A solution may appear to
possess properties that it does not have at all or only to a lesser degree.
- Also, positive results sometimes occur by chance as shown in the example
below. In both cases, such spurious results can seriously distort CS knowledge.
- Most of the time, however, the authors only try to convey a success,
but fail to convince the reader of it. As a result, a lot of CS research
lacks credibility, which also harms CS as a whole.
The problem of cases 1 and 3 is lack of a fair and thorough evaluation
of a solution. Several papers have published quantitative evidence or constructive
critique in this matter, e.g. [Fenton et al. 1994];
[Prechelt 1996]; [Tichy et al.
1995] . One reason why we find such insufficient evaluations is that
they would often produce negative results which would be hard to publish.
The problem of case 2 is the non-publication of negative results as illustrated
by the following example.
2.4 Example 2: Comparing neural network algorithms
The following is an example of distributed research. It shows
how the suppression of negative results can lead to spurious positive results.
The example is not
concrete, because it is impossible to find all the participants, but
is quite realistic. It is discussed in similar form by Salzberg [Salzberg
Problem: Many researchers are trying to improve current neural
network learning algorithms, e.g., for pattern classification tasks. Let
us say that 20 different researchers are all trying to improve the same
Idea: Let us further assume that each of these 20 researchers
has come up with the same modified version M of A and that
this modification is useless: it neither improves nor reduces the performance
of A. Both assumptions are realistic; there are many changes to
learning algorithms that seem plausible as an improvement, but are neutral
overall and that many people could come up with independently.
Result: Ideally, each of our 20 researchers will evaluate his
or her change using multiple different problems and multiple training runs
for each, and they will compare the results obtained for M to their
results for A using a statistical significance test. Note that most
neural network learning algorithms are indeterministic, because they start
with a random initialization of the the network parameters. Therefore,
the results of the significance test are indeterministic as well (after
all, that is what statistical tests are for) and we can expect one of our
20 researchers to obtain significance at the 0.05 level.
Insight: The conclusion of this researcher will be that M
is indeed better than A.
Handling: This one researcher will publish M as an improvement
of A. Maybe one or two others also had (weakly) significant results
and publish them as well. The other 17 will probably not publish
their negative result that M is not a useful improvement of A
although M seems appealing.
Effect: The research community will get the false impression
that M is better than A - a spurious insight which is due
to the suppression of the negative results obtained by the majority of
researchers. The same could happen, although with smaller probability,
even if M was in fact worse than A. The spurious positive
result may further contribute to the evolution of false and misleading
theories of learning that explain why M is supposed to be
better than A.
2.5 Misdirected research
As a consequence of both lost or spurious insights, other researchers
might pursue investigations that are ineffective or at least inefficient
and that they would not have pursued, had the respective negative results
been published with an appropriate analysis.
2.6 Example 3: Dataflow computers et al.
The history of dataflow computers is an example of misdirected research
due to insufficient evaluation or insufficient consideration of negative
aspects of research results. It bears many similarities to several
other areas of CS; these could be discussed here just as well.
Problem: How to build efficient computer hardware given advancing
electronics technology, beginning in the early 1970s.
Idea: Express a program as a dataflow graph and build hardware
that can execute dataflow graphs. This will automatically exploit instruction-level
parallelism by executing a program instruction when all of its input values
available. Implicit control flow replaces the program counter. Programming
becomes simpler and increasing numbers of transistors per chip can be utilized
by increasing the number of basic execution units. Instruction-level parallelism
is the most general kind of parallelism and thus will be more efficient
than explicit parallelism with explicit synchronization [Dennis
Result: Operational prototypes of static dataflow computers were
built in the mid-1970s. For most program domains, their parallelism was
limited severely by the inability to execute loop iterations or recursive
calls in parallel. This limitation is inherent in the principle of a static(!)
dataflow computer. In the absence of sufficient instruction parallelism,
sequential execution of dataflow computers is quite slow.
Insight: The insight at this point should have been that entirely
replacing von Neumann style computing with dataflow computing might be
the wrong idea. The next goal should have been understanding what combination
of aspects of both paradigms would be most efficient [Iannucci
Handling: However, a decade after dataflow computers were first
proposed and several years after the first prototypes became operational
and the lack of instruction-level parallelism became apparent, one of the
principal dataflow researchers still wrote: ``What are the prospects
for data flow supercomputers? [. . . ] A machine with up to 512 processing
elements or cell blocks seems feasible.'' [Dennis
Effect: Instead of working towards hybrid von-Neumann/dataflow
architectures, the dataflow community went on to building dynamic dataflow
machines [Hwang and Briggs 1984] , which increased
the amount of available parallelism but (predictably) suffered from its
large token tagging, tag comparing, and data duplication overhead and was
never able to keep up with von Neumann processors of similar cost.
A more critical evaluation and increased focus on problematic aspects
of the dataflow idea could have saved significant amounts of research resources
and had probably resulted in faster progress. As Hwang and Briggs diplomatically
put it in 1984: ``Most advances are claimed by researchers in this area.
The claimed advantages were only partially supported by performance analysis
and simulation experiments. Operational statistics are not available from
existing prototype data flow machines. Therefore, some of the claimed advantages
are still subject to further verification.'' [Hwang
and Briggs 1984, p. 745]
CS research history features several other examples of similar nature,
such as most areas of Artificial Intelligence (e.g. automatic program verification,
pat- tern recognition, symbolic AI, neural network learning, fuzzy logic)
computer integrated manufacturing (CIM), object-oriented methods, and others.
In all of these cases, a lack of weakness analysis or the suppression of
its negative results has led to avoidable waste of research resources and
slowdown of progress, at least for a significant time during the early
development phases of the respective areas.
Again: This is clearly not to say that all research in the above areas
was wasted. Each of these areas has produced many valuable contributions
to our knowledge. However, some parts of the work in these areas was wasted
or inefficient and these parts were much larger than would have been necessary.
2.7 Example 4: Hardware verification
This final example illustrates how deeply researchers have absorbed
the principle of not publishing negative results and how this can prevent
Problem: In formal hardware (VLSI) verification, several research
groups have produced operational systems that all have different strengths
and weaknesses. A comparative evaluation of these systems could be a powerful
means of understanding why these weaknesses occur and might produce
ideas for further improvements.
Idea: One researcher in this field, who wishes to remain anonymous,
invited selected colleagues from all of these research groups to write
a contribution to an edited monograph that was intended to provide such
a comparative evaluation. Each group was given a set of example problems
and was asked to elaborate which of these their system could handle well
or not well and why. All of the papers were practically already accepted
before they were even written, so there was no pressure towards producing
only positive results - quite on the contrary: The editor asked explicitly
to elaborate on weaknesses and their cause.
Result: Despite repeated explicit queries, several of the groups
did hardly describe, let alone discuss, those cases where their system
did not do well.
Effect: The comparative analysis was only half as useful as it
could have been. Probably some important insights were lost.
3 A counter-measure: The Forum for Negative Results
Even if a meant-to-be problem-solving contribution fails and thus represents
no direct engineering progress, it can be a useful research contribution:
Quite often an analysis of the reasons why a particular approach to a problem
failed could contribute to understanding, thus promoting further engineering
advances and avoiding unfruitful research efforts.
The right thing to do with such a failure would thus be to publish a
description and an analysis of the reasons instead of the now common disguised
mis-presentation as a success. One major reason why such presentation of
research as a negative result is so rare today is a lack of encouragement
as discussed in Section 1.
This is why J.UCS hereby announces the establishment of a publication
forum that explicitly and exclusively calls for negative results:
The Forum for Negative Results (FNR). FNR is a permanent, specially
marked section of J.UCS.
Call for Papers: The Forum for Negative Results (FNR)
The Forum for Negative Results (FNR) is a permanent special section
of the Journal of Universal Computer Science (J.UCS) and exclusively publishes
negative results, i.e., research that did not have the desired outcome,
but still advances knowledge. J.UCS is an electronic journal published
by Springer Verlag.
Rationale: As most of Computer Science is rather usefulness-oriented,
it is currently difficult to publish work that demonstrates a non-progress,
or negative result, with respect to usefulness. Therefore today,
- lessons to be learned from negative results are often lost, and
- many works tend to demonstrate neither progress nor non-progress.
FNR is a top-class forum for publishing Computer Science negative results
that imply scientific insights. Just like J.UCS, FNR does not restrict
contributions to particular topics. However, only papers with the following
properties qualify for publication in FNR:
- The work described had a clear goal, stated in the paper.
- The starting point or approach of the work was promising and had plausible
chances of success. These chances are explained in the paper.
- Still, the goal was not met. The failure was not foreseeable during
the implementation phase of the work; it was apparent only from the evaluation
phase. (This rules out most purely theoretical work.)
- There must be danger of somebody else trying a similar approach again,
- Both implementation and evaluation were carried out according to highest
scientific standards. These standards are documented in the paper.
- At least part of the reason for the failure was understood in the evaluation
or in subsequent analysis. The explanation is given in the paper. This
explanation represents the scientific contribution of the paper.
FNR will be extremely selective. Any paper to appear in FNR must
be impeccable with respect to points (1) and (5). High standards
will also be applied to points (2), (3), and (4). As for point (6), the
lesson learned must become clear, but no cure needs to be known.
Articles should be as concise as possible and concentrate on goals,
approach, and reasons for failure instead of on technical details of implementation
and evaluation. The reviewers of a paper submitted to FNR will apply these
criteria when judging the contribution.
For further information see the FNR homepage at http://wwwipd.ira.uka.de/fnr.
3.1 Additional remarks
Some points require particular emphasis: First, in order not to become
a trash can of failed low-quality research, FNR will be very demanding.
FNR will only
have a significant positive impact on the overall publication climate
if it becomes a prestigious place for publishing one's research.
Second, whether an initial idea was really ``promising'' and the failure
``unforeseeable'' does obviously depend on the researchers' previous knowledge;
others might have anticipated the problem. Here, similar reasonably high
(but not too high) standards will be applied as for conventional J.UCS
Submissions to FNR will be reviewed and published like submissions to
J.UCS, except that
- the FNR review criteria will be applied,
- the paper will appear with the subtitle ``a contribution to the Forum
for Negative Results'', which also must be used by the author for submitting
In particular, FNR contributions are in the same publication queue as
J.UCS contributions. There is no fixed minimum or maximum number of FNR
contributions in one J.UCS issue. No article submitted to FNR will ever
directly compete with any non-FNR article submitted to J.UCS, as such competition
could invalidate FNR's basic idea. Instead, when space becomes scarce,
accepted articles will usually be published in order of submission. The
typical publication delay, however, will be short compared to other high-class
Most people I talked to are in favor of the idea of having an explicit
forum for negative results. Some others, though, disapprove. This section
discusses their objections.
- Science is not about truth, it is about status, money, and power.
This objection was posed by a few and seems to be considered correct
by many - to some degree. However, all researchers I talked to also feel
that science should not be this way. Moreover, the contradiction
between truth and personal status that most people see connected with a
failure is only a result of over-emphasizing engineering success in Computer
Science. Most researchers dislike the contradiction; so why not try and
open new opportunities for removing it? FNR is such an opportunity.
- Nobody likes failures. (This one is closely connected to the
one above.) Sure, no researcher likes admitting that something just did
not work. However, most dislike disguise even more and will often prefer
to analyze the failures they had as failures instead of feeling pressed
to discuss or mis-evaluate them into successes.
- Knowing the reasons for a failure is a competitive advantage that
people will not give away. For a few research areas that are both very
focused and fast-moving, this may be true. In such an area, many research
groups are targeting the same problems using similar methods and the area
is leaping from success to success - and only success counts. In any really
fast-moving area, on the other hand, the usual publication delay is sufficient
for protecting the competitive advantage. Most areas of computer science
are not critical in this respect, anyway.
- A published failure may keep people from picking up the same idea
later. This fear is valid when a failure was only due to technological
or constraints that might change later: If an idea was published as
leading to a negative result, wouldn't other researchers be deterred from
trying the idea again later? Wouldn't some successes be lost that way?
No, they wouldn't - quite on the contrary: The contribution of the respective
FNR paper would be to make the relevant technological constraints explicit
and identify alternative conditions under which the same idea would probably
work well. Such a description would foster, rather than discourage, picking
up the idea again later, at exactly the right time.
- High-quality negative results are also published elsewhere. Right.
Any paper FNR will accept would most probably also be accepted by other
high-class journals. But that is not the point. The point is that today
writing a paper in this way is daunting and getting it accepted is often
unnerving. Hence, only a fraction of all failures that could be instructive
is actually published and analyzed as negative results, thus damaging scientific
progress. With FNR, more such useful negative results would appear.
As we see, on close examination all of this critique is invalid. Nevertheless,
it may still adversely affect the success of FNR.
We cannot know in advance whether FNR will be accepted and will become
a scientific success. However, if we want to improve the scientific quality
of Computer Science research, we will have to give it a try.
Furthermore, J.UCS has an annotation facility whereby comments or additions
can be attached to published articles. The annotation facility can be used
by everyone: select ``Discussion forum'' (http://www.iicm.edu/jucs_annotations)
on the JUCS homepage, register, and submit. All annotations are reviewed
to ensure high quality. Discussions and additions bundled through the annotation
mechanism will further improve the scientific impact of FNR contributions.
Hence, the Journal of Universal Computer Science proudly announces the
Forum for Negative Results and encourages all authors to submit
appropriate high-quality papers.
I also encourage every CS researcher to contribute an additional argument
for or against FNR itself or an additional research war story, etc., by
means of an annotation to the present article.
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