Prologemma –Newton’s use of formal
systems

Perhaps the most
important legacy of Newton is in the use of formal systems.He established, for the first time, a close
mapping between a formal system and a set of aspects of our world. This mapping
allowed complex inferences to be made about many different aspects of the
world. This went beyond merely exploring mathematics for its own sake and
beyond using mathematics to merely express relations found in data. In fact,
the mapping seemed to be so accurate in so many different ways,
explaining so many diverse phenomena, making so many novel yet
correct predictions about the world and bringing together so many
different types of phenomena together into a single descriptive framework, that
it was taken (with some justification) for the literal truth. Here the full
potential of formal systems was revealed.

As it happens, Newton
did more than discover this mapping, he also invented a system of mathematics
for the mapping to go to (as did Leibniz). He presented his system in a
pseudo-axiomatic form - the three Newtonian laws. When his theory is taught, it
is the formal part that is brought to the fore, since for people today this is
the less obvious and more difficult part.The overriding importance of the mapping between his system and
the world is now less prominent. Shallow imitations of Newton’s method
concentrate upon inventing new formal systems, treating the mapping into the
observed world as a secondary concern.The result of such imitation is technical brilliance along side almost
complete irrelevance.

The aim of this paper
is to re-emphasise that the purpose of formal systems is to provide something
to map into and to stem the tide of unjustified formal systems.I start by arguing that expressiveness alone
is not a sufficient justification for a new formal system but that it must be
justified on pragmatic grounds.I then
deal with a possible objection as might be raised by a pure mathematician and
after that to the objection that theory can be later used by more specific
models.I go on to compare two
different methods of developing new formal systems: by a priori
principles and intuitions; and by post hoc generalisation from data and
examples.I briefly describe the
phenomena of “social embedding” and use it to explain the social processes that
underpin “normal” and “revolutionary” science.This suggests social grounds for the popularity of normal science.I characterise the “foundational” and
“empirical” approaches to the use of formal systems and situate these with
respect to “normal” and “revolutionary” modes of science.I suggest that successful sciences (in the
sense of developing relevant mappings to formal systems) bare either more
tolerant of revolutionary ideas or this tolerance is part of the reason they
are successful.I finish by enumerating
a number of ‘tell-tale’ signs that a paper is presenting an unjustified formal
system.

The Justification of Formal Systems

By themselves formal systems tell us nothing, since we can
construct them with whatever properties we desire. It is easy to get the
impression that they inform us of the consequences of our assumptions (or
conversely the assumptions behind our reasoning) but this is not the case. A
formal system only relates its assumptions to its conclusions via its inference
rules and in general we are free to choose these rules as we like.

Some formal systems
are so general (or equivalently so expressive) that we can use them to capture
any other formal system (as far as we know), examples include: set theory, type
theory and category theory (Marquis, 1995). In each of these, other formal
systems (including each other) can be embedded. The bare fact that one is using
one of these general formal systems tells us nothing about what is being
formalised unless something about the nature of the relationship between the
formal system's entities and the object of modelling is specified. (Sometimes
this relationship is specified by a default interpretation, typically derived
from the context of the formal system’s original development.)

Such general systems
only derive explicit content when they are constrained in some way.This constraint can be achieved by the
specification of additional information in the form of assumptions or by
mapping part of the system into a more restricted system. The more constrained
the systems are, the more explicit content they have but the less general they
are – there is an inescapable trade-off between generality and the amount of
content (although this trade-off is not necessarily simple).

However, formal
systems also have implicit content derived from their structure. The
structure of a formal system makes it easier to formalize certain kinds of
subsystem - those whose structure somehow 'suits' that of the general system.
This means that for any being with limited resources (at any one time) the choice
of formal system will affect the difficulty of formalizing something. That is,
a formal model of something will almost certainly be more difficult in one
formal system than in another. To put it another way, the model that results
from being formulated within one formal system will be more complex than that
formulated in another. Thus our choice of formal system will inevitably bias
our modelling efforts (impeding them in one direction and facilitating them in
another). This is the reason we need different formal systems – otherwise we
would use just one general system (e.g. set theory) for everything.

There is no need to
invent more expressive formal systems, nor does this seem possible.The purpose of developing new formal systems
is thus entirely pragmatic.That
is to say it is useful to develop new formal systems in order to facilitate the
formalization of particular domains.It
could be that a new formalism can make a certain type of model simpler, perhaps
making this feasible for the first time.Alternatively it might make the mapping of the formalism onto the domain
of modelling easier and more natural, and thus provide a readily accessible meaning
for the formal expressions. Thirdly, the properties of the formalism might be
useful for manipulating or thinking about descriptions of the intended
domain.

Presentations of novel
formal systems (or formal systems with novel features) that only establish
basic properties (like consistency or validity) and are justified purely
on arguments of expressiveness should be treated with caution.This is because we already have many such
systems and it is an almost trivial matter to extend an existing formal system
to make it a bit more expressive.

The problem is quite
acute in some fields.For example the
realm of multi-agent systems (MAS) in artificial intelligence it is common to
come across papers that exhibit a formal logic (or fragment thereof) which are
used to express some aspect of agency.Typically some of the basic properties of the logic are shown (e.g.
soundness, semantics, proof theory, simple upper bounds to their computational
complexity) and some argument presented as to why the increase in
expressiveness is needed. Such a paper does not get us anywhere unless
such a formalisation can be shown to be useful, for instance: lead to
interesting theorems, make some new computations possible, have helpful
properties for transforming formal descriptions or just simplify formal
descriptions and manipulations in some domain.

The assessment of the
appropriateness and utility of a formal system is made more difficult if its
intended domain is not made clear. One common source of domain vagueness is
when similar domains are conflated.

For example it is
common that the demonstration of the relevance of a formal system is
demonstrated with respect to an idealization of the intended domain of
application – it being implied that it will be useful in the original
(non-idealised) domain without actually demonstrating this.Such conflations are often based on the
assumption that the approximations necessary for the subsequent mapping onto
the final domain are essentially unproblematic. An indication that a paper is
focused on idealisations is when a system is demonstrated only upon “toy”
problems or otherwise artificially simple cases.Another tell-tale sign is when it is assumed that the extension
to “scaling-up” to realistic examples will be unproblematic or is simply listed
under “further research”.

An Argument Against

However, a
mathematician (or logician or whatever) may object in the following manner: “the
history of the development of formal systems has included many systems that
would have failed on the above criteria and yet turned out to be immensely
useful later on- are you not in danger
of preventing similar advances with such warnings?”. My answer is fourfold.

•Earlier, we did
not have the huge number of formal systems we have today, and in particular the
general systems mentioned above were not mature.Today we are overwhelmed by choice in respect to formal systems -
unless substantial advances are made in their organization all new systems will
need to be substantially justified if their clutter is not to overwhelm us.

•There is a proper
domain for formal systems that do not relate to a specific domain using one of
the criteria specified above: pure mathematics.Presenting a formal system elsewhere implies that it is relevant
in the domain it is being presented in.

•Even in pure
mathematics presentations or publications are required to justify themselves
using analogues of the above criteria - novelty, expressiveness and soundness
are not enough (although the other criteria perform a weaker role than
when they are applied elsewhere).For
example, in the examination of a doctoral thesis in pure mathematics once the
soundness of the work is deemed acceptable it is the importance, generality and
relevance of the results that are discussed.

•The cost
structure of the modelling enterprise has changed with the advent of cheap
computational power.It used to be the
case that it was expensive in both time and other resources to use and apply a
formal theory, so that it was important to restrict which formalisms were
available.Given that the extensive
verification of the success of formal systems was impossible they had to be
selected almost entirely on a priori grounds. Only in the fullness of
time was it possible to judge their more general ease of use or the utility of
their conclusions.Now this situation
has changed, so that the application of formal systems has been greatly
facilitated using computational techniques.

Chains of Models

Another possible
objection that might be raised is that a particular theoretical system is the
starting point and that others will then apply this in directly useful and testable
models and simulations.

It is true that one
may need to employ more than one model in order to capture a particular
phenomenum. In fact it is common to have whole chains of models reaching from
the most abstract theory down to the most basic data. At the bottom is the
object or system that is being modelled (e.g. the natural phenomena one is
concerned with).From this data may be
obtained by the process of measurement – so at the next level up one may find a
data model.At the other extreme
there might be some fundamental law or system that a formal model has to be
consistent with – this may be as abstract as a system of definitions or the
syntax of the formal modelling framework. Each model in the chain has to relate
to the models “above” and “below” it via the relations of validation and
verification (see figure 1).

Figure 1.
A chain of models from data model upwards (abstracted from an actual example in
chemistry)

One model validates
another when it specifies some constraints that the second model must obey -
for example: a model of chemical interaction has to be consistent with atomic
physics.Thus validation provides a prior
constraint upon a model - for it constrains the design of a model.

One model is verified
by another when the predictions or output of the model is shown to be
consistent with the second model.For
example a law may be verified against a set of data if it predicts the data
with sufficient accuracy.Thus
verification is a post hoc constraint upon a model - it determines
whether a complete model is in acceptable agreement with another (usually a
model closer to the target phenomena).

Such chains of models
are a common and natural means of dividing the design, implementation, checking
and justification of complex models into manageable steps.It does mean that in many domains it may be
impractical to verify the utility and relevance of formal models immediately.
Suchverification might require a
combination of models, as just described.These chains of models are discussed more in chapter 2 of (Edmonds
1999b)

In such situations,
although one may not be able to exhibit a final justification of a formalism in
terms of the criteria above, one can provide some justification by establishing
its coherence with its theoretical context (its validation) and some
verification against a model that is as near to the grounding phenomena as
possible.This could be necessarily
only a step towards a finally convincing justification, which would occur when
the complete chain of verifications, all the way down to the target phenomena,
is completed. However, until the chain is completed it might be
wise to retain a level of agnosticism as to the appropriateness of the model
since it could turn out that the model does not relate, even indirectly, to the
target phenomena. That such a complete verification has been repeatedly put off
it can be taken as evidence that either people have failed in their attempts to
complete it or even that this has seemed too difficult to attempt. A formal
system which can boast of no thoroughly verified models, and thus currently
unproven is much closer to an unfulfilled intention than a successfully
executed plan.

A Priori vs. Post Hoc Formalization

One common method of
establishing the relevance of a formal system is to justify the system's design
with reference to a set of abstract principles. These are typically a priori
principles, that is they are decided upon the basis of intuitions or tradition
prior to the verification of the system against the problem or domain of
study.This is in contrast to a post
hoc formalization where one is trying to generalize from a substantial
series of observations or trials in the domain of study.

In general post hoc
formalisation is greatly to be preferred to a priori formalisation. The reason
for this is that as soon as one starts to use a formalisation this tends to
bias one's perception of the phenomena or problem under study. To apply Kuhn's
term, one’s observations are “theory-laden” (Kuhn 1962), because one can not
help but view the basic data through the “lens” of the theory or formal system
one is using. One cannot escape the fact that any formal system has implicit
content as described above – it will inevitably make some models easier and
others more difficult. If one is attempting an a priori formalisation then the
chances of it happening to bias ones efforts in the best direction is very
small because one is guided only by one’s intuitions.In post hoc attempts, one already has a body of data drawn
directly from the phenomena under question in order to constrain and guide the
direction of ones efforts.The problem
domain itself is likely to be a better guide to that domain than intuitions
gained over other problem domains, especially if the domain under study
is new.

Great post hoc formal
systems are sometimes associated with “revolutions” in science.A new theory is proposed outside the
framework of established theory that explains and/or predicts a wide set of
observed phenomena or solves a wide set of existing problems.If the new theory is sufficiently successful
compared to others it may come to be accepted as the new established theory.
Examples of this are the Newtonian theory of gravity and the plate tectonics revolution
in geology.

At other times “normal
science” prevails. Researchers in these periods seem to work largely within an
established theoretical framework, building on each other’s work by solving
complementary problems. The danger of this is that a field can become closed to
outside influence and contrary findings. It thus immunizes itself to
falsification to some extent and limits the invention of new theories and
formalisms to those consistent with the established paradigm. Thus although
such periods of science can be very efficient and productive, the simultaneous
weakening of selective pressure from outside the field and the lessening of the
variation inside means that it can become sterile once it has exhausted the
domain of applicability of the established framework.If this established framework is very general and successful then
the span of productive work within the paradigm can be long, but if it is
limited in generality and poor at explaining and predicting the target
phenomena then it may only have a stifling effect upon the development of
knowledge.

Social Pressures and Embedding

It is interesting to
note that an analogous process can be observed among co-evolving populations of
adaptive social agents.When the
complexity of their environment is great they may come to rely on the outputs
of other agents as effective “proxies” for aspects of that environment. This
occurs when constraints on their rationality mean that the full modelling of
their environment is impractical and hence the social proxy is a useful
substitute (despite its relative unreliability). If a substantial proportion of
the agents in a population use each other's outputs as such proxies the
development of knowledge can become somewhat self-referential within that
population. Elsewhere I have investigated this effect using simulations of this
phenomenum, which I called “social embedding” (Edmonds 1999a). When it occurs
it can increase the computational efficiency of that population but also means
that the absolute success of that population may drop slightly over time
(especially if only relative success among the agents is important to the
participants, as in competitive situations).

In my simulations
(Edmonds 1999a) I found that new agents (or new models introduced by existing
agents) typically either do relatively badly when introduced to the population
or (more rarely) very well.The new
agents are not well embedded in the society and hence can not immediately make
use of the computational resources implicit in the available “proxies” (since
they do not know how to use or interpret these). However they may happen upon a
better model than those current in the established population due to the fact
they are not embedded.If the model is
much better than existing models it will do much better than the rest and
quickly become established as a proxy for use by others. If its models are only
marginally better, their objective superiority may not be sufficient to
counter-act the efficiency of the embedded computation occurring in the
population. In this latter case the model may eventually be discarded despite
its marginal superiority in conventional terms.

Figure 2 below is an
illustration of some of the causal links between each agent’s best models
(represented by a single box) during the last three time periods of the
simulation.A line means that a model
explicitly uses the output of a previous model.For some of the models (indicated by a high number in the box)
their results depend upon the results of several previous models that
themselves depend upon previous models etc.In fact this chain stretches back over a very large amount of time and
involves a large proportion of the total population.In such cases it is sometimes much simpler to explain the actions
and in terms other than the detailed web of reference and the explicit content
of the models if taken alone.The
practical effect and meaning of the agent’s models comes from the web of social
interaction to a considerable extent.

Fig. 2. A causation network going back
over the simulation time at the end of a simulation (from Edmonds 1999a)

Such models illustrate
why it could be a lot more comfortable to participate in a process of “normal
science”. Once one has become accepted into a field (i.e. becomes embedded in it)
one can participate in a complementary process of problem solving, by
specialising in a certain area and building on each other’s work. The
efficiency of a socially embedded group, its accompanying tendency to encourage
specialisation and the provision of an established framework mean that one’s
work is far less onerous. The fact that others may come to accept one as a
“proxy” in certain areas means that one’s status (and hence ones job) is
relatively secure. Here the picture is of a communal building-up of a wall of
knowledge: each brick needs careful checking so that it can support those that
will be placed on top of it.

A life pursuing
“revolutionary” science is much less comfortable. One does not know how one’s
ideas will fare – they may succeed if they are significantly better than
existing models to justify their acceptance or they may completely fail. Rather
than participating in a complementary process of specialised problem-solving
one is involved in sharp competition. Unless one succeeds in causing minor
revolutions one will have to endure being permanently relegated to the fringes.
Here we have more of an evolutionary picture: a constant stream of new variant
models and theories are being produced which are then weeded-out according to
their acceptance amongst peers – instead of being built-up, knowledge is
constantly being adapted to meet current needs.

Clearly these
different modes of science will attract and be suitable to different types of
people. Both processes are needed and hence both types of people are needed.
The ideal (viewed from outside) would be that: “normal science” should
predominate in areas where an empirically successful theoretical framework has
been found (e.g. chemistry), so that the maximum possible benefit can be efficiently
extracted; while “revolutionary science” should be encouraged in areas where
empirical progress is inadequate (e.g. economics).

Unfortunately, it
often seems to occur the opposite way around: empirically unsuccessful sciences
(the “degenerate research programmes” of Lakatos 1983) seem to covert the garbs
of “normal science” in order to claim academic respectability whereas
successful sciences display the confidence to allow the presence of
revolutionaries. Of course, this may be the wrong way around: it may be that
allowing revolutions is necessary for the success of a science, due to the
stability of highly embedded groups and the self-justifying nature of
theoretical frameworks, and that fields which constrain progress to small
advances within established frameworks inevitably stagnate.

Foundational vs. Empirical Approaches

The approach whereby
one starts by postulating quite abstract, a priori principles and then tries to
demonstrate that, with the addition of auxiliary assumptions, that the
consequences are adequate to the domain of study can be called a
“foundationalist” approach. An approach with more emphasis on starting with the
observations or problems derived from the domain of study, postulating
appropriate models for each of these and later generalizing these to theories
can be called an “empirical” approach.

Both the foundational
and empirical approaches are only completely successful if they complete the
chain all the way from problems or observations in the domain of study up to
some more generally applicable theories (as described above).If the foundationalist approach achieves
only weak verification against “toy” problems then its relevance remains in
doubt.If the empirical approach does
not manage to achieve generality to the extent that aspects of a model for one
situation are applicable to another situation then it is not very useful.

Both approaches have
their part to play.The foundationalist
approach has had most success in well-defined and measurable domains such as
mathematics, physics and computer science, but even in these fields there are
distinct limitations.The
foundationalist approach has also had a productive role in creating a large
variety of formal systems for the empirical scientist to choose among (and a
less glorious role in providing straw men to be knocked down).

The empirical approach
has been more successful in complex domains such as biology and the social
sciences.These are areas where our
intuitions are weak and frequently misleading. This approach has the hard task
of establishing reliable mappings from the real world of phenomena and problems
to formal (or formal sable) theories - it is this that makes the formal system
useful because it means that inference within the formal system produces
conclusions that successfully relate back to the world.

Not all foundations
are a priori in origin.For example
atomic physics provides empirically verified foundations for chemistry.This has been a productive way forward - to
choose foundations that have been empirically verified. This contrasts with
foundations that have only weak grounding, what could be called “armchair
grounding” because they could have been invented from a philosopher's armchair.

Of course, it is
impossible to avoid a priori assumptions and systems altogether - one is bound
to use some framework to aid one to look for data and formulate
hypotheses. However this does not change the fact that the more a formalism
directly relates to real observations and problems and the more flexible one
can be about which formalism is deployed the better.

Simplicity – a solely pragmatic
virtue

An ‘old chestnut’ that
is often brought out to justify the introduction of otherwise unsupported a
priori assumptions and structures is that it is for the sake of simplicity.The implication is often that this has
virtues other than the obvious pragmatic ones of making it easier to construct,
communicate and analyse.There has been
a (disputed) tradition in the philosophy of science that the simplicity is
truth-indicative (that is, it is something that is a useful guide to the
truth).This is traced back to William
Of Occam who used the maxim “entities are not to be needlessly multiplied”.

The fact is that there
is no evidence or good argument to show that simplicity is truth-indicative in
general.In fact, when machines have
been set to comprehensively search all possible models in a given formal
language to compare their accuracy and their simplicity on real data then it
can be seen that this maxim does not hold.Further there is an alternative explanation for why simpler models can
be preferred without having to introduce a separate and mysterious connection
between simplicity and truth: that it is common to elaborate unsuccessful
models, which means that if one comes across a model which has been frequently
elaborated then this is an indication it has been unsuccessful. Thus Occam’s
razor eliminates itself!This
explains why a large part of the philosophy on this principle has been
concerned with inventing different interpretations of “simplicity” in order to
try and make the principle true – the principle is unsuccessful and is
undergoing elaboration.

Constructivist vs. Realist Viewpoints

If the social
embedding picture of “normal” science is correct, then this has the implication
that the constructivist picture of their activity is, at least, somewhat
valid.The models that are developed
are constrained by the product of other agents since the computational cost of
always developing new models inevitably biases model development.This does not mean that the models developed
are necessarily incorrect or sub-optimal, but that the implied lack of
input variety does suggest that this is probably the case.In the simulations of social embeddedness I
ran socially embedded populations did develop models that were slightly worse
than non-socially embedded populations, but only by a small margin.However it might be the case that in the
long run this difference (which indicated a loss of variety) would be
significant.Socially embedded
populations might eventually close in on the best models of their set but be
unable to ever branch out to explore different (and possibly better) models.

Thus one can see the
“revolutions” in science as ‘steps’ towards a more realistic set of models –
steps where the improvement in the explanatory power of a model overwhelms the
processes of social construction.There
is some anecdotal evidence that such revolutions have happened when gifted and
hard-working individuals who are not socially embedded posit new models guided
substantially by the observations and data to be explained rather than by other
people’s approaches.

Conclusion

Just as it is
important for engineers to know the strengths and weaknesses of the material
with which they are going to build, so it is important That builders of formal
systems know the strength and weaknesses of different methodologies.

An empirical
methodology is more likely to arrive at the truth, because it starts with what
is directly verifiable in the target domain. It starts with messy
“phenomenological laws” (Cartwright 1983) and later attempts to draw
generalizations. This requires a lot of effort both in terms of fieldwork and
invention (as it is unlikely that an “off-the-shelf” formal system will work
without modification).If
generalization is successfully achieved the effect may be revolutionary as it
has not been developed within established frameworks.When generalization is weak then the theories remain messy and
difficult to apply.

A foundationalist approach
takes much less effort or, to put it positively, is far more efficient in terms
of collective effort.It is most
effective when the framework within which it works is itself empirically
well-verified. In fact, the better an empirically-based revolutionary theory,
the more it supports and encourages a successful foundationalist approach in
its wake.Foundationalist approaches
are prone to being mislead by the formal spectacles they use to model, what
they add is not so much truth content, as simplification and a framework for
coordinated collective action.

A new formal system
that is presented in an a priori fashion that is unjustified in terms of its
usefulness in a domain has no place in the furthering of real knowledge,
despite its social function and status within a socially embedded group. Such a
presentations can usually be recognised by a number of tell-tale signs,
including:

The lack of empirically verified
foundations – the fact that its basis could have been invented in a
“philosophers armchair” without detailed justification in terms of
observations or known facts from the problem domain or phenomena;

The fact that it is verified only against
highly abstract and artificial “toy” problems, rather than against real
data or a real problem;

That the application to real problem
domains (i.e. the final verification of a model chain as described above)
are left for “future research” or simply dismissed as “scaling problems”;

The emphasis on purely descriptive formal
virtues and the lack of any pragmatic justification of formalism systems
or substantial theories;

The conflation of an idealized problem
domain with a real one, without explicit recognition of the difficulties
of bridging the gap;

The lack of explicit exhibition of the
disadvantages of a system to balance its claimed advantages, especially
when the key advantage is generality.

Acknowledgments

Scott Moss, with whom
I have discussed these issues for so long that it is now very difficult to
identify who thought of which idea first, Pat Hayes whose clear arguments
spurred on these thoughts.

References

Cartwright, N. (1983). How the Laws of Physics Lie.
Oxford: Oxford University Press.

Edmonds, B. (1997). Complexity and Scientific Modelling.
20th International Wittgenstein Symposium, Kirchberg am Wechsel, Austria,
August 1997. To be published in Foundations of Science.
http://cfpm.org/cpmrep23.html