BEHAVIORAL AND BRAIN SCIENCES (1994) 17, 43-104
Printed in the United States of America
Neuropsychological inference with
an interactive brain: A critique of
the "locality" assumption
Martha J. Farah
Department of Psychology, University of Pennsylvania, Philadelphia, PA
19104-6196
Electronic mail: mfarah@cattell.psych.upenn.edu
Abstract: When cognitive neuropsychologists make inferences about the functional architecture of the normal mind from selective
cognitive impairments they generally assume that the effects of brain damage are local, that is, that the nondamaged components of
the architecture continue to function as they did before the damage. This assumption follows from the view that the components of the
functional architecture are modular, in the sense of being informationally encapsulated. In this target article it is argued that this
"locality" assumption is probably not correct in general. Inferences about the functional architecture can nevertheless be made from
neuropsychological data with an alternative set of assumptions, according to which human information processing is graded,
distributed, and interactive. These claims are supported by three examples of neuropsychological dissociations and a comparison of
the inferences obtained from these impairments with and without the locality assumption. The three dissociations are: selective
impairments in knowledge of living things, disengagment of visual attention, and overt face recognition. In all three cases, the
neuropsychological phenomena lead to more plausible inferences about the normal functional architecture when the locality
assumption is abandoned. Also discussed are the relations between the locality assumption in neuropsychology and broader issues,
including Fodor's modularity hypothesis and the choice between top-down and bottom-up research approaches.
Keywords: brain lesions; cognitive architecture; face recognition; localization; modularity; neural nets; neuropsychology; semantics;
The fact that the various parts of the encephalon, though
anatomically distinct, are yet so intimately combined and
related as to form a complex whole, makes it natural to
suppose that lesions of greater or lesser extent in any one part
should produce such general perturbation of the functions of
the organ as a whole as to render it at least highly difficult to
trace any uncomplicated connection between the symptoms
produced and the lesion as such.
Ferrier (1886)
1. Introduction
Brain damage often has rather selective effects on cognitive
functioning, impairing some abilities while sparing
others. Psychologists interested in describing the "functional
architecture" of the mind, that is, the set of relatively
independent information-processing subsystems
that underlies human intelligence, have recognized that
patterns of cognitive deficit and sparing after brain damage
are a potentially useful source of constraints on the
functional architecture. In this target article I wish to
focus on one of the assumptions that frequently underlies
the use of neuropsychological data in the development of
cognitive theories.
1.1. The locality assumption
Cognitive neuropsychologists generally assume that damage
to one component of the functional architecture will
have exclusively "local" effects. In other words, the nondamaged
components will continue to function normally
and the patient's behavior will therefore manifest the
underlying impairment in a relatively direct and straightforward
way. This assumption follows from a view of the
cognitive architecture as "modular," in the sense of being
"informationally encapsulated' (Fodor 1983; see also multiple
book review, BBS 8(1)1985).
According to this version of the modularity hypothesis,
the different components of the functional architecture do
not interact with one another except when one has completed
its processing, at which point it makes the end product
available to other components. Even these interactions
are limited, so that a given component receives input
from relatively few (perhaps just one) of the other components.
Thus, a paradigm module takes its input from just
one other component of the functional architecture (e.g.,
phonetic analysis would be hypothesized to take its input
just from prephonetic acoustic analysis), carries out its
computations without being affected by other information
available in other components (even potentially relevant
information, such as semantic context), and then presents
its output to the next component in line, for which'it might
be the sole input (e.g., the auditory input lexicon, which
© 1994 Cambridge University Press 0140-525X194 S5.00+.00 43
Farah: Neuropsychological inference
would again be hypothesized to take only phonetic input).
In such an architecture, each component minds its own
business and knows nothing about most of the other
components. What follows for a damaged system is that
most of the components will be oblivious to the loss of any
one, carrying on precisely as before. If the components of
the functional architecture were informationally encapsulated
then the locality assumption would hold; the removal
ofone component would have only very local effects on the
functioning ofthe system as awhole, affectingperformance
only in those tasks that directly call upon the damaged
component. Indeed, one of Fodor's other criteria for
modulehood, which he suggests will coincide with informational
encapsulation, is that modules make use of
dedicated hardware and can therefore be selectively impaired
by local brain damage. In contrast, if the different
components of the cognitive system were highly interactive,
each one depending on input from many or most of the
others, then damage to any one component could significantly
modify the functioning of the others.
Several cognitive neuropsychologists have pointed out
that informational encapsulation and the locality of the
effects of brain damage are assumptions, and they have
expressed varying degrees of confidence in them (Allport
1985; Caplan 1981; Humphreys & Riddoch 1987; Kinsbourne
1971; Kosslyn & Van Kleek 1990; Moscovitch &
Umilta 1990; Shallice 1988; von Klein 1977). For example,
Shallice (1988, Ch. 2) endorses a weaker and more general
version of modularity than Fodor's, according to which
components of the functional architecture can be distinguished,
(1) conceptually in terms of their specialized
functions and (2) empirically by the relatively selective
deficits that ensue upon damage to one of them. He likens
this concept of modularity to Posner's (1978) "isolable
subsystems" and offers the followingcriterion from Tulving
(1983) for distinguishing modular systems with some mutual
dependence among modules from fully interactive systems:
components ofa modular system in this weaker sense
may not operate as efficiently when other components
have been damaged but they will nevertheless continue to
function roughly normally. According to this view, the
locality assumption is not strictly true, but it is nevertheless
roughly true: one would not expect pronounced
changes in the functioning of nondamaged components.
Closely related to the locality assumption is the "transparency
assumption" of Caramazza (1984; 1986). Although
different statements ofthis assumption leave room
for different interpretations, it is probably weaker than
the locality assumption. Particularly in more recent statements
(e.g., Caramazza 1992), it appears transparency
requires only that the behavior of the damaged system be
understandable in terms of the functional architecture of
the normal system. Changes in the functioning of nondamaged
components are not considered a violation of the
transparency assumption so long as they are understandable.
In particular, interactivity and consequent nonlocal
effects are permitted; presumably only if the nonlocal
interactions became unstable and chaotic would the transparency
assumption be violated.
Unlike the weaker transparency assumption, the locality
assumption licenses quite direct inferences from
the manifest behavioral deficit to the identity of the
underlying damaged cognitive component, inferences of
the form "selective deficit in ability A implies a component
of the functional architecture dedicated to A." Obviously
such inferences can go awry if the selectivity of the
deficit is not real, for example, if the tasks testing A are
merely harder than the comparison tasks, if there are
other abilities that are not tested but are also impaired, or
if a combination of functional lesions is mistaken for a
single one (see Shallice 1988, Ch. 10, for a thorough
discussion of other possibilities for misinterpreting dissociations
in a weakly modular theoretical framework). In
addition, even simple tasks tap several components at
once, and properly designed control tasks are needed to
pinpoint the deficient component and absolve intact components
downstream. However, assuming that the relevant
ability has been experimentally isolated and that the
deficit is truly selective, the locality assumption allows us
to delineate and characterize the components of the
functional architecture in a direct, almost algorithmic
way.1
1.2. The locality assumption is ubiquitous in cognitive
neuropsychology
At this point the reader may think that the locality
assumption is naive and that the direct inferences that it
licenses constitute a mindless reification of deficits as
components of the cognitive architecture, something
"good" cognitive neuropsychologists would not do. Note,
however, that the locality assumption is justifiable in
terms of informational encapsulation. Furthermore,
whether or not this seems an adequate justification, many
of the best-known findings in neuropsychology fit this
form of inference. A few examples will be given here and
three more will be discussed in detail later (perusal of
recent journals and textbooks in cognitive neuropsychology
will reveal many more examples).
With the domain of reading, phonological dyslexics
show a selective deficit in tasks that require grapheme-tophoneme
translation; they are able to read real words
(which can be read by recognizing the word as a whole),
they can copy and repeat nonwords (demonstrating intact
graphemic and phonemic representation), but they cannot
read nonwords, which must be read by grapheme-tophoneme
translation. This has been interpreted as an
impairment in a grapheme-to-phoneme translation
mechanism and hence as evidence for the existence of
such a mechanism in the normal architecture (e.g., Coltheart
1985). Similarly, in surface dyslexia a selective
deficit in reading irregular words with preserved regular
word and nonword reading has been used to identify
a deficit in whole-word recognition and hence to infer
a whole-word reading mechanism distinct from the
grapheme-to-phoneme route (e.g., Coltheart 1985).
In the production and understanding of spoken language,
some patients are selectively impaired in processing
closed class, or "function" words, leading to the
conclusion that these lexical items are represented by a
separate system, distinct from open class or "content"
words (e.g., Zurif 1980).
In the domain of vision, some right hemispheredamaged
patients show an apparently selective impairment
in the recognition of objects viewed from unusual
perspectives. This has been taken to imply the existence
of a s*we or stages of visual information processing concerned
specifically with shape constancy (e.g., Warrington
1985). Highly selective deficits in face recognition
44 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Farah: Neuropsychological inference
have been taken to support the existence of a specialized
module for face recognition, distinct from more generalpurpose
recognition mechanisms (e.g., DeRenzi 1986).
In the domain of memory, the finding that patients can
be severely impaired in learning facts and other so-called
declarative or explicit knowledge while displaying normal
learning of skills and other forms of implicit knowledge is
interpreted as evidence for multiple learning systems,
one of which is dedicated to the acquisition of declarative
knowledge (e.g., Squire 1992).
Some of these inferences may well be proved wrong in
the light of further research. For example, perhaps there
is a confounding between the factor of interest and the
true determinant of the deficit. In the case of aphasics
who seem selectively impaired at processing closed class
words, perhaps speech stress pattern, and not lexical
class, determines the boundaries of the deficit. Critical
thinkers may find reasons to question the inferences in
any or all of the examples given above. However, note that
in most cases the question will concern the empirical
specifics of the case, such as stress pattern versus lexical
class. In the course of scientific debate on these and other
deficits, the form of the inference is rarely questioned. If
we can truly establish a selective deficit in ability A then it
seems reasonable to attribute the deficit to a lesion of
some component of the functional architecture that is
dedicated to A, that is, necessary for A and necessary only
for A. We are, ofcourse, thereby assuming that the effects
of the lesion on the functioning of the system are local to
the lesioned component.
7.3. Two empirical Issues about the locality assumption
Although it is reasonable to assume that the effects of a
lesion are confined to the operation of the lesioned components
and the relatively small number of components
downstream in a system with informationally encapsulated
modules, we do not yet know whether the brain is
such a system. There is, in fact, some independent reason
to believe it is not. Neurologists have long noted the
highly interactive nature of brain organization and the
consequent tendency for local damage to unleash new
emergent organizations or,modes of functioning in the
remaining system (e.g., Ferrier 1886; Jackson 1873). Of
course, the observations that led to these conclusions
were not primarily of cognitive disorders. Therefore,
whether or not the locality assumption holds in the
domain of cognitive impairments, at least to a good
approximation, is an open empirical question.
Note that we should be concerned more about "good
approximations" than precise generalizations to neuropsychological
methodology. As already mentioned, Shallice
(1988) has pointed out that modularity versus interactionism
is a matter of degree. From the point of view of
neuropsychological methodology, if nonlocal interactions
were to modulate weakly the behavior of patients after
brain damage, this would not necessarily lead to wrong
inferences using the locality assumption. In such a case,
in which the remaining parts of the system act ever-soslightly
differently following damage, the cognitive neuropsychologist
would simply fail to account for 100% of
the variance in the data (not a novel experience for most of
us) but would make the correct inference about functional
architecture. If deviations from locality were a first-order
effect, however, then the best-fitting theory for the data
using the locality assumption would be false.
There is a second question concerning the locality
assumption: Is it really indispensable to cognitive neuropsychology?
Must we abandon all hope of relating patient
behavior to theories of the normal functional architecture
if lesions in one part of the system can change the
functioning of other parts? Like the first question, this
one too is a matter of empirical truth or falsehood.
Nevertheless, unlike many empirical questions, these
two are not of the type that lend themselves to single
critical experiments. They concern very general properties
of the functional architecture of cognition and our
ability to make scientific inferences about complex systems
using all the formal and informal methods and types
of evidence available to us. The most fruitful approach to
answering these two questions would therefore involve an
analysis of the body of cognitive neuropsychological research,
or at least an extensive sample of it.
As a starting point, I will describe three different
neuropsychological dissociations that have been used to
make inferences about the functional architecture of the
mind. The aspect of cognition under investigation in each
case is different: semantic memory, visual attention, and
the relation between visual recognition and awareness.
What all three have in common is the use of the locality
assumption. For each I will explore alternative inferences
about the functional architecture that are not constrained
by the locality assumption.
How will such explorations answer the questions posed
above? We can assess the empirical basis for the locality
assumption by comparing the conclusions about functional
architecture that are arrived at with and without it.
Specifically, we can determine which conclusions are
preferable, in the sense of being simpler and according
better with other, independent evidence about the functional
architecture. If the locality assumption generally
leads to preferable conclusions, this suggests that we are
probably justified in using it. However, if it often leads to
nonpreferable conclusions, this suggests we should not
assume that the effects of brain damage on the functioning
of the cognitive architecture are local. The question of
whether it is possible to draw inferences about the functional
architecture from neuropsychological dissociations
without the locality assumption will also be addressed by
the degree to which sensible conclusions can be reached
without it.
1.4. An architecture for interactive processing
Of course, comparisons between the results of inferences
made with and without the locality assumption will be
meaningful only if both types of inferences are constrained
in principled ways. The locality assumption is
one type of constraint on the kinds of functional architectures
that.can be inferred from a neuropsychological
dissociation. It limits the elements in our explanation of a
given neuropsychological deficit to just those in the normal
functional architecture (minus the damaged component),
operating in their normal fashion. If we simply
eliminate that constraint without replacing it with other
principled constraints on how local damage affects the
remaining parts of the system then the comparison proposed
above will not be fair to the locality assumption. We
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 45
Farah: Neuropsychological inference
could, of course, pick the simplest, most appealing model
of the normal functional architecture and say "the way in
which the remaining parts of the system change their
functioning after damage produces this deficit," without
saying why we chose to hypothesize that particular
change in functioning as opposed to some other that
cannot explain the deficit.
The parallel distributed processing (PDP) framework
will be used as a source of principled constraints on the
ways in which the remaining parts of the system behave
after local damage. Computer simulation will be used to
test the sufficiency of the PDP hypotheses to account for
the dissociations in question. Readers who would like a
detailed introduction to PDP are referred to Rumelhart
and McClelland's (1986) collection of readings. For present
purposes, the relevant principles of PDP are:
Distributed representation of knowledge. In PDP systems,
representations consist of patterns of activation
distributed over a population of units. Different entities
can therefore be represented using the same set of units,
because the pattern of activation over the units will be
distinctive. Long-term memory knowledge is encoded in
the pattern of connection strengths distributed among a
population of units.
Graded nature of information processing. In PDP
systems processing is not all or none: representations can
be partially active, for example, through partial or subthreshold
activation of some of those units that would
normally be active. Partial knowledge can be embodied in
connection strengths, either before learning has been
completed or after partial damage.
Interactivity. The units in PDP models are highly
interconnected and thus mutual influence among different
parts of the system is the rule rather than the exception.
This influence can be excitatory, as when one part of
a distributed representation activates the remaining parts
(pattern completion), or it can be inhibitory, as when
different representations compete with one another to
become active or to maintain their activation. Note that
interactivity is the aspect of the PDP framework that is
most directly incompatible with the locality assumption.
If the normal operation of a given part of the system
depends on the influence of some other part, it may not
operate normally after that other part has been damaged.
The psychological plausibility of PDP is controversial
but it need not be definitively established here before
proceeding. Instead, just as locality is being identified as
an assumption and evaluated, so PDP is to be evaluated as
a specific alternative assumption. In addition, as will be
discussed further in the "General Discussion" (sect. 3),
much of the controversy surrounding PDP concerns its
adequacy for language and reasoning. It is possible that
the arguments advanced here will not generalize to these
cognitive domains.
2. Reinterpreting dissociations without the
locality assumption: Three case studies
2.1. The functional architecture of semantic memory:
Category-specific?
The existence of patients with apparent category-specific
impairments in semantic memory knowledge has led to
the inference that semantic memory has a categorical
organization, with different components dedicated to
representing knowledge from different categories. The
best-documented forms of category-specific knowledge
deficit (as opposed to pure naming or visual recognition
deficits) are the deficits in knowledge of living and nonliving
things.
2.1.1. Evidence for selective impairments in knowledge of
living and nonliving things. Beginning in the 1980s, Warrington
and her colleagues began to report the existence
of patients with selective impairments in knowledge of
either living or nonliving things (Warrington & McCarthy
1983; 1987; Warrington & Shallice 1984). Warrington and
Shallice (1984) described four patients who were much
worse at identifying living things (animals, plants) than
nonliving things (inanimate objects); all four had recovered
from herpes encephalitis and had sustained bilateral
temporal lobe damage. Two of the patients were studied
in detail and showed a selective impairment for living
things across a range of tasks, both visual and verbal.
Table 1 shows examples of their performance in a visual
identification task (in which they were to identify by name
or description the item shown in a colored picture) and in
a verbal definition task (in which the names of these same
items were presented auditorially and they were to define
them). Examples of their definitions are shown in Table 2.
Other cases of selective impairment in knowledge of
living things include additional postencephalitic patients
described by Pietrini et al. (1988), Sartori and Job (1988),
and Silveri and Gianotti (1988), a patient with encephalitis
and strokes described by Newcombe et al. (in press), two
head injury patients described by Farah et al. (1991), and
a patient with a focal degenerative disease described by
Basso et al. (1988). In all these cases there was damage to
the temporal regions, known to be bilateral except in
Pietrini et al.'s case 1 and the case of Basso et al., where
there was evidence only of left temporal damage.
The opposite dissociation, namely, impaired knowledge
of nonliving things with relatively preserved knowledge
of living things, has also been observed. Warrington
and McCarthy (1983; 1987) described two cases of global
dysphasia following large left-hemisphere strokes in
which semantic knowledge was tested in a series of
matching tasks. Table 3 shows the results of a matching
task in which the subjects were asked to point to the
picture in an array that corresponded to a spoken word.
Table 1. An impairment in knowledge of living things:
Performance on two tasks assessing knowledge
of living and nonliving things
Case Task
JBR
SBY
JBR
SBY
Picture identification
Living (%) Nonliving (%)
6 90
0 75
Spoken word definition
Living (%) Nonliving (%)
8 79
0 52
46 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Farah: Neuropsychological inference
Case
Table 2. Examples of definitions of living
and nonliving things
Definition
Living Tilings
JBR Parrot: don't know
Daffodil: plant
Snail: an insect animal
Eel: not well
Ostrich: unusual
SBY Duck: an animal
Wasp: bird that flies
Crocus: rubbish material
Holly: what you drink
Spider: a person looking for things, he was a spider
for his nation or country
Nonliving things
JBR Tent: temporary outhouse, living home
Briefcase: small case used by students to carry
papers
Compass: tools for telling direction you are going
Torch: hand-held light
Dustbin: bin for putting rubbish in
SBY Wheelbarrow: object used by people to take material
about
Towel: material used to dry people
Pram: used to carry people, with wheels and a
thing to sit on
Submarine: ship that goes underneath the sea
Umbrella: object used to protect you from water
that comes
Their performance with animals and flowers was more
reliable than with nonliving things. One subject was also
tested with a completely nonverbal matching task in
which different-looking depictions of objects or animals
were to be matched to one another in an array; the same
selective preservation of knowledge of animals relative to
inanimate objects was found.
Although these patients are not entirely normal in their
knowledge of the relatively spared category, they are
markedly worse at recognizing, defining, or answering
questions about items from the impaired category. The
existence of a double dissociation makes it unlikely that a
sheer difference in difficulty underlies the apparent selectivity
of the deficits; some of the studies cited above tested
several alternative explanations of the impairments in
terms of factors other than semantic category (such as
name frequency, familiarity, etc.) and failed to support
them.
2.1.2. Interpretation of "living things" and "nonliving
things" deficits relative to the functional architecture of
semantic memory. Using the locality assumption, the
most straightforward interpretation of the double dissociation
between knowledge of living and nonliving things
is that they are represented by two separate categoryspecific
components of the functional architecture of
semantic memory. A related interpretation is that semantic
memory is represented using semantic features such as
"animate," "domestic," and so on, and that the dissociations
described here result from damage to these features
(Hillis & Caramazza 1991). In either case, the dissociations
seem to imply a functional architecture for semantic
memory that is organized along rather abstract semantic
or taxonomic lines. Figure 1 represents a categoryspecific
model of semantic memory and its relation to
visual perception and language.
Warrington and colleagues, however, have suggested
an alternative interpretation, according to which semantic
memory is fundamentally modality-specific. They argue
that selective deficits in knowledge of living and
nonliving things may reflect the differential weighting of
information from different sensorimotor channels in representing
knowledge about these two categories. They
have pointed out that living things are distinguished
primarily by their sensory attributes, whereas nonliving
things are distinguished primarily by their functional
attributes. For example, our knowledge of an animal such
as a leopard, by which we distinguish it from other similar
creatures, is predominantly visual. In contrast, our
knowledge of a desk, by which we distinguish it from
other furniture, is predominantly functional (i.e., what it
is used for). Thus, the distinctions between impaired and
preserved knowledge in the cases reviewed earlier may
not be living/nonliving distinctions per se but sensory/functional
distinctions, as illustrated in Figure 2.
The modality-specific hypothesis seems preferable to a
Table 3. An impairment in knowledge of nonliving things:
Performance on two tasks assessing knowledge
of living and nonliving things
Case
VER
YOT
YOT
Task
Spoken word/picture matching
Animals (%) Flowers (%) Objects (%)
86 96 63
86 86 67
Picture/picture matching
Animals (%) Objects (1
100 69
Living
Things
Semantics
Nonliving
Things
Names Vision
Figure 1. Category-specific functional architecture for semantic
memory.
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 47
Farah: Neuropsychological inference
Figure 2. Modality-specific functional architecture for semantic
memory.
strict semantic hypothesis for two reasons. First, it is
more consistent with what is already known about brain
organization. It is well known that different brain areas
are dedicated to representing information from specific
sensory and motor channels. Functional knowledge could
conceivably be tied to the motor system. A second reason
for preferring the sensory/functional hypothesis to the
living/nonliving hypothesis is that exceptions to the latter
have been observed in certain cases. For example, Warrington
and Shallice (1984) report that their patients, who
were deficient in their knowledge of living things, also
had impaired knowledge of gemstones and fabrics. Warrington
and McCarthy's (1987) patient, whose knowledge
of most nonliving things was impaired, seemed to have
retained good knowledge of very large outdoor objects
such as bridges or windmills. It is at least, possible that our
knowledge of these aberrant categories of nonliving
things is primarily visual.
Unfortunately, there appears to be a problem with the
hypothesis that "living-thing impairments" are just impairments
in sensory knowledge, and "nonliving-thing
impairments" are just impairments in functional knowledge.
This hypothesis seems to predict that cases of
living-thing impairment should show good knowledge
of the functional attributes of living things and cases of
nonliving-thing impairment should show good knowledge
of the visual attributes of nonliving things. The evidence
available in cases of nonliving-thing impairment is limited
to performance in matching-to-sample tasks, which does
not allow us to distinguish knowledge of visual or sensory
attributes from knowledge of functional attributes. However,
there does appear to be adequate evidence in cases
of living-thing impairment, and in at least some cases it
disconfirms these predictions (for review see Farah &
McClelland 1991). For example, although the definitions
of living things shown in Table 2 contain little visual
detail, in keeping with the sensory/functional hypothesis,
they are also skimpy on functional information. If these
cases had lost just their visual semantic knowledge, then
why could they not retrieve functional attributes of living
things, for example, the fact that parrots are kept as pets
and can talk, that daffodils are a spring flower, and so on?
A more direct and striking demonstration of the apparently
categorical nature of the impairment is provided by
Newcombe et al. (in press), whose subject was impaired
relative to normal subjects in his ability to sort living
things according to such nonsensory attributes as whether
or not they were generally found in the United Kingdom,
in contrast to his normal performance when the task
involved nonliving things.
In sum, the sensory/functional hypothesis seems preferable
to the living/nonliving hypothesis because it is
more in keeping with what we already know about brain
organization. However, it is not able to account for the
impaired ability of these patients to retrieve nonvisual
information about living things.
2.1.3. Accounting for category-specific impairments with
an interactive modality-specific architecture. Jay McClelland
and I have modeled the double dissociation between
knowledge of living and nonliving things using a simple
autoassociative memory architecture with modalityspecific
components (Farah & McClelland 1991). We
found that a two-component semantic memory system,
consisting of visual and functional components, could be
lesioned to produce selective impairments in knowledge
of living and nonliving things. More important, we found
that such a model could account for the impairment of
both visual and functional knowledge of living things.
The basic architecture of the model is shown in Figure
2. There are three pools of units, representing the names
of items, the perceived appearances of items, and the
semantic memory representations of items. The semantic
memory pool is subdivided into visual semantic memory
and functional semantic memory. An item, living or
nonliving, is represented by a pattern of +1 and - 1
activations over the name and visual units, and a pattern
of +1 and —1 activations over a subset of the semantic
units. The relative proportion of visual and functional
information comprising the semantic memory representation
of living and nonliving things was derived empirically.
Normal subjects identified terms in dictionary definitions
of the living and nonliving items used by
Warrington and Shallice (1984) as referring to either
visual or functional properties. This experiment confirmed
that visual and functional information was differentially
weighted in the definitions of living and nonliving
things and the results were used to determine the average
proportions of visual and functional units in semantic
memory representations of living and nonliving items.
For the living items, about seven times as many visual
semantic units than functional ones participated in the
semantic memory pattern; for nonliving items the proportions
were closer to equal. Units of semantic memory not
involved in a particular item's representation took the
activation value of 0.
The model was trained using the delta rule (Rumelhart
et al. 1986) to associate the correct semantic and name
portions of its pattern when presented with the visual
portion as input, and the correct semantic and visual
portions when presented with the name portion as input.
It was then damaged by eliminating different proportions
of functional or visual semantic units and its performance
was assessed in a simulated picture-name matching task.
In this task, each item's visual input representation is
presented to the network and the pattern activated in the
name units is assessed, or each pattern's name is pre-
48 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
sented and the resultant visual pattern is assessed. The
resultant pattern is scored as correct if it is more similar to
the correct pattern than to any of the other 19 patterns.
Figure 3A shows the averaged picture-to-name and
name-to-picture performance of the model for living and
nonliving items under varying degrees of damage to
visual semantics. With increased damage, the model's
performance drops, and it drops more precipitously for
living things, in effect showing an impairment for living
things comparable in selectivity to that of the patients in
the literature. Figure 3B shows that the opposite dissociation
is obtained when functional semantics is damaged.
The critical challenge for a modality-specific model of
semantic memory is to explain how damage could create
an impairment in knowledge of living things that includes
A. 10
0.4-
0.2-
0.0
20 40 60 80 100
% damage to visual semantic memory
B.
a
0.6
0.4
0.2
0.0
•o- Nonliving
•*- living
20 40 60 80 100
% damage to functional semantic memory
Figure 3. A: Effects of different degrees of damage to visual
semantic memory units on ability of network to associate names
and pictures of living things (diamonds) and nonliving things
(squares). B: Effects ofdifferent degrees ofdamage to functional
semantic memory units on ability of network to associate names
and pictures of living things (diamonds) and nonliving things
(squares).
Farah: Neuropsychological inference
functional knowledge of living things. To evaluate the
model's ability to access functional semantic knowledge,
we presented either name or visual input patterns as
before, but instead of assessing the match between the
resulting output pattern and the correct output pattern,
we assessed the match between the resulting pattern in
functional semantics and the correct pattern in functional
semantics. The normalized dot product of these two
patterns, which provides a measure between 0 (completely
dissimilar) and 1 (identical), served as the dependent
measure.
Figure 4 shows the accuracy with which functional
semantic memory information could be activated for living
and nonliving things after different degrees of damage
to visual semantics. At all levels of damage, the ability to
retrieve functional semantic knowledge of living things is
disproportionately impaired.
These dissociations can be understood as follows. In the
case of picture-name matching, the ability of a given
output unit (e.g., a name unit, in the case of picture-toname
matching) to attain its correct activation value
depends on the input it receives from the units to which it
is connected. These consist of other name units (collateral
connections) and both visual and functional semantic
units. Hence the more semantic units that have been
eliminated, the more the output units are deprived of the
incoming activation they need to attain their correct
activation values. Because most of the semantic input to
the name units of living things is from visual semantics,
whereas the same is not true for nonliving things, damage
to visual semantics will eliminate a greater portion of the
activation needed to retrieve the name patterns for living
things than nonliving things, and will therefore have a
more severe impact on performance.
The same principle applies to the task of activating
functional semantics, although in this case the units are
being deprived of collateral activation from other semantic
units. Thus, when visual semantic units are destroyed,
one of the sources of input to the functional semantic units
I
*
0.6-
0.4
0.2
0.0
•o- Nonliving
-•- Living
20 40 60 80 100
% damage to visual semantic memory
Figure 4. Effects of different degrees of damage to visual
semantic memory units on ability of network to activate correct
pattern in functional semantic memory units for living things
(diamonds) and nonliving things (squares).
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 49
Farah: Neuropsychological inference
is eliminated. For living things, visual semantics comprises
a proportionately larger source of input to functional
semantic units than for nonliving things, hence the
larger effect for these items.
2.1.4. Relevance of the locality assumption for architecture
of semantic memory. Contrary to the locality assumption,
when visual semantics is damaged the remaining
parts of the system do not continue to function as
before. In particular, functional semantics, which is part
of the nondamaged residual system, becomes impaired in
its ability to achieve the correct patterns of activation
when given input from vision or language. This is because
of the loss of collateral support from visual semantics. The
ability of this model to account for the impairment in
accessing functional knowledge of living things depends
critically upon this nonlocal aspect of its response to
damage.
2.2. The functional architecture of visual attention: A
"disengage" module?
One of the best-known findings in cognitive neuropsychology
concerns the "disengage" deficit that follows
unilateral parietal damage. In an elegant series of studies,
Posner and his colleagues have shown that parietally
damaged patients have a selective impairment in their
ability to disengage attention from a location in the spared
ipsilesional hemifield in order to move it to a location in
the affected contralesional hemifield (e.g., Posner et al.
1984). From this they have inferred the existence of a
disengage component in the functional architecture of
visual attention.
2.2.1. Evidence for the disengage deficit. Posner and
colleagues inferred the existence of a disengage operation
from experiments using a cued simple reaction time task.
The typical task consists of a display, as shown in Figure
5A, which the subject fixates centrally, and in which both
"cues" and "targets" are presented. The cue is usually the
brightening of one of the boxes, as depicted in Figure 5B.
This causes attention to be allocated to the region of space
around the bright box. The target, usually a simple
character such as an asterisk, is then presented in one of
A. • • •Prior to cue
B. • •Cue
c. • •Target
Figure 5. Sequence of trial events in the lateralized simple
reaction time task: (A) fixation display; (B) cue; (C) target.
the boxes, as shown in Figure 5C. The subject's task is to
press a button as soon as possible after the appearance of
the target, regardless of its location. When the target is
"validly" cued, that is, when it occurs on the same side of
the display as the cue, reaction times to it are faster than
with no cue, because attention is already optimally allocated
for perceiving the target. When the target is "invalidly"
cued, reaction times are slower than with no cue
because attention is focused on the wrong side of space.
When parietally damaged patients are tested in this
paradigm, they perform roughly normally on validly cued
trials when the target appears on the side of space ipsilateral
to their lesion. However, their reaction times are
greatly slowed to invalidly cued contralesional targets. It
is as if once attention has been engaged on the ipsilesional,
or "good," side it cannot be disengaged to be moved
to a target occurring on the contralesional, or "bad," side.
2.2.2. Interpretation of the disengage deficit relative to the
functional architecture of visual attention. The disproportionate
difficulty that parietally damaged patients have in
disengaging their attention from the good side to move it
to the bad side has led Posner and colleagues to infer
the existence of a separate component of the functional
architecture of disengaging attention. The resulting
model of attention therefore postulates distinct components
for engaging and disengaging attention, as shown in
Figure 6.
ALERT
1
INTERRUPT
1 LOCALIZE
DISENGAGE
—
MOVE
ENGAGE
INHIBIT
Figure 6. Functional architecture of visual attention system
derived by Posner et al. (1984) from the study of brain-damaged
patients.
50 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Farah: Neuropsychological inference
2.2.3. Accounting for the disengage deficit with an interactive
architecture that has no "disengage" component.
Jonathan Cohen, Richard Romero, and I (Cohen et al., in
press) have modeled normal cuing effects and the disengage
deficit using a simple model of visual attention that
contains no "disengage" component.
The model is depicted in Figure 7. The first layer
consists of visual transducer, or input, units, through
which stimuli are presented to the network. These units
send their output to visual perception units, which represent
the visual percept of a stimulus at a particular
location in space. In this simple model there are only two
locations in visual space. The visual perception units are
connected to two other kinds of units. One is the response
unit, which issues the detection response when it has
gathered sufficient activation from the perception units to
reach its threshold. We will interpret the number of
processing cycles that intervene between the presentation
of a target to one of the visual transducer units and the
attainment of threshold activation in the response unit as
a direct correlate of reaction time.
The visual perception units are also connected to a set
of spatial attention units corresponding to their spatial
location. The spatial units are activated by the visual unit
at the corresponding location and reciprocally activate
that same unit, creating a resonance that reinforces its
activation. These reciprocal connections are what allow
the spatial attention units to facilitate perception.
The spatial attention units are also connected to each
other. For units corresponding to a given location, these
connections are excitatory, that is, they reinforce each
other's activation. The connections between units corresponding
to different locations are inhibitory. In other
words, if the units at one location are more active, they
will drive down the activation of the other location's units.
These mutually inhibitory connections are what give rise
to attentional limitations in the model, that is, the tendency
to attend to just one location at a time.
Connection strengths in this model were set by hand.
Units in the model can take on activation values between
0 and 1, have a resting value of 0.1, and do not pass on
activation to other units until their activation reaches a
threshold of 0.9.
Before the onset of a trial, all units are at resting level
Response
Attention
activation except for the attention units, which are set to
0.5 to simulate the subject's allocation ofsome attention to
each of the two possible stimulus locations. The presentation
of a cue is simulated by clamping the activation value
of one of the visual input units to 1 for the duration of the
cuing interval. Presentation of the target is then simulated
by clamping the activation value of one of the visual
input units to 1. The target is validly cued if the same
input unit is activated by both cue and target and invalidly
cued if different input units are activated. We also simulated
a neutral cuing condition in which no cue preceded
the target. The number of processing cycles needed for
the perception unit to raise the activation value of the
response unit to threshold after target onset is the measure
of reaction time. By regressing these numbers of
cycles onto the data from normal subjects, we were able to
fit the empirical data with our model.
Figure 8 shows the data from normal subjects obtained
by Posner et al. (1984) and the model's best fit to the data.
Why does our model show effects of valid and invalid
cuing? In our model, attentional facilitation due to valid
cuing is the result of both residual activation from the
Empirical Data
400.
Neutral Valid
Simulation Data
Invalid
Neutral Valid Invalid
Figure 7. Functional architecture ofvisual attention system as
modeled by Cohen et al. (in press).
Figure 8. Performance of normal subjects and network in
lateralized cued simple reaction time task. Number of cycles
needed for "response" unit to reach threshold has been regressed
onto reaction times.
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 51
Farah: Neuropsychological inference
cue and top-down activation that the attention units
give the perception unit at its corresponding location.
When the perception unit is activated by the cue, it
activates the attention units on that side, which feed
activation back to the perception unit, establishing a
resonance that strengthens the activation of the target
representation. Attentional inhibition due to invalid
cuing is the result of the activated attention unit at the
cued location suppressing the activation of the attention
unit at the target location, leading to diminished topdown
activation ofthe target perception unit. That is, the
attention units on the cued side inhibit the attention units
on the opposite side. As a result, when the target is
presented to the opposite side, the attention unit on that
side must first overcome the inhibition of the attention
unit on the cued side before it can establish a resonance
with its perception unit, and response time is therefore
prolonged.
This very simple model of attention, which has no
disengage component, captures the qualitative relations
among the speeds of response in the three different
conditions and can be fitted quantitatively to these average
speeds with fairly good precision. In this regard, it
seems preferable to a model that postulates separate
components for orienting, engaging, and disengaging
attention. The disengage component, however, was postulated
on the basis ofthe behavior ofparietally damaged
subjects, not normal subjects. The critical test of this
model, therefore, is whether it produces a disengage
deficit when damaged.
A subset of the attention units on one side was eliminated
and the model was run in the valid and invalid cuing
conditions. (No patient data were available for the neutral
condition.) Figure 9 shows the data ofPosner et al. (1984)
from parietally damaged patients and the simulation results,
fitted to the data in the same way as before. Both
sets ofresults show a disengage deficit: a disproportionate
slowing from invalid cuing when the target is on the
damaged side.
Why does the model show a disengage deficit when its
attention units are damaged? The answer lies in the
competitive nature of attentional allocation in the model
and the imbalance introduced into the competition by
unilateral damage. Attentional allocation is competitive,
in that once the attention units on one side have been
activated, they inhibit attentional activation on the other
side. When there are fewer attention units available on
the newly stimulated side, the competition is no longer
balanced and much more bottom-up activation will be
needed on the damaged side before the remaining attention
units can overcome the inhibition from the attention
units on the intact side to establish a resonance with the
perception unit.
One might wonder whether we have really succeeded
in simulating the disengage deficit without a disengage
component, or whether some part of the model with a
different label, such as the attention units or the inhibitory
connections between attention units, is actually the
disengage component. To answer this question, consider
some of the attributes that would define a disengage
component. First, it should be brought into play by
perception ofthe target, and not the cue, on a given trial.
Second, it should be used to disengage attention and not
for any other function. By these criteria, there is no part of
Empirical Data
850
450
Valid Invalid
O Damaged
• Undamaged
Damage to Attention Units
850
rimeiseRespor
750'
650-
550-
450
Valid Invalid
Figure 9. Performance of parietally damaged patients and
damaged network in lateralized cued reaction time task. Number
ofcycles needed for "response" unit to reach threshold has
been regressed onto reaction times.
the model that is a disengager. The attention units as well
as their inhibitory connections are brought into play by
both cue and target presentations. In addition, the attention
units are used as much for engaging attention as for
disengaging it. We therefore conclude that the disengage
deficit is an emergent property of unbalanced competitive
interactions among remaining parts ofthe system that
do not contain a distinct component for disengaging
attention.
Humphreys and Riddoch (1993) have independently
proposed an account ofthe disengage deficit that does not
include a disengage component in the normal architecture.
Instead, they suggest that the deficit could be
secondary to an impairment in orienting attention or to an
overly strong engagement of attention ipsilesionally.
2.2.4. Relevance of the locality assumption for architecture
of visual attention. After damage to the attention
units on one side ofthe model, the nondamaged attention
units on the other side function differently. Specifically,
once activated they show a greater tendency to maintain
their activation. This is because of the reduced ability of
the attention units on the damaged side to recapture
activation from the intact side, even when they are receiving
bottom-up stimulus activation. The ability of this
52 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
model to account for the disengage deficit depends critically
upon this nonlocal aspect of its response to damage.
2.3. The functional architecture of visual face
recognition: Separate components for visual
processing and awareness?
Prosopagnosia is an impairment of face recognition that
can occur relatively independently of impairments in
object recognition and is not caused by impairments in
lower-level vision or memory. Prosopagnosic patients are
impaired in tests of face recognition such as naming faces
or classifying them according to semantic information
(such as occupation); they are also impaired in everyday
life situations that call for face recognition. Furthermore,
based on their own introspective reports, prosopagnosics
do not feel as though they recognize faces; however, when
tested using certain indirect techniques, some of these
patients do show evidence of face recognition. This has
been taken to imply that their impairment lies not in face
recognition per se, but in the transfer of the products of
their face-recognition system to another system required
for conscious awareness. This in turn implies that different
components of the functional architecture of the mind
are needed to produce perception and awareness of
perception.
2.3.1. Evidence for dissociated recognition and awareness
of recognition. Three representative types of evidence
will be summarized here. The most widely documented
form of "covert" face recognition occurs when
prosopagnosics are taught to associate names with photographs
of faces. For faces and names that were familiar to
the subjects prior to their prosopagnosia, correct pairings
are learned faster than incorrect ones (e.g., de Haan et al.
1987b). An example of this type of finding is shown in
Table 4. It seems to imply that, at some level, the subject
must have preserved knowledge of the faces' identities.
The other two types of evidence come from reaction time
tasks. One measures speed of visual analysis of faces, in
which subjects must respond as quickly as possible to
whether two photographs depict the same face or different
faces. Normal subjects perform this task faster with
familiar than unfamiliar faces. Surprisingly, as shown in
Table 5, a prosopagnosic subject showed the same pattern,
again implying that he was able to recognize them
(de Haan et al. 1987b). The last task to be reviewed is a
kind of semantic priming task. Subjects must classify
printed names as actors or politicians as quickly as possible,
while on some trials photographs of faces are presented
in the background. Even though the faces are
Table 4. Performance on correct and incorrect face-name
pairings in a face-name relearning task
Farah: Neuropsychological inference
Table 5. Speed of visual matching for familiar
and unfamiliarfaces (in msec)
Familiar Unfamiliar
Prosopagnosic subject 2,795
Normal subjects 1,228
3,297
1,253
irrelevant to the task subjects must perform, they influence
reaction times to the names. Specifically, normal
subjects are slowed in classifying the names when the
faces come from the other occupation category. As shown
in Table 6, the prosopagnosic patient who was tested in
this task showed the same pattern of results, implying that
he was unconsciously recognizing the faces fully enough
to derive occupation information from them (de Haan et
al. 1987a; 1987b).
2.3.2. Interpretation of covert recognition relative to the
functional architecture of visual recognition and conscious
awareness. The dissociation between performance
on explicit tests of face recognition and patients'
self-reporting of their conscious experience of looking at
faces, on the one hand, and performance on implicit tests
of face recognition on the other, has suggested to many
authors that face recognition and the ability to make
conscious use of it depend on different components of the
functional architecture. For example, de Haan et al.
(1992) interpret covert recognition in terms of the components
shown in Figure 10, in which separate components
of the functional architecture subserve face recognition
and conscious awareness thereof. According to their
model, the face-specific visual and mnemonic processing
of a face (carried out within the "face processing module")
proceeds normally in covert recognition, but the results of
this process cannot access the "conscious awareness system"
because of a lesion at location number 1.
2.3.3. Accounting for dissociated covert and overt recognition
with an interactive architecture. Randy O'Reilly,
Shaun Vecera, and I (Farah et al. 1993) have modeled
overt and covert recognition using the five-layer recurrent
network shown in Figure 11, in which the same set of
so-called face units subserves both overt and covert recognition.
The face input units subserve the initial visual
representation of faces, the "semantic" units represent
the semantic knowledge of people that can be evoked
either by the person's face or by the name, and the "name"
units represent names. Hidden units were used to help
the network learn the associations among patterns of
activity in each of these three layers. These are located
between the "face" and "semantic" units (called the "face"
Trial:
Correct pairings
Incorrect pairings
Trial:
Correct pairings
Incorrect pairings
1
2
0
9
2
1
2
1
0
10
3
1
CO—IO
11
2
0
4
2
1
12
2
0
5
1
1
6
2
0
7
0
0
8
3
0
Table 6. Priming
Prosopagnosic
subject
Normal subjects
of occupation judgments (in
Baseline
1,565
821
Unrelated
1,714
875
msec)
Related
1,560
815
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 53
Farah: Neuropsychological inference
Perceptual input
Face processing module
Structural encoding^
Expression
analysis
JL
Other face
relevant
processes
Stored V i /
representations
(FRU's)
Response
effector
systems
Conscious awareness system
Executive system
Figure 10. Functional architecture of perception and awareness,
proposed by de Haan et al. (1992).
hidden units) and between the "name" and "semantic"
units (the "name" hidden units). Thus, there are two pools
of units that together comprise the visual face-recognition
system in our model in that they represent visual information
about faces: the "face input" units and the "face
hidden" units.
The connectivity among the different pools of units was
based on the assumption that in order to name a face, or to
visualize a named person, one must access semantic
knowledge of that person. Thus, face and name units are
not directly connected but send activation to one another
through hidden and semantic units. All connections
shown in Figure 11 are bidirectional.
Faces and names are represented by random patterns
of 5 active units out of the total of 16 in each pool.
Semantic knowledge is represented by 6 active units out
of the total of 18 in the semantic pool. The only units for
which we have assigned an interpretation are the "occupation
units" in the semantic pool: one represents the
semantic feature "actor," and the other, "politician." The
network was trained to associate an individual's face,
semantics, and name whenever one of these was presented,
using the Contrastive Hebbian Learning algorithm
(Movellan 1990). After training, the network was
damaged by removing units.
Figure 12 shows the performance of the model in a 10-
Semantic
Name Hidden Face Hidden
Name Input Face Input
Figure 11. Functional architecture of face perception as modeled
by Farah et al. (1993).
Overt Performance: Hidden Unit Lesions
(Forced Choice with 10 Alternatives)
100 7
-115 0.0 115 25.0 373 50.0 615 75.0 87.5 100.0
Lesion Size
Overt Performance: Face Pool Lesions
(Forced Choice with 10 Alternatives)
100 •
•115 0.0 115 25.0 373 50.0 615 75.0 873 100.0
Percent Lesion
Figure 12. Effect of different amounts ofdamage to face units
on the network's ability to perform 10-alternative forced choice
naming of faces, an overt face recognition task.
alternative, forced-choice naming task for face patterns
after different degrees of damage to the "face input" and
"face hidden" units. At levels of damage corresponding to
removal of 62.5% and 75% of the face units in a given
layer, the model performs at or near chance on this overtrecognition
task. This is consistent with the performance
of prosopagnosic patients who manifest covert recognition.
Such patients perform poorly, but not invariably at
chance, on overt tests of face recognition.
In contrast, the damaged network showed faster learning
of correct face-name associations. When retrained
after damage, it consistently showed more learning for
correct pairings than incorrect ones in the first 10 training
epochs, as shown in Figure 13. The damaged network also
completed visual analysis of familiar faces faster than
unfamiliar ones. When presented with face patterns after
damage, the face units completed their analysis of the
input (i.e., the face units settled) faster for familiar than
unfamiliar faces, as shown in Figure 14. And finally, the
damaged network showed semantic interference from
faces in a name classification task. Figure 15 shows that
when the network was presented with name patterns and
54 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
50% Face Input Unit Lesion
100
t
t
<3
c
t
90-
80"
70-
60-
50-
40-
30-
20-
10-
o•*—
Correct Pairings
—•*— Incorrect Pairings
i—'
-2 -1 0 1 2 3 4 5 6 7 8 9 10 11 12
Epoch Number
t
3
*— Correct Pairings
--•*•- Incorrect Pairings
Farah: Neuropsychological inference
50% Face Hidden Unit Lesion
100-
90-
80-
70"
60-
50"
40-
30-
20-
10-
0
-2 -1 0 1 2 3 4 5 6 7 8 9 10 11 12
Epoch Number
Z
E
3
62.5% Face Input Unit Lesion
100 "I
62.5% Face Hidden Unit Lesion
90
80
70-
60
50
40
30
20
10
0
•*— Correct Pairings
--•*•- Incorrect Pairings
-2 -1 0 1 2 3 4 5 6 7 8 9 10 11 12
Epoch Number
100
90
80
70
60
50
40
30
20"
10
0
•*— Correct Pairings
—•*"" Incorrect Pairings
1 2 3 4 5 6 7 8 9 10 11 12
Epoch Number
i
<3
75% Face Input Unit Lesion
100T
75% Face Hidden Unit Lesion
~~^— Correct Pairings
""•*"" Incorrect Pairings
-2 -1 0 1 2 3 4 5 6 7 8 9 10 11 12
Epoch Number
I
100
90
80
70
60
50
40
30
20
10
0
•
•
— * — Correct Pairings
--•*— Incorrect Pairings
-2 -1 0 1 2 3 4 5 6 7 8 9 10 11 12
Epoch Number
Figure 13. Ability of the network after different amounts of damage to face units to produce the name associated to a face (to within 2
bits), for correctly and incorrectly paired names and faces, immediately after damage and following 10 epochs offurther training. Note
that learning occurs more quickly for correctly paired names and faces.
the time it took to classify them according to occupation
(i.e., the number of processing cycles for the occupation
units to reach threshold) was measured, classification
time was slowed when a face from the incorrect category
was shown, relative to faces from the correct category
and, in some cases, to a no-face baseline.
Why does the network retain "covert recognition" of
the faces at levels of damage that lead to poor or even
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 55
Farah: Neuropsychological inference
Same-Different Matching Task
Hidden Unit Lesions
600
i
£
8
I
|I
1
550-
500-
450-
400-
350-
300-
250-
200-
150-
100-
50"
- * — Familiar Faces
-•*•- Novel Faces
0.0 125 25.0 375 50.0 625 75.0 875 100.0
Percent Lesion
Same-Different Matching Task
Face Pool Lesions
600
s
V)
S
S
O
E
D
z
550-
500-
450-
400-
350-
300-
250-
200-
150-
100-
50-
o-
* — Familiar Faces
•"*— Novel Faces
t—*-.
0.0 12.5 25.0 375 50.0 62.5 75.0 875 100.0
Percent Lesion
Figure 14. Effect of different amounts of damage to face units
on the time needed for the face units to settle, for familiar input
patterns (closed triangles) and for unfamiliar input patterns
(open triangles). Note that familiar patterns tend to settle more
quickly.
Semantic Priming Task
Hidden Unit Lesions
Same Occupation
—*"- Different Occupation
'" Name Only
125 25.0 375 50.0 62.5 75.0 875 100.0
Percent Lesion
Semantic Priming Task
Face Pool Lesions
"*— Same Occupation
—"*"" Different Occupation
• - * - Name Only
0.0 125 25.0 375 50.0 625 75.0 875 100.0
Percent Lesion
Figure 15. Effect of different amounts of damage to face units
on the number of cycles needed for the "actor" and "politician"
units to reach threshold when presented with name and face
input patterns. When the face is from a different occupation
category, it takes longer for the name to push the correct
occupation unit over threshold.
chance levels of overt recognition? The general answer
lies in the nature of knowledge representation in PDP
networks. As already mentioned, knowledge is stored in
the pattern of weights connecting units. The set of the
weights in a network that cannot correctly associate patterns
because it has never been trained (or has been
trained on a different set of patterns) is different in an
important way from the set of weights in a network that
cannot co'rrectly associate patterns because it has been
trained on those patterns and then damaged. The first set
of weights is random with respect to the associations
in question, whereas the second is a subset of the necessary
weights. Even if it is an inadequate subset for
performing the overt association, it is not random: it has
"embedded" in it some degree of knowledge of the associations.
Furthermore, consideration of the tasks used
to measure covert recognition suggest that the covert
measures should be sensitive to this embedded knowl-
edge.
A damaged network would be expected to relearn
associations that it originally knew faster than novel associations
because of the nonrandom starting weights. The
faster settling with previously learned inputs can be
attributed to the fact that the residual weights come from
a set designed to create a stable pattern from that input.
Finally, to the extent that the weights continue to activate
partial and subthreshold patterns over the nondamaged
units in association with the input, these resultant patterns
will contribute activation toward the appropriate
units downstream, which are simultaneously being activated
by intact name units.
56 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Farah: Neuropsychological inference
2.3.4. Relevance of the locality assumption for architecture
of perception and awareness. The role of the locality
assumption is less direct in the foregoing example than in
the previous two, but it is nevertheless relevant. Many
authors have reasoned according to the locality assumption
that the selective loss of overt recognition and the
preservation of covert recognition implies that there has
been localized damage to a distinct component of the
functional architecture needed for overt, but not covert,
recognition. The alternative account, proposed here, suggests
that partial damage to the visual face-recognition
component changes the relative ability of the remaining
parts of the system (i.e., the remaining parts of the facerecognition
component along with the other components)
to perform the overt and covert tasks. Specifically, the
discrepancy between the difficulty of the overt and covert
tasks is increased, as can be seen by comparing the steep
drop in overt performance as a function of damage shown
in Figure 12 with the relatively gentle fall-off in the
magnitude of the covert recognition effects shown in
Figures 13-15. According to the model, this is because
the information processing required by the covert tasks
can make use of partial knowledge encoded in the weights
of the damaged network and is therefore more robust to
damage than the information processing required by the
overt task. In other words, with respect to the relative
ability of the remaining system to perform overt and
covert tasks, the effects of damage were nonlocal. The
ability of the model to account for the dissociation between
overt and covert recognition depends critically on
this violation of the locality assumption.
components: although the overviews of the models presented
in Figures 6 and 7 are not strictly comparable (Fig.
6 includes components postulated to account for other
attentional phenomena and Fig. 7 includes separate depictions
of the left and right hemispheres' attentional
mechanisms as well as two different levels of stimulus
representation), it can be seen that the same "attention"
component shown in Figure 7 does the work of both the
"engage" and "disengage" components in Figure 6. Similarly,
setting aside the irrelevant differences in the complexity
of Figures 10 and 11 arising from factors such as
the greater range of phenomena to be explained by
Figure 10, it is clear that the same visual "face" components
in Figure 11 do the work of the visual "face"
components and "conscious awareness system" in Figure
10, at least as far as explaining performance in overt and
covert tasks is concerned.
It should be noted that the success of these models is a
direct result of denying the locality assumption, as explained
in subsections on the relevance of the locality
assumption (sects. 2.1.4, 2.2.4, 2.3.4). In linking each
neuropsychological dissociation to the more parsimonious
functional architecture, a key explanatory role is
played by the nonlocal effects that damage to one component
of the architecture has on the functioning of other
components. Hence the weight of evidence from the
three cases discussed here suggests that the locality
assumption is false. Finally, with respect to its necessity,
the examples provide existence proofs that principled
inferences can be made in cognitive neuropsychology
without the locality assumption.
3. General discussion
3.1. Evaluating the truth and methodological necessity
of the locality assumption
The foregoing examples were intended as a small "data
base" with which to test two empirical claims about
the locality assumption. First, that it is true, namely,
that after local brain damage the remaining parts of the
system continue to function as before. Second, that it is
necessary, in other words, that there is no other way to
make principled inferences from the behavior of braindamaged
subjects to the functional architecture of the
mind, and that the only alternative is therefore to abandon
cognitive neuropsychology.
The examples allow us to assess the likely truth of the
locality assumption by assessing the likely truth of the
different inferences made with and without it. Of course,
each such pair of inferences was made on the basis of the
same data and fits those data equally well, so the choice
between them rests on considerations of parsimony and
consistency with other information about brain organization.
On the basis of these considerations, the inferences
made without the locality assumption seem preferable. In
the case of semantic memory, the model obtained without
the locality assumption is consistent with an abundance of
other data implicating modality-specificity as a fundamental
principle of brain organization and with the lack of any
other example of a purely semantic distinction determining
brain organization. In the case of visual attention, the
model obtained without the locality assumption has fewer
3.2. Possible objections
In this section I consider some possible objections to
these conclusions, with the hope of clarifying what has
and has not been demonstrated here.
3.2.1. PDP and box-and-arrow: Apples and oranges? One
kind of objection concerns the comparability of the hypotheses
that were derived with and without the locality
assumption. The two types of hypotheses do indeed differ
in some fundamental ways, and comparing them may be a
bit like comparing apples and oranges. Nevertheless,
apples and oranges do share some dimensions that afford
meaningful comparisons, and I argue that the hypotheses
under consideration here are likewise comparable in the
ways discussed above.
For example, it might be objected that the computer
models denying the locality assumption can only demonstrate
the sufficiency of a theory, not its empirical truth,
whereas the alternative hypotheses are empirically
grounded. It is true that the models presented here have
only been shown to be sufficient to account for the
available data, but this is also true of the alternative
hypotheses, and indeed of any hypothesis. It is always
possible that a hypothesis can fit all the data collected so
far, but that some other, as yet undiscovered, data could
falsify it. The reason this may seem more problematic for
PDP models is that there is a research tradition in
computer modeling that takes as its primary goal the
accomplishment of a task rather than the fitting of psychological
data (e.g., Rosenberg & Sejnowski 1986), relying
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Farah: Neuropsychological inference
exclusively on computational constraints rather than empirical
constraints to inform the models. This is not a
necessary feature of modeling, however, and the models
presented here are constrained as much as the alternative
hypotheses are by the empirical data.
Furthermore, the computational models presented
here and the alternative hypotheses are on equal footing
with respect to the distinction between prediction and
retrodiction of data. In all three cases, the locality assumption
has been used to derive a hypothesis, post hoc,
from the observed neuropsychological dissociation. It was
not the case that researchers had already formulated
hypotheses to the effect that semantic memory was subdivided
by taxonomic category or that there was a distinct
component ofthe attention system for disengaging attention,
or that awareness of face recognition depended on
distinct parts of the mental architecture from face recognition;
nor did they then go looking for the relevant
dissociations to test those hypotheses. Rather, they began
with the data and inferred their hypotheses just as we
have done with the models presented earlier. Both the
hypotheses derived using the locality assumption and the
PDP models presented here await further testing with
new data. An example ofthe way in which new data can be
used to distinguish between the competing hypotheses
comes from the work of Verfaellie e't al. (1990) with a
bilateral parietally damaged patient. They found that,
contrary to their expectation of a bilateral disengage
deficit, their subject showed diminished effects of attentional
cuing. When attention units are removed bilaterally
from the Cohen et al. (in press) model, which was
developed before the authors knew of the Verfaellie et al.
finding, the model also shows reduced attentional effects
rather than a bilateral disengage deficit. This is because
the disengage deficit in our model is caused by the
imbalance in the number of attention units available to
compete with one another after unilateral damage; bilateral
damage does not lead to an imbalance but it does, of
course, reduce the overall number of attention units and
therefore the magnitude of the attentional effects.
Another way the comparisons presented above might
seem mismatched is in their levels of description. The
hypotheses derived using the locality assumption concern
"macrostructure,' that is, the level of description that
identifies the components of the functional architecture,
as shown in the so-called box-and-arrow models. In contrast,
the hypotheses that deny the locality assumption
appear to concern "microstructure," that is, the nature of
the information processing that goes on within the architectural
components. However, the latter hypotheses
concern both microstructure and macrostructure, as
should be clear from the macrostructures depicted in
Figures 2, 7, and 11. We can therefore compare the two
types of hypotheses at the level of macrostructure.
3.2.2. The locality assumption can be saved with more
fine-grained empirical analysis of the deficit. Perhaps the
prospects for the locality assumption look so dim because
the types ofdata considered so far are unduly limited. The
arguments and demonstrations presented above concern
a relatively simple type of neuropsychological observation,
namely, a selective deficit in some previously normal
ability. I have focused on this type of observation for two
reasons; the first is its very simplicity, and the seemingly
straightforward nature of the inferences that follow from
it. At first glance, a truly selective deficit in A does seem
to demand the existence of an A component, and this
inference is indeed sound under the assumption that the
A component is informationally encapsulated. The second
reason is that this is still the most common form of
inference in cognitive neuropsychology, as argued earlier
in the section on ubiquity (sect. 1.2).
Nevertheless, other, finer-grained ways of analyzing
patient performance are used increasingly by cognitive
neuropsychologists to pinpoint the underlying locus of
impairment in a patient's functional architecture. The two
most common are qualitative error analyses, and selective
experimental manipulations ofdifficulty of particular
processing stages. Can the use of the locality assumption
be buttressed by the additional constraints offered by
these methods? Several recent PDP simulations of patient
performance suggest that these finer-grained analyses
are just as vulnerable to nonlocal effects of brain
damage as are the more brute-force observations of deficit
per se.
For example, semantic errors in single-word reading
(e.g., pear—* "apple") have been considered diagnostic of
an underlying impairment in the semantic representations
used in reading, and visual errors (pear —» "peer")
are generally taken to imply a visual processing impairment
(e.g., Coltheart 1985). Hinton and Shallice (1991)
showed how a PDP simulation of reading could produce
both kinds of errors when lesioned either in the visual or
the semantic components of the model. Humphrey et al.
(1992) make a similar point in the domain ofvisual search:
error patterns suggestive ofan impairment in gestalt-like
grouping processes can arise either from direct damage
to the parts of the system that accomplish grouping or
by adding noise to earlier parts of the system. In both
cases, the nondiagnosticity of error types results from
the interactivity among the different components of the
model.
Another well-known example of the use of error types
to infer the locus of impairment is the occurrence of
regularization errors in the reading performance of surface
dyslexics (e.g., Coltheart 1985). As mentioned earlier,
surface dyslexics fail to read irregular words; this has
been interpreted, using the locality assumption, as the
loss of a whole-word reading route with preservation of
the sublexical grapheme-phoneme translation route. The
inference that these patients are relying on the latter
route seems buttressed by a further analysis of the nature
of their errors, which are typically regularizations (e.g.,
pint is pronounced like "lint"). Patterson et al. (1989),
however, showed that a single-route architecture, comprised
only of whole-word spelling-sound correspondences,
produced, when partially damaged, both a selective
impairment in the reading of irregular words and a
tendency to regularize them. With the distributed representations
used in their model, similar orthographies and
phonologies have similar representations at each of these
levels and there is consequently a tendency toward generalization.
Although with training the system learns not to
generalize the pronunciation of, say, pint to the pronunciation
of most other -int words (such as lint, mint, hint),
this tendency is unmasked at moderate levels ofdamage.
The model's regularization errors are probably best understood
as a result of the distributed nature of the word
58 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Farah: Neuropsychological inference
representations in their model. The principles of PDP are
closely interrelated, however, and the regularization effects
can also be viewed as the result of interactions
among different word representations, with the less common
pronunciations losing their "critical mass" and therefore
being swamped by the remaining representations of
more common pronunciations.
Analyses of selective deficits and of the nature of the
errors produced have in common the use of a purely
observational method. Perhaps experimental manipulations
designed to tax the operation of specific components
offer a more powerful way of pinpointing the locus of
impairment. Two recent models speak to this possibility
and show that direct manipulations of particular processing
stages are no more immune to nonlocal effects than
are the previous methods. Mozer and Behrmann's (1990)
model of visual-spatial neglect shows how the manipulation
of a stimulus property designed to affect postvisual
processing, namely the lexicality of a letter string (word,
pseudoword, nonword), can have pronounced effects on
the performance of a model whose locus of damage is
visual. Interactions between attended visual information
and stored lexical representations allow letter strings to
be reconstructed more efficiently the more they resemble
familiar words. Tippett and Farah (in press) showed how
apparently conflicting results in the literature on the
determinants of naming difficulty in Alzheimer's disease
can be accounted for with a single hypothesis. Although
most researchers believe that the naming impairment in
Alzheimer's disease results from an underlying impairment
of semantic knowledge, manipulations of visual
difficulty (degraded visual stimuli) and lexical access difficulty
(word frequency) have pronounced effects on patients'
likelihood of naming, leading to alternative hypotheses
of visual agnosia or anomia (Nebes 1989). When
semantic representations were damaged, a PDP model of
visual naming showed heightened sensitivity to visual
degradation and word frequency. Thus, when one component
of an interactive system is damaged, the system as a
whole becomes more sensitive to manipulations of the
difficulty of any of its components.
In sum, the problem of nonlocal effects of brain damage
is not limited to inferences based on the range and
boundaries of the impairment; it also affects inferences
based on the qualitative mode of failure and the sensitivity
of the system to manipulations designed to affect
specific components directly.
3.2.3. PDP could be false. A different type of objection
concerns the assumptions of the PDP framework. As
already acknowledged, PDP is controversial. How can
one be convinced, through comparisons involving PDP
models, that the locality assumption is false, if it has not
been established first that PDP is a correct way of characterizing
human information processing? First, it should
be pointed out that much of the controversy concerning
PDP involves the adequacy of PDP models of language
and reasoning, which are not relevant here. Few vision
researchers would deny that the basic principles of PDP
are likely to apply to visual attention and pattern recognition
(e.g., see the recent textbook overviews of these
topics by Allport 1989; Biederman 1990; Hildreth &
Ullman 1989; Humphreys & Bruce 1989; and even Pinker
1985, who has been critical of PDP models of language).
Semantic memory may be a more controversial case.
Second, and perhaps more important, one can remain
agnostic about PDP as a general framework for human
information processing and still appreciate that the particular
models presented here are credible alternatives to
those derived using the locality assumption. PDP, like
the locality assumption, is ultimately an empirical claim
that will gain or lose support according to how well it helps
explain psychological data. The ability of PDP to provide
parsimonious accounts for neuropsychological dissociations
such as the ones described here counts in its favor.
Finally, even if PDP were false, there would remain other
ways of conceptualizing human information processing
that would provide explicit, mechanistic alternatives to
modularity. For example, in production system architectures
(see Klahr et al. 1987) working memory is highly
nonencapsulated. Kimberg and Farah (in press) found
that weakening association strengths in working memory
produced an array of specific and characteristic frontal
impairments that were in no transparent way related to
working memory. Although interactive computation is at
the heart of PDP, which makes PDP the natural architecture
to contrast with the locality assumption, other architectures
are also capable of accommodating high degrees
of interactivity.
3.3. General implications of denying the locality
assumption
3.3.1. Modularity. The truth of the locality assumption has
implications for issues in psychology beyond how best to
infer functional architecture from the behavior of braindamaged
patients. As discussed at the outset, the locality
assumption follows from a view of the mind and brain
according to which the components of the functional
architecture are informationally encapsulated, that is,
their inputs and outputs are highly constrained. Components
interact only when one has completed its processing,
at which point it makes the end product available to a
relatively small number of other components. If this were
true, then the effects of damaging one component should
be relatively local. Alternatively, if we judge that the best
interpretation of various neuropsychological deficits (on
the grounds of parsimony or consistency with other scientific
knowledge, not on the grounds ofa priori preferences
for encapsulation or interactivity) involves denying the
locality assumption, then this counts as evidence against
modularity.
The term "modularity" is often used in a more general
sense than I have used it so far, and this more general
sense is not challenged by the failure of the locality
assumption. Specialized representations are sometimes
called "modules," so that the model in Figure 2 could be
said to contain "visual knowledge" and "functional knowledge"
modules. In this more general sense, the "modularity
hypothesis" is simply that there is considerable
division of labor among different parts of functional architecture
with, for example, knowledge of language represented
by a separate part of the system (functionally, and
possibly anatomically), compared with other knowledge.
Of course, if such a system is highly interactive, it may be
difficult to delineate and characterize the different modules,
but this is a problem of how you find something out,
not of what it is or whether it exists.
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Farah: Neuropsychological inference
3.3.2. Top-down versus bottom-up research strategies.
Denying the locality assumption also has a more general
implication for research strategy in cognitive neuroscience.
Most researchers in neuroscience and cognitive
science acknowledge that there are multiple levels of
description of the nervous system, from molecules to
thoughts, and that one ofthe goals ofscience is a complete
description of the nervous system at all of these levels.
However, such researchers may differ in their opinions as
to the most efficient way to arrive at this complete description.
The bottom-up, or reductionist, approach is to
begin with the most elementary levels of description,
such as the biophysics ofneurons, believing that it will be
impossible to understand higher levels of organization if
one does not know precisely what is being organized. This
approach is anathema to cognitive neuroscience, which
is, by definition, forging ahead with the effort to understand
such higher-level properties ofthe brain as perception,
memory, and so forth, while acknowledging that our
understanding of the more elementary level of description
is far from complete.
The main alternative, explicitly endorsed by many
cognitive neuroscientists, is the top-down approach, according
to which the most efficient way to understand the
nervous system is by successive stages of analysis of
systems at higher levels of description in terms of lower
levels of description. It is argued that our understanding
of lower levels will be facilitated ifwe know what higherlevel
function they serve. It is also argued that the
complexity of the task of understanding the brain will be
reduced by the "divide and conquer" aspect of this strategy,
in which the system is analyzed into simpler components
that can then be further analyzed individually (e.g.,
Kosslyn et al.'s 1990 "hierarchical decomposition constraint").
In the context of the three examples discussed
earlier, this corresponds to first deriving the macrostructural
hypotheses, in which the relevant components of
the functional architecture are identified, and then investigating
the microstructure of each component's internal
operation. Unfortunately, to derive a macrostructure
from neuropsychological data requires either making the
locality assumption or considering the system's microstructure,
as was done in the foregoing examples. If the
locality assumption is false, the microstructure has implications
for the macrostructure, and one cannot be
assured ofarriving at the correct macrostructural description
without also considering hypotheses about micro-
structure.
Thus, even if one's only goal is to arrive at the correct
macrostructural description of the functional architecture,
as is the case for most cognitive neuropsychologists,
the three examples presented here suggest that one must
nevertheless consider hypotheses about microstructure.
This points out a correspondence between theories of
functional architecture and the methodologies for studying
it. If one holds that the components of the functional
architecture are informationally encapsulated, one can
take a strictly top-down approach to the different levels of
description, "encapsulating" one's investigations of the
macrostructure from considerations ofmicrostructure. In
contrast, if one views the functional architecture as a
highly interactive system, with each component responding
directly or indirectly to the influences ofmany others,
then one must adopt a more interactive mode ofresearch,
in which hypotheses about macrostructure are influenced
by constraints imposed simultaneously at both the macrostructural
and the microstructural levels.
3.3.3. Implications for cognitive neuropsychology. The
conclusion that the locality assumption may be false is a
disheartening one. It undercuts much of the special
appeal of neuropsychological dissociations as evidence
about the functional architecture. Although perhaps naive
in hindsight, this special appeal came from the apparent
directness of neuropsychological data. Conventional
methods of cognitive psychology are limited to what
Anderson (1978) has called "input-output" data: manipulation
of stimuli and instructions on the input end and the
measurement of responses and response latencies at output.
From the relations between these, the nature of the
intervening processing must be inferred. Such inferences
are indirect, and as a result often underdetermine choices
between competing hypotheses. In contrast, brain damage
directly affects the intervening processing, constituting
a direct manipulation of the "black box."
Unfortunately, the examples presented here suggest
that even if the manipulation of the intervening processing
is direct, the inferences by which the effects of the
manipulations must be interpreted are not. In Ferrier's
(1886) words, it may well be "at least highly difficult to
trace any uncomplicated connection between the symptoms
produced and the lesion as such." The locality
assumption, which constitutes the most straightforward
way of interpreting neuropsychological impairments,
does not necessarily lead to the correct interpretation. If
the locality assumption is indeed false, then dissociations
lose their special status as particularly direct forms of
evidence about the functional architecture.
Even for cognitive neuropsychologists who would not
claim any special status for neuropsychological data,
abandoning the locality assumption would make their
work harder. The interpretation of dissociations without
the locality assumption requires exploring a range of
possible models that, when damaged, might be capable of
producing that dissociation. What makes this difficult is
that the relevant models would not necessarily have
components corresponding to the distinctions between
preserved and impaired abilities and we therefore lack
clear heuristics for selecting models to test.
The foregoing demonstrations and arguments are not
intended to settle decisively the issue of whether the
locality assumption is correct. As already acknowledged,
this is not the type ofissue that can be decided on the basis
of a single study or even a small number of studies.
Instead, my goal has been to call attention to the fact that
we do not have any firm basis for an opinion one way or the
other, despite the widespread use of the locality assumption.
Furthermore, at least in a few cases the best current
interpretation seems to involve denying the locality
assumption.
It is possible that some cognitive domains will conform
more closely to the locality assumption than others; if so,
this would have interesting theoretical as well as methodological
implications concerning the degree of informational
encapsulation in different subsystems of the functional
architecture. However, until we have a broad
enough empirical basis for deciding when the locality
assumption can safely be used and when it will lead to
60 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Commentaryi'Farah: Neuropsychological inference
incorrect inferences, we cannot simply assume it to be
true, as has been done almost universally in the past.
ACKNOWLEDGMENTS
The writing of this paper was supported by ONR grant
N00014-91-J1546, NIMH grant R01 MH48274, NIH career
development award K04-NS01405, and a grant from the
McDonnell-Pew Program in Cognitive Neuroscience. I thank
my coauthors on the projects described herein for their collaboration
and tutelage in PDP modeling: Jonathan Cohen, Jay
McClelland, Randy O'Reilly, Rick Romero, and Shaun Vecera.
Special thanks to Jay McClelland for his encouragement and
support. I thank several colleagues for discussions of the ideas in
this paper: John Bruer, Alfonso Caramazza, Clark Glymour,
Mike McCloskey, Morris Moscovitch, Edmund Rolls, and Larry
Squire. I also thank Larry Weiskrantz for calling my attention to
the passage from Ferrier quoted at the beginning. Finally, I
thank the reviewers and editor of BBS for useful comments and
criticisms of a previous draft: C. Allen, S. Hamad, G. Humphreys,
M. McCloskey, M. Oaksford, T. Van Gelder, and four
anonymous reviewers.
NOTES
1. There are, of course, many other ways to make a wrong
inference using the locality assumption, even with the foregoing
conditions satisfied, but these have to do with the particular
content of the hypothesis being inferred and its relation to the
data, not the use of the locality assumption per se. For example,
Caramazza et al. (1990) have pointed out that selective impairments
in modality-specific knowledge do not imply that knowledge
of different modalities is represented in different formats;
dissociability will not, in general, tell us about representational
formats.
Open Peer Commentary
Commentary submitted by the qualified professional readership of this
journal will be considered for publication in a later issue as Continuing
Commentary on this article. Integrative overviews and syntheses are
especially encouraged.
Simulating nonlocal systems: Rules of the
game
John A. Bullinaria
Department of Psychology, University of Edinburgh, Edinburgh EH8 9JZ,
Scotland
Electronic mail: johnbulKsied.ac.uk
Farah notes that the locality assumption, as usually stated, may
appear "naive. Indeed, Shallice(1988, Ch. 11; see also multiple
review, BBS 14[3] 1991) has described a whole range of systems
that can give rise to double dissociations (DDs), and Dunn and
Kirsner (1988) have presented a class of single process systems
that can result in DDs and have formulated the new concept of
reversed association to replace DDs as a valid indicator of
modularity. Consequently, one might argue that the locality
assumption is simply an artefact from the days of "box-andarrow"
models and that since the advent of connectionist (i.e.,
parallel distributed processing [PDP] or neural network) modelling
we can (and should) work in finer detail and use finergrained
evidence to constrain our theories.
As Farah notes, for a fair comparison of local and nonlocal (or,
box-and-arrow and connectionist) systems we must place appropriate
constraints on both approaches. To make general statements
about the need for the locality assumption and the
superiority of connectionism over boxes and arrows we should
also constrain the types of system we attempt to model. Thus, in
addition to the implicit constraint that our nonlocal systems are
neural networks, it seems reasonable to propose the following
"rules of the game":
1. Since single dissociations and weak DDs can be explained
as resource artefacts (Shallice 1988, Ch. 10), and no one will be
impressed if we use anything more complicated, we should
concentrate on modelling strong DDs.
2. If a neural network is simple enough to set the connection
weights (synaptic strengths) by hand then a PDP approach is
probably not required. The weights should be learnt.
3. If the system has inbuilt structure it is little more than an
explicit implementation of a box-and-arrow system. We should
try to allow any modularity to be learnt rather than imposed by
hand. However, if we then fail to find DDs we will not know
whether this is because DDs in real brains arise solely because
of innate structures that have not been built into our models or if
our learning algorithms are too dissimilar to those in real brains
for the same modular structures to arise.
4. If we are forced to have inbuilt structure then with neural
networks we no longer have to restrict ourselves to cases with
truly separate modules - we can (and should) try all kinds of
subtle connections between the modules, examining their
implications.
5. We must ensure that our neural networks are sufficiently
complex: we need enough training patterns to prevent them
from operating by table lookup and enough hidden layers and
connections for a modular structure to arise if that is
appropriate.
6. The input and output representations must be chosen
carefully — in small systems random fluctuations can be converted
into strong dissociations by an (un)suitable choice of
representation.
7. We often restrict our neural networks to the minimum
number of units and connections required to solve the problem
because this tends to speed up the training, improves generalisation,
and makes it easier to understand the hidden unit
representations. Minimal systems are not likely to behave in the
same way as nonminimal systems such as brains, however, and
should be avoided.
8. Some forms of neural network damage are more realistic
than others. The most obvious is the removal of subsets of units
and connections but we should also consider various changes to
the weights and activations: adding noise, global rescaling,
clipping, and so on.
9. Neurological patients often (but not always) show rapid
improvement in performance after a lesion occurs (Geschwind
1985) so we should also allow our systems to relearn after
damage. With minimal networks we can easily lesion them so
that they become subminimal and then allow them to relearn.
This can confuse the results since relearningcan create, destroy,
or even reverse the sense of dissociations. For nonminimal
networks we have the problem that releaming tends to compensate
totally for the damage and we get no dissociations at all.
10. One must be able to argue that the system and our
analyses of it can scale up to sizes comparable to those found in
the brain. Combinatorial explosions often make this difficult.
Many of these points are discussed in more detail in Bullinaria
and Chater (1993). These rules are difficult to follow and should
perhaps be aimed for in the future rather than expected of
current models. None of Farah s three models gets past rule 1
and it is unlikely that any existing model satisfies them all.
We end by suggesting the kind of model that might one day
satisfy these rules. We deal explicitly with reading (where
surface and phonological dyslexia constitute a strong DD) since
this was listed by Farah as a typical case where locality is
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Commentary/Farah: Neuropsychological inference
assumed. In fact, there have been arguments against locality
here (in particular the strong dual-route hypothesis) for some
time, even before PDP came along (e.g., Humphreys & Evett
1985). There now exist fully distributed, nonminiinal, singleroute
neural network models of reading that learn to achieve
100% performance on both regular and exception words of any
length in their training data and can read nonwords as well as
humans (Bullinaria 1993). With a specific form of global damage
(that easily scales up) they exhibit symptoms similar to surface
dyslexia but are unable to acquire phonological dyslexia, suggesting
that there must still be some kind of missing (lexical/semantic)
route. These models can already use context
information to deal successfully with homographs so, although it
remains to be seen how we can fully incorporate semantics into
these systems, any additional route is unlikely to be totally
independent and uncoupled. We are within the rules so far. If
we can add in the semantics and get the full DD without
breaking the rules we might really have a serious and general
challenge to the locality assumption.
Local representations without the locality
assumption
A. Mike Burton and Vicki Bruce
Department of Psychology, University of Stirling, Stirling FK9 4LA, United
Kingdom
Electronic mail: mb1@forth.stir.ac.uk; vb1@forth.stir.ac.uk
Farah s arguments against what she calls the "locality assumption"
appear to us to be well-founded, yet we would like to take
issue with two aspects of her target article. First, we will argue
that the rejection of this assumption should not lead one to take
on board all the assumptions of the parallel distributed processing
(PDP) approach. We focus in particular on the "distributed"
assumption. Second, we will argue that many cognitive neuropsychologists
share the same insight about the locality assumption.
As a result, much recent theoretical work avoids this
assumption but does not necessarily resort to a radical PDP
approach.
PDP as a "specific" alternative? Farah lists three assumptions
of the PDP approach: distributed representations, gradedness,
and interactivity (sect. 1.4). She reminds us that the psychological
plausibility of PDP is controversial, stating that "PDP is to be
evaluated as a specific alternative [to the locality] assumption"
(sect. 1.4, our italics). The three example models used to test the
PDP approach, however, seem radically different from one
another. It appears that PDP is not a specific alternative, but a
huge family of alternatives that may be mixed and matched as it
suits the builders of these models. It is never clear how much of
the particular PDP architecture of each model is intended to
carry explanatory power in accounting for the phenomenon
under study. We will focus on the issue of distributed representations
to illustrate this point.
In the model of semantic memory (an autoassociator trained
with the delta rule), the notion of a distributed representation is
used in a componential way, so a representation is highly visual if
it comprises a higher proportion of visual semantic units than
functional semantic ones. Under some (strict) definitions of
distributed representations, individual units have no referent.
In this case, however, each of the semantic units must in some
sense be individually referential, as their effect can be summed.
This componential approach is not new. If by the term distributed
Farah means that large things are made up of smaller
things, we are not prepared to dispute this. However, this is not
the exclusive insight of the PDP approach.
In the model of visual attention (a snapshot model with no
learning) there is no very clear definition ofwhether representations
are distributed or local, but the model of face perception
(trained with the contrastive Hebbian learning algorithm)
clearly mixes local and distributed representations. The input to
the model from either face or name is a distributed pattern over
5 (out of 16) input units. These input patterns appear to be more
strictly distributed than in the model of semantic memory. As far
as we can see, no content is assigned to any of the individual
components of these input patterns. The semantic units, on the
other hand, appear to be entirely local, as two of these are
assigned the interpretation "actor" and "politician."
These examples illustrate a weakness in the PDP approach as
articulated by Farah. The assertion that explanations of cognitive
phenomena should be distributed is insufficiently constraining.
There are infinitely many ways we may construct
distributed representations, as opposed to the single way we
construct local representations. Unless advocates of PDP modelling
are prepared to state exactly how representations should
be distributed, there is little to be gained from this dictum.
Researchers will inevitably choose a mode of distribution which
allows their model to work, but the reasons for this choice will
usually remain hidden. Appeals to the undeniably distributed
nature of neural processing are irrelevant here, unless researchers
are explicitly modelling particular structures in the brain.
Finally, there are pragmatic reasons to use local representations
where possible. Distributed representations are inherently
difficult to interpret. There are various ways one can
interrogate a model comprising this type of representation (e.g.,
dot-products with canonical representations, solution of simultaneous
equations, etc.). However, one cannot simply observe
their behaviour directly. This of course adds to a models mystique,
but mystique is not necessarily desirable in cognitive
theorising.
Does the locality assumption prevail? Contrary to Farah's
statement at the start of section 1.1, cognitive neuropsychologists
do not "generally assume" that damage to one component
of the functional architecture will have exclusively local effects.
Many cognitive neuropsychologists are exploring the potential
of PDP models as ways of implementing theories of cognitive
processing; Farah's text is peppered with examples of this (e.g.,
Hinton & Shallice 1991; Humphreys et al. 1992; Patterson et al.
1989).
In (at least) the case of covert recognition in prosopagnosia,
Farah seems to have focussed selectively on an example of "oldfashioned"
cognitive neuropsychologising. It is of course possible
to offer an account of the phenomenon without resorting to
an explanation in terms of a separate "awareness" component.
Such an account in fact already exists in the literature (Burton et
al. 1991). This model uses an interactive activation and competition
(IAC) architecture (cf. McClelland 1981), which includes
graded responses and interactivity (but not distributed representations).
Moreover, that account is not based on "a hypothesis
[derived] post hoc from the observed neuropsychological dissociation"
(cf. Farah, sect. 3.2.1). The account of covert recognition
was built upon a preexisting theoretical framework for face
processing and person identification (Bruce & Young 1986, itself
a revision of earlier work by Hay & Young 1982). This framework
has been built on converging evidence from experimental psychology
and neuropsychology, and in its latest stage of development
has implemented part of the framework in IAC terms
(Bruce et al. 1992; Burton et al. 1990; 1991). We did not need to
overturn the apple (orange?) cart to develop interactive simulations;
instead, these form a natural progression from the "boxand-arrow"
style of theorising which preceded them. One of our
worries about the style of PDP theorising exemplified in Farah s
target article is that it seems to represent punctate modelling of
isolated phenomena. We find models (of any architecture) more
constructive when they build upon and accommodate previous
bodies of data and theory derived from diverse sources.
In conclusion, we agree with Farah's call for gradual and
interactive models in neuropsychological and cognitive theorising.
Many cognitive neuropsychologists appear to share this
62 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Co7nmentary/Favah: Neuropsychological inference
view. However, we take issue with the assertion that these
models need to be distributed (except in the trivial sense of
compositionality). Local representations in such simple architectures
as IAC networks carry all the advantages of the interactive
approach, but none of the problems associated with distributed
representations.
Regional specialities
Brian Butterworth
Department of Psychology, University College London, London WC1E 6BT,
United Kingdom
Electronic mail: ucjtsbb@ucl.ac.uk
The first puzzling feature of Farah's "critique" is this: Who is
being criticised? She claims that the locality assumption (LA) is
ubiquitous among neuropsychologists. She cites four researchers
in four domains who are meant to exemplify this
commitment, but she does not demonstrate that they "assume
that damage to one component of the functional architecture
will have exclusively 'local' effects"; nor that any of the researchers
assume that these components are informationally
encapsulated. I can think of no one who has maintained in print
that all components of the brain's functional architecture are
informationally encapsulated. Even Fodor (1983) separates
modularised - and hence encapsulated - input systems from
nonencapsulated central systems. This is a distinction Farah
does not mention. Why is information encapsulation picked on
as the sole defining characteristic of the neuropsychologists'
functional components? Why not domain-specificity, which
would be a much more plausible choice for most neuropsy-
chologists?
When she comes to consider neuropsychologists' explicit
accounts of their own methodologies, Farah details the work of
two influential methodological theorists who, by her own admission,
do not hold the LA: Shallice's (1988) account of "isolable
subsystems' entails, according to her, that "the locality assumption
is not strictly true"; and Caramazza's (1986) "transparency
principle" is "probably weaker than the LA." They are nevertheless
attacked as if they do hold LA.
Neuropsychologists - not to mention neurologists and neuroscientists
- certainly believe that regions of the brain may have
specialised functions. They do not assume this in order to make
neuropsychology possible: they infer it from the abundant
phenomena. The second puzzling feature, therefore, is this:
Does Farah believe that regions of the brain do not have
specialisations? Does she believe in the theory of "mass action'?
She writes sometimes as ifshe did: her "constraining principles'
of distributed representation, graded information processing,
and interactivity are consistent with this theory.
A third puzzling feature: Farah is inviting us to reject the LA,
if we ever held it, in favour of a parallel distributed processing
(PDP) approach, on the grounds that theories based on three
PDP simulations do a better job explaining neuropsychological
data than previous non-PDP accounts. Now, of course, the fact
that some A(bnormal performances) are B(est explained by
PDP), does not entail that all A are B. Even to licence the
inference from one better PDP account to a rejection of the
universal necessity of the LA she needs to show that the inferior
explanation assumes locality in Farah's sense.
Certainly this is not the case for Warrington and Shallice s
story about category-specific deficits (Shallice 1988, Ch. 12;
Warrington 1975; 1981). Warrington and McCarthy (1987) quite
explicitly entertain differential weightings for different types of
infqrmation. This, they argue, is necessary to explain finegrained
within-category effects - such as selective deficits for
fruit and vegetables (e.g., Hart et al. 1985). Thus
colour, shape, motion and location are known to be separable both
physiologically, anatomically and psychologically at very early stages
of information processing. . . . It seems not implausible to suggest
that this early segregation may have concomitants for later stages of
cognitive analysis and that the evidence provided by or derived from
such functions, i.e. channels, may interact differentially with information
from other sources, (p. 1291; my italics)
The processing of information about living things is, for them,
though perhaps localised, explicitly not informationally encapsulated.
Shallice (1988, p. 302) notes, regarding category specificity:
"Instead of conceiving of the semantic system as a set of
discrete subsystems (functions, sensory properties, and so
on) . . . it may be more useful to think of it as a giant distributed
net in which regions tend to be specialised for different types of
processes." So an attack on standard neuropsychological accounts
of category-specific deficits would not be an attack on a
position here that entails the LA.
If Farah wishes to persuade neuropsychologists of the usefulness
of PDP modelling, she needs to demonstrate that a single
network can be selectively lesioned to produce their favourite
type of observation: the double dissociation. Has she done this?
Her treatments of attention and face recognition deal only with a
single dissociation. Her only case of modelling a double dissociation
is the category-specific losses in semantic memory, where
she shows selective impairment of living (Fig. 3, top panel) and
nonliving things (Fig. 3). This has been achieved by selectively
damaging one set of units ("visual semantic memory units") to
get a deficit of living things, and another set of units ("functional
semantic memory units") to get the deficit of nonliving things.
This is not formally different from the position she is attacking.
The architecture of the model in Figure 1 is identical to the one
in Figure 2. Only the labels have been changed. It may well be,
as she has argued in Farah and McClelland (1991; and indeed as
Warrington and McCarthy had argued on the basis of patient
data), that labelling the nodes "functional" and "visual" is to be
preferred, but this cannot bear on the question ofarchitecture or
theoretical framework. There are still sets of nodes dedicated to
specific functions. Like the rest of us neuropsychologists, she
explains double dissociations in terms ofselective damage to two
separable systems — in neural terms, two regions, each with its
own speciality.
Locality, modularity and numerical cognition
Jamie I. D. Campbell
Department of Psychology, University of Saskatchewan, Saskatoon,
Saskatchewan, Canada S7N 0W0
Electronic mall: campbellj@sask.usask.ca
Farah does not discuss numerical cognition in her target article,
but much recent research on number processing in normal and
brain-damaged subjects has focused on the issue of locality,
modularity, and selective impairments. In this commentary I
outline how the locality assumption has been applied to numerical
cognition and describe phenomena from normal subjects
that, consonant with Farah's conclusions, challenge the
locality assumption and the simple type of dissociation logic it
promotes.
Architectures for cognitive number processing
Modular model. The locality assumption is inherent in one of
the prominent theories of cognitive number processing and
dyscalculia, the modular model introduced by McCloskey et al.
(1985; see McCloskey 1992 for a review of related research).
According to the model, basic number processing is comprised
of three functionally distinct groups of processes specialized for
number comprehension, calculation, and production, respectively.
The comprehension system converts different surface
notations (e.g., digits, written, or spoken number words) into an
abstract (i.e., modality-independent) semantic code that provides
the basis for subsequent processing in the calculation or
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 63
Commentary/Farah: Neuropsychological inference
production systems. The calculation system stores numerical
information in the abstract format and includes memory for
basic numerical facts, rules, and procedures (e.g., 6 + 7 = 13, 6
x 9 = 54, 0 X N = 0, 0 + N = N). The production system is
comprised of modules that convert the abstract output from the
comprehension or calculation modules into specific output formats,
such as digits or written or spoken number words.
The locality assumption is inherent in the modular model
because it is assumed that (1) the hypothetical modules are
represented separately and so can be disrupted independently
by brain damage, and (2) no component process is involved in
the inner workings of the others (McCloskey et al. 1992,
pp. 496—97). McCloskey (1992) reviews case studies that identify
selective deficits corresponding to the major subsystems in
the modular model and that, given the locality assumption,
appear to validate the functional modular architecture assumed
in the model. For example, McCloskey, et al. (1986) observed
patients with impaired number-reading skills who could successfully
perform certain numeral transcoding, comparison, and
calculation tasks. Conversely, other patients were observed with
number-reading and number-comparison skills relatively intact,
but with impaired calculation (Sokol et al. 1991). Such dissociations
seem to support the view that calculation processes are
independent of the encoding and production mechanisms that
mediate number reading.
Interactive model. Campbell and Clark (1988; 1992; Campbell
1992; 1993; Clark & Campbell 1991) challenged the locality
assumption on which the modular model is based. They proposed
an alternative encoding complex theory in which numerical
encoding and calculation functions are integrated and interactive
and depend on modality-specific processes rather than
abstract codes. One compelling source of evidence for the
encoding-complex view came from analyses of normal adults'
speed-induced errors of simple addition and multiplication
(Campbell 1992; 1993; Campbell & Clark 1992). The errors
frequently involved operand intrusions in which a problem
operand appeared in the error response (e.g., 2 + 9 = "nine";
8 x 4 = "twentyfour"). Intrusion errors are important because,
as summarized below, they demonstrate notation-dependent
interactions of numerical encoding, retrieval, and response
mechanisms that cross basic functional boundaries assumed in
the modular model. In other words, operand-intrusion errors
appear to be products of strikingly nonlocal, interactive
processes.
Campbell (1993) demonstrated three prominent characteristics
of operand intrusions that support these conclusions. First,
intrusions were much more frequent with problems in numberword
format (e.g., nine X six = ?) as opposed to Arabic-digit
format (9X6 = ?), and the effect of notation on intrusions varied
with arithmetic operation (i.e., multiplication or addition; see
Campbell, 1993, for a detailed discussion). Notation X operation
interactions demonstrate that some processes of calculation
vary with surface form. Second, intrusions frequently preserved
the number-word lexical class (i.e., tens or ones words) corresponding
to the input-order or position of the intruding operand
(e.g., 6 x 9 = "sixty three"; 9 x 6 = ("thirty six"). This
characteristic implies that intrusion errors are due to spontaneous
number-reading processes that converge with calculation
processes at some point in processing. A third feature of intrusions
demonstrates that the point of convergence cannot be
localized at a "postcalculation" stage: if operand intrusions arose
by the priming of postretrieval lexical processes, then intrusions
would frequently produce random answers. Instead, intrusion
errors usually involved answers that were associatively or semantically
related to the problem (e.g., 8 x 4 = "twenty four").
This implies that numeral reading processes penetrate the
ongoing arithmetic retrieval process, possibly because both
processes compute similar verbal-phonological structures.
Taken together, these characteristics of intrusions demonstrate
that aspects of number reading and arithmetic are interactive
and determined by surface notation, rather than separate,
notation-independent processes.
Interactive functions and selective deficits. The specific features
of intrusion errors produced by normal subjects cast doubt
on the locality assumption underlying the modular model;
consequently, they also cast doubt on the validity of interpreting
selective deficits of number processing as direct evidence about
the functional architecture. The notation x operation interactions
revealed by intrusion errors violate the locality assumption
because such interactions admit the possibility that a disruption
of modality-dependent encoding processes could selectively
disrupt specific calculation or production processes downstream.
Thus, intact performance on encoding "control tasks"
does not necessarily eliminate encoding processes as the source
of specific calculation or production deficits. Furthermore, the
evidence that distinct numerical functions such as number
reading and arithmetic-fact retrieval are interpenetrated greatly
complicates the functional classification of selective deficits. For
example, the evidence that number reading and arithmetic
retrieval processes are strongly interactive in normal subjects
implies that a reading-related deficit (e.g., a weakened capacity
to control or inhibit number-reading processes) could disrupt
calculation, while other number-processing skills, including
number reading, were relatively spared.
Although it is likely that there are genuinely modular cognitive
systems that respect the locality assumption, complex skills
such as number reading, comprehension, and calculation probably
are not independently localized. Instead, consistent with
Farah's conclusions regarding several other cognitive domains,
there is evidence in numerical cognition of a substantial degree
of modality specificity and functional interactivity that questions
the locality assumption.
Discarding locality assumptions: Problems
and prospects
Ruth Campbell
Department of Psychology, Goldsmiths College, London SE14 6NW, United
Kingdom
Electronic mail: r.campbell@gold.ac.uk
Farah argues that the locality assumption in neuropsychology is
not useful for further theoretical understanding of cognitive
processes since local damage in complex dynamic systems has
effects beyond the site of damage. In some ways this is akin to
showing that when a stone is dropped in a pond there are ripples
from the epicentre. It is a useful demonstration for those who
might deny that complex dynamic systems, like cognitive ones,
including brains, have such characteristics. Furthermore, Farah
is right to point out that such denial is a common (though not a
universal) feature of theorising in cognitive neuropsychology.
However, as the stone analogy might suggest, there are
reasons for not abandoning the locality assumption prematurely.
Farah suggests that "we . . . lack clear heuristics for selecting
models to test." The locality assumption itself, when used
properly, can surely offer just such a heuristic. Farah has
previously pointed out that one means of delimiting functional
subsystems (hence defining the constituent layers of hierarchically
arranged systems for simulation) is to investigate
patterns of double dissociation of function in association with
patterns of associated disorder. She has successfully used this
tactic to indicate the precise fractures between face processing
and reading (Farah 1991). The double dissociation method is
strict - for example, the covert-overt processing distinction
would not have been a candidate for system-schism since there
are no clear cases ofabsence of covert processing in the presence
of overt skill. Furthermore, constellations of associated disorders
can give necessary clues for locating the fault-lines between
64 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Commentary/Farah: Neuropsychological inference
subsystems. In other words, Farah and her colleagues are
already making effective use of locality assumptions, albeit
strictly defined locality assumptions, in driving their theoretical
simulations. A less radical conclusion of her target article is that
some locality assumptions are justified, others are not.
A second reason for not abandoning all locality assumptions is
that their utility (or the lack of it) has not yet been fully tested
within simulations themselves. A variety of disturbances instantiated
in simulations is needed to extend the validity of Farah's
claims concerning the nonlocalisation of effects. These include
the effects of lesion combinations: when two stones are dropped
in the pond the ripples interact in previously unforeseen ways.
Which model Is best? Once we accept Farah's general point
concerning the importance of simulations, further problems
arise, which she recognises. How do we choose between different
means of modelling complex dynamic states? For face
recognition, Burton et al. (1991) have described a simple interactive
activation model which simulates precisely the same
phenomena as those instantiated in the model described here by
Farah et al. (1993). Yet the organising principles of the two
models are sufficiently different for it to be clear that they are
not isomorphic. The Burton et al. model has no learning algorithm,
hidden units, or distributed representations. It does have
a further "localisation assumption" in its distinction between
"person identity nodes" and other semantic representations.
Since both these models show covert face processing in the
absence of overt face knowledge, how are we to know which is
better? Perhaps all dynamic models that capture probabilistic
representations at different levels might work? Even models
with organising principles quite different from those involving
distributed activation (other combinatorial mathematical
models, for instance) might perform the covert processing trick,
too. Massaro (1988) has alerted us to the possibility of overpowerful
modelling in parallel distributed processing (PDP). It is a
warning that should be heeded.
Prospects: Distant effects of a local analysis. One of the most
useful functions of Farah s target article is that it allows us to
loosen the self-imposed modularity straitjacket. With the old
localising assumptions, remediation and rehabilitation for brain
damage were distinct and sombre enterprises. A missing or
damaged function cannot be replaced, only bypassed. With
these assumptions relaxed, more is possible; not least, an
explanation of the wide variety of modes of response and
recovery to brain damage. And not just brain damage; striking
aspects of cognitive variability can be observed in development
as well. Greater functional plasticity may be inferred from the
assumption of a missing or partial component within a connexionist
system than within a more localised one. Congenital sensory
loss provides an example. The primary characteristic of
people born deaf is that their mastery of cognitive processes that
rely on heard language is far more varied than that of hearing
people. Deaf people of very similar background, constitution,
and intelligence may or may not achieve spoken language,
"inner speech," regularity effects in reading and spelling, and so
forth (Campbell 1992; Dodd & Murphy 1992). A strictly modular,
localising approach has difficulty with this range of achievements,
which would not be predicted when the sensory input is
too limited to deliver the required distinctions. An interactive
systems approach advocates a more relaxed stance, for activity at
higher levels would be slowed and possibly skewed by profound
lack of sensory discriminanda, but it need not be blocked. Such
an approach could be used to find the conditions under which, as
in the case of the deaf with good language, "a little can go a long
way." The loosened approach advocated by Farah may also help
us understand some apparently modular developmental phenomena
which are nevertheless not as circumscribed as "tight"
modular theory suggests, such as specific language impairment
(Bishop 1992) and its apparent converse: language skills in the
"savant" with poor intelligence (Smith &TsimpIi 1991). This is a
long way from the cognitive neuropsychological focus of Farah's
paper, yet the implications reach out quite directly from it, just
as the ripples from the stone cast in the pond.
Casting one's net too widely?
D. P. Carey and A. D. Milner
Psychological Laboratory, University of St. Andrews, St. Andrews
KY16 9JU, Scotland, United Kingdom
Electronic mail: dpd@st-and.ac.uk.; adm@st-and.ac.uk
1. The locality assumption as a starting point. Dissociations are
the meat and drink of experimental neuropsychology. But no
such observation is strong enough to enable the investigator to
make an "inference" from it. To suppose otherwise is to misrepresent
most neuropsychological reasoning. In general, the data
lead instead to a hypothesis, and the first hypothesis to be
entertained should be the simplest one that would (a) fit the
facts, (b) have some biological plausibility, and (c) be testable. In
practice, the initial hypothesis will generally be one implicitly
based on at least a weak version of the locality assumption. But a
hypothesis is only a beginning, never a conclusion: the next step
is to look for independent evidence that might challenge or
support the hypothesis. Ideally, one seeks convergent evidence
from other forms of enquiry such as neurophysiology or functional
anatomy. In many cases in cognitive neuropsychology,
however, this may be unobtainable, requiring one to make do
with fresh neuropsychological evidence garnered from other
patients or from normal subjects.
In different parts of the brain and in different functional
systems, the likelihood that some version of the locality assumption
might be helpful when framing an initial hypothesis will
vary enormously. In the visual system, for example, a great deal
of modularity appears to be present (Felleman & Van Essen
1991). Therefore, when a behavioral dissociation is discovered in
this domain, hypotheses as to the role of different areas of the
cortex do not generally deserve to be greeted with hollow
laughter. A recent example is a hypothesis generated to explain
a double dissociation between the visual capacities of an agnosic
patient (Goodale et al. 1991; Milner et al. 1991) and patients
with optic ataxia (Jakobson et al. 1991; Perenin & Vighetto
1988). This hypothesis, that the functional architectures for
visual recognition and visuomotor guidance might be largely
independent, was strengthened by data from behavioral, neurophysiological,
and neuroanatomical findings (Goodale & Milner
1992; Milner & Goodale 1993). In no sense was the proposal
inferred from the empirical dissociations found in the two types
of patient, however: rather, the findings were used along with
other available evidence to generate a testable hypothesis that
makes explicit predictions about the functional properties of two
streams of visual processing in human and nonhuman primates.
That hypothesis (and in fact any hypothesis about functional
modules in the visual system) has to be constrained by the
current evidence for elements of both serial and parallel processing,
and for considerable cross-talk between separate cortical
areas and the functional modules that may lie within them
(Merigan & Maunsell 1993). The modular proposals of Goodale
and Milner accordingly have to be tempered with a recognition
that the hypothesized functional streams in the cortex would not
operate in isolation from one another. In fact, the obvious need
for object identity to be able to inform visually guided prehension
demands an interaction between the two systems. A patient
has recently been described (Sirigu et al., personal communication)
who cannot use object knowledge in this way; it may thus
be hypothesized that she has suffered a neural disconnection
between the two systems.
Although different functional modules will inevitably interact
with each other much of the time, this does not mean that in
some instances they may not behave rather autonomously.
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 65
Commentary/Far ah: Neuropsychological inference
Those instances may provide the initial evidence for modularity;
to ignore such evidence because it appears "naive" to accept the
locality assumption would be a dereliction of scientific duty. Of
course, the conditions necessary for the occurrence or nonoccurrence
of such instances would be incorporated into the
functional hypothesis.
2. Nets: What do they catch? The explosion of neural net
models in the recent neuroscience and cognition literature
reflects the immense fascination these models have for many
researchers (e.g., Hinton 1992), but although neural nets often
have fascinating properties, in practice many of the proposals for
direct analogies to brain/cognitive function can be highly problematic
(Crick 1989). In particular, any neural net which produces
a desired output from a specified input is hugely underconstrained;
an infinitely large number ofsolutions can be found
for each problem addressed (Fodor & Pylyshyn 1988; Reeke &
Sporns 1993). That is, solving an input-ouput problem which has
several computable solutions means little more than that the
problem is solvable; for such nets to model brain function they
have to do more. The explanatory utility of a given net is rather
limited unless it has at least two properties. First, it should be
biologically plausible; second, it should lead to testable predictions
in normal subjects and patients, predictions not specified
by the input/output characteristics of the system it purports to
model (see Reeke & Sporns 1993).
As a class of models, neural nets undoubtedly provide a step
in the right direction insofar as they emphasize plasticity,
interconnectedness, and parallelism. The evidence for structures
in the real CNS that look like the postulated nets is still
relatively scant, however (Eagleson & Carey 1992). All three
networks endorsed in the target article (like many others, e.g.,
Kettner et al. 1993; Plaut & Shallice 1993) utilize the backpropagation
algorithm, which has been repeatedly criticized for
its lack of biological feasibility (Crick 1989; Eagleson & Carey
1992). Others have made attempts to build more "biologically
plausible nets" (e.g., Mazzoni et al. 1991a; 1991b), but these
contain similarly questionable assumptions about brain function.
For example, the learning rule now advocated by Andersen
and his colleagues (Mazzoni et al. 1991a; 1991b) does not bypass
the "spatial crosstalk" problem (conflicting error messages to the
same hidden unit), which is a difficulty for it and for many other
nets (Jacobs & Jordan 1992).
3. Disengagement of visual attention. Last, we wish to question
whether the second of the author's three examples can be
correctly characterized as an instance of the locality assumption.
Impaired shifting of visual attention was experimentally documented
in patients exhibiting clinical "extinction" following
unilateral damage to the parietal lobe (Posner et al. 1984). The
patients had a particular problem in detecting visual signals in
the contralesional field following an invalid warning cue located
in the ipsilesional field. The authors hypothesized that the
deficit was one of disengaging attention from the cue, but
the patients were also impaired even when the warning cue
was placed centrally (whether it was symbolic or neutral),
provided that the target stimulus was contralesional. The only
kind of "disengage" deficit that could have explained the impairment
accordingly had to be one of disengaging-attention-ina-contralesional-direction.
And indeed more recent evidence
directly supports such a directional interpretation (e.g., Posner
et al. 1987). Thus, the data were never explicable in terms of a
"disengage" operation independent of later components in the
attention-shifting process.
If a pure "disengage" operation would not figure in any
plausible hypothesis to account for the neuropsychological data,
however, how does tlie particular model proposed by Cohen et
al. (in press) help our understanding of this disorder of shifting
attention? It certainly does not explain the patients' difficulty in
shifting attention from a central site in the contralesional direction.
No doubt it could be changed in an ad hoc way so that it
did, but how does one then choose among the many possible
different neural net models that could be devised? We remain
uneasy about the heuristic and explanatory value of a class of
theories against which no evidence can ever count decisively.
Modularity, interaction and connectionist
neuropsychology
Nick Chater
Neural Networks Research Group, Department of Psychology, University of
Edinburgh, Edinburgh EH8 9JZ, United Kingdom
Electronic mail: nicholas@cogsci.ed.ac.uk
Farah argues that cognitive neuropsychology assumes a modular
cognitive architecture, in Fodor's (1983) sense, and that this
leads naturally to the "locality assumption." She recommends an
alternative class of computational models, interactive connectionist
networks, which violate locality. Although the specific
interactive connectionist models she discusses are interesting
alternatives to existing box-and-arrow accounts in their respective
domains, the general arguments they are intended to
illustrate are less compelling.
First, violations of locality are common in modular as well as
interactive systems. Consider the muscular system, which has a
clearly defined modular structure. Damage to one component
(for example, straining a particular leg muscle) may cause
significant compensatory changes in the behaviour of others
(causing a completely different gait, or even a different method
of locomotion - e.g., hopping rather than walking). Thus, the
behaviour of a component, even in a modular system, may very
well change immediately if another component of that system is
damaged. In psychological terms, one would say that damage
may cause patients to change their strategy for carrying out a
particular task. For example, a subject who has lost the putative
lexical reading route might start to rely on phonological or
semantic routes which were not involved in premorbid reading.
Nonetheless, whereas what we might term "behavioural locality"
may be violated in such situations, locality of function
need not be. The functional capabilities of the individual muscles
(i.e., the forces they can generate) will presumably be
unchanged immediately after damage elsewhere in the muscular
system. However, these functional capabilities will themselves
rapidly alter as the system becomes adapted to the new
mode of function. Just as muscles adjust rapidly to their new
role, so components of a modular cognitive system may rapidly
learn to adapt to their new cognitive function. Violations of
locality, either behavioural or functional, will make it very
complex to draw inferences about normal function from impaired
performance.
Second, the modularity thesis (Fodor 1983) is not addressed
by Farahs models, despite being the subject of the introductory
discussion. Fodor's contention, which Farah opposes, is that the
cognitive processes involved in perceptual analysis, motor control,
and language processing are organized into modules which
are informationally isolated from one another and from the
unencapsulated central processes which mediate common sense
thought. The precise grain of such modules is not specified, but
Fodor's principal concern is to defend the view that large
cognitive domains (e.g., language processing, visual analysis,
etc.) are subserved by separate modules. This position is entirely
consistent with the models that Farah presents: one model
concerns memory, which is generally not thought to be informationally
encapsulated, and the others can reasonably be interpreted
as partial specifications of modules for attention and face
recognition. Furthermore, the assumption of some kind of
global modularity seems to be a presupposition of the very
attempt to model a specific cognitive function. If the functioning
of the face-recognition system, say, is really intimately bound up
with the function of many or even most other cognitive pro-
66 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Co7nmentaryl Farah: Neuropsychological inference
cesses then a free-standing face-recognition model is surely not
possible.
Third, the emphasis on the interactive nature of connectionist
models is idiosyncratic. Although McClelland (1991) emphasizes
interaction in his GRAIN networks, most connectionist
models are feedforward networks (or variants) trained by backpropagation.
In experimental cognitive psychology many of the
same phenomena may be captured by both interactive and
feedforward network architectures (e.g., McClelland & Elman
1986; Norris 1990; Shillcock et al. 1992). Furthermore, connectionist
neuropsychological models, such as Patterson et al.'s
(1989) model of surface dyslexia and Hinton and Shallice's (1991)
model of deep dyslexia, derive interesting and detailed predictions
using feedforward networks. Since the analysis of the
general patterns of breakdown observed in even simple feedforward
networks is extremely difficult (Bullinaria & Chater 1993),
it is surely much too early to decide between alternative network
architectures for neuropsychological modelling.
What is fundamental, and what rightly takes centre stage in
Farah's general discussion, is the difference between connectionist
neuropsychological models and the traditional boxand-arrow
approach. Traditional box-and-arrow models are so
underspecified that only very gross patterns of damage largely
concerning task dissociations can be predicted. [See Precis of
Shallice's From Neuropsychology to Mental Structure, BBS
14(3) 1991. ] By contrast, connectionist models are fully specified
mechanisms on which the behavioural effects of all manner of
damage can readily be tested, and which, when intact, can be
assessed as models of normal performance. This is perhaps the
real promise of Farah's work and that of the rest of the growing
field of connectionist neuropsychology.
ACKNOWLEDGMENT
This work was supported by grant SPG-9029590 from the Joint Councils
Initiative in Cognitive Science/HCI.
Modularity, abstractness and the interactive
brain
James M. Clark
Department of Psychology, University of Winnipeg, Winnipeg, Manitoba,
Canada R3B 2E9
Electronic mail: clark@uwpgO2.uwinnipeg.ca
Farah has contested the assumption that brain functioning is
localized or modular and has argued for a highly interactive
brain. I cite another example against modularity, describe an
added benefit of the competing associative view, and challenge
further the received view of brain functioning.
Number processing. The locality assumption rejected by
Farah for semantic taxonomies, visual attention, and face recognition
is also central to other areas. In number processing,
McCloskey and his colleagues (e.g., McCloskey et al. 1986;
1992; Sokol et al. 1989) have proposed a modular view based on
distinct comprehension, calculation, and production modules
that communicate solely by mediating abstract number codes.
Campbell and Clark (1988; 1992; Clark & Campbell 1991)
have presented an alternative, encoding-complex view of number
processing in which numbers are represented as concrete
codes in diverse formats (e.g., digits, number words, analogue
codes). In place of function-specific modules, interactive excitatory
and inhibitory associations among specific codes perform
number identification, calculation, and production.
The arguments advanced against modular views of number
processing have reflected criteria similar to those cited by
Farah. In particular, nonlocalized associative theories can accommodate
findings thought to support modularity and can
explain phenomena that are awkward for modular views. The
abstract number codes that segregate modules are also questionable
(see below). Although these claims have been challenged
(see papers cited earlier), the example nonetheless
demonstrates the generality of the issues and arguments advanced
by Farah.
Associative models. Modular views are weakened by demonstrations
that nonlocalized associative theories can explain behavior
in terms of excitatory and inhibitory connections among
mental representations. Associative theories include connectionist
models, such as those described by Farah, as well as
related approaches that do not assume distributed representations
(e.g., Campbell & Oliphant 1992). Farah points out the
empirical adequacy and other benefits of such models.
One particular strength of associative models not emphasized
by Farah is that they are undeniably mechanistic; that is, they
identify physical events (e.g., representations, activation) intervening
between inputs to and responses of the cognitive system.
This mechanistic quality elevates associative models above psychological
theories that interpret behavior by abstract symbolic
processes (e.g., "if-then" procedures, retrieval) that all too often
say little about concrete, underlying mechanisms. The associative
approach compels researchers to deal with the underlying
mechanisms, or at least to admit their present ignorance about
those mechanisms. In turn, the translation of psychological
metaphors into physical mechanisms will perforce reveal the
associative quality of the underlying causal links and neuronal
systems.
Associationism has a controversial history. Associative models
have been criticized for being vague and weakly specified, and
for lacking formal constraints. Farah correctly noted that connectionist
models are not intrinsically more post hoc than highlevel,
symbolic models, and also that empirical constraints
should be more important than formal constraints. Undue
emphasis on formal properties has contributed to the unwarranted
faith in modularity and obstructed the development of
mechanistic, associative models. Bever et al. (1968), for example,
argued on formal grounds that associative models in principle
could not explain many facets of human behavior. Such
arguments count for little in the face of successful connectionist
and other associative models.
The received view. Farah challenged the tacit and widely held
assumption that brain and cognitive processes are localized
and modular, but the received view is based on other fundamental
premises that are similarly doubtful. In particular, a
critical evaluation is needed of the assumption that abstract
semantic codes and processes underlie human behavior. The
abstract code and locality assumptions tend to cooccur (e.g.,
abstract codes define the boundaries between McCloskey et al.'s
modules).
Despite rejecting modularity, Farah retained abstract semantic
codes and, implicitly, the assumption of a distinct semantic
module. This is clearest in her models for taxonomic categories
and face perception (Figs. 1 and 11). Figure 11, for example,
identified special semantic units to identify such features as
"actor. "This abstract code assumption is unnecessary, inasmuch
as the word "actor" and other similarly specific codes can
subserve functions attributed to semantic codes and can avoid
the artificial distinction between semantic and nonsemantic
processing modules (i.e., hidden "locality").
Thus Farah unadvisedly left intact a second central fallacy of
much cognitive and brain theorizing, namely, that a semantic
system exists distinct from patterns of activation in specific
verbal or nonverbal codes. According to strong associative views
(e.g., Campbell & Clark 1988; Clark & Campbell 1991; Paivio
1986), meanings and concepts emerge from interactive brain
processes involving associations among words, objects, motor
images, and other concrete representations. The added assumption
of abstract, semantic codes is superfluous.
Conclusions. Farah's challenge to locality is a positive step
toward ridding the behavioral and brain sciences of unwarBEHAVIORAL
AND BRAIN SCIENCES (1994) 17:1 67
Commentary/Farah: Neuropsychological inference
ranted, restrictive assumptions about the human brain and
related psychological processes. The modularity assumption
and correlated claims about abstract codes lack a sound empirical
foundation. They only became dominant because of fallible
rational arguments and because their proposed view of cognition
and the brain was amenable to scientists' thought processes
and available computational tools. More generally, Farah has
demonstrated how vital it is that every scientific assumption, no
matter how rational it seems, be questioned, be put to rigorous
empirical test, and be challenged by contrasting theories, such
as associative models based on interactive excitatory and inhibitory
mechanisms.
ACKNOWLEDGMENT
Preparation ofthis paper was supported by grant OGP0042736 from the
Natural Sciences and Engineering Research Council of Canada.
Further advantages of abandoning the
locality assumption in face recognition
Jules Davidoffa
and Bernard Renault"
"Department of Psychology, University of Essex, Colchester CO4 3SQ,
England and "University of Paris 6, CNRS URA654-LENA, Hopital de la
Salpetriere, 75651 Paris Cedex 13, France
Electronic mail: "jdavid@sx.ac.uk; b
martiner@arthur.citi2.fr
Farah proposes that dissociations reported in the neuropsychological
literature are the result of damage to interactive neural
networks and not to impairments at "localised" sites. There is, in
essence, nothing new about her opposition of global and stage
accounts of intellectual functions. The long history of the debate
can be gathered by Farah's introductory quotation from Ferrier
(1886) and it could have been equally replaced by ones from
Charcot (1883) or Freud (1891/1935). However, Farah is explicit
in her parsimony. For example, she shows how a neural network
for faces can be damaged to effect chance levels for overt
recognition but still retain connections that can facilitate learning.
A consequence of the model is that there is no need to
postulate a magic box within which resides the "conscious
awareness system" (de Haan et al. 1992).
Farah sidesteps the impossible task of defining consciousness
by showing that the results from overt and covert tasks are
interpretable from the same implementation; we recommend
that the exercise be extended. Network models would find it
convenient and more parsimonious ifthe implementation could
also include differences between the processing of unfamiliar
and familiar faces. These are unlike local models of the Bruce
and Young (1986) type that use a clearly separate stage for the
processing of familiar faces.
The study of prosopagnosia has been taken to validate the
locality assumption, but the evidence is somewhat in dispute.
Not one of the nine prosopagnosics tested by Schweich and
Bruyer (in press) showed normal performance in all tasks with
unfamiliar faces; similarly for the four prosopagnosic patients of
Davidoff and Landis (1990). The frequent connection between
impairments on tasks with familiar and unfamiliar faces indicated
to Davidoff and Landis (1990) that common processing was
involved. They suggested that the intact status of the neural
implementation should be assessed with superiority tasks based
on those of Homa et al. (1976). These tasks use unfamiliar faces,
and prosopagnosics, unlike other patients with posterior brain
damage, do not show object superiority effects. To accommodate
the Davidoff and Landis (1990) results, a local processing model
would be forced to infer that prosopagnosic deficits were based
on failure at the structural encoding stage for faces. Farah's
model, however, might be extended to cover impairments to
unfamiliar faces from a single lesion of the network.
We accordingly applaud the attempt to produce a network
implementation for face recognition but still feel it necessary to
ask whether Farah's model provides a satisfactory account for all
covert tasks that have been used with prosopagnosic patients:
First, why does the degraded representation produce a GSR
(galvanic skin response) to an unrecognised familiar face (Bauer
1984)? Is it because connections to limbic structures may be
activated by only part of the face representation? Compare, for
example, the equal GSR response to whole and part stimuli
demonstrated for words by Fuhrer and Eriksen (1960) in an
earlier debate concerning unconscious processing (see Dixon
1981).
Second, would lesions to Farah's network produce the systematic
changes to evoked potentials observed by Renault et al.
(1989)? They showed, for faces that were not overtly recognised,
that the amplitude of the P300 evoked potential was inversely
related to the probability of presentation of the face category.
Could Farah's model be sensitive to such short-term manipulations
of probability? Furthermore, the latency of the P300 ERP
- an index of stimulus evaluation time - increased with the
familiarity of the face. The results of Renault et al. (1989) imply
that extended coding produces an "attractor" from which it takes
a long time to escape. Could this be incorporated into Farah's
model?
Neurocomputing and modularity
Joachim Diederich
Neurocomputing Research Centre, School of Computing Science, Faculty
of Information Technology, Queensland University of Technology, Brisbane
Q 4001, Australia
Electronic mail: joachim@fitmail.fit.qut.edu.au
Farah claims that inferences about the functional cognitive
architecture can be made from neuropsychological data with a
"nonmodular" set of assumptions, that is, human information
processing is graded, distributed, and interactive. To support
this claim, Farah presents simulation data from three different
interactive systems. The nature of these simulation systems is
important, because according to Farah (sect. 3.3.2), the microstructure
of a cognitive system is relevant (if the locality assumption
is abandoned) because of its implications for the macrostructure,
that is, the functional cognitive architecture.
Although Farah stresses the importance of microstructure, all
three models fail to include common knowledge about it, for
example, connectivity patterns in the brain, the elaborate structure
of neurons, and so on. In addition, there are a number of
biologically unrealistic assumptions: neurons have both excitatory
and inhibitory connections; there is no differentiation of
neurons in various morphological types or transmitter types,
and neurons communicate by exchanging activation values (i.e.,
there is no coding of spike frequency or other communication
types; e.g., hormones).
Farah is using simple associative networks to show that a
strongly interactive system can explain established data without
the locality assumption. The simple associative networks are
inadequate for neural modeling, however, and violate common
knowledge about neural processing. It is therefore an open
question what kind of inferences can be made based on the
simulation results, in particular, what kind of inferences can be
made based on damaging biologically unrealistic networks.
It is widely acknowledged in modeling systems that an inputoutput
function at one level of organization can be simulated by
an infinity of models based on subcomponents from lower levels
(Shepherd 1990, p. 83). For cognitive and neural modeling, this
implies that the subcomponents should not be arbitrary but
must represent properties which can be found in real biological
systems. Farah fails to address this issue but uses a number of
assumptions that are inconsistent with common knowledge
about neural information processing.
Furthermore, the effect of damage to the networks can easily
68 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Commentary!Farah: Neuropsychological inference
be explained by the network structures. For example, in simulation
1, category-specific impairments (sect. 2.1.3), there are
seven times as many visual semantic units for living things as
there are functional semantic units. Therefore, because most of
the semantic input to the name units of living things is from
visual semantics, damage to visual semantics eliminates a
greater portion of the excitation needed to activate the names of
living things (sect. 2.1.3). Farah claims this result contradicts the
locality assumption because "when visual semantics is damaged
the remaining parts of the system do not continue to function as
before." This is not really surprising, given the way the network
is set up.
Farah (following Shallice 1988) points out that modularity
compared to interactionism is a matter of degree. A strong point
for interactionism can certainly be made, but Farah fails to
address a number of issues that are important for a highly
distributed, interactive system. For example, if a conceptual
representation is spread over some fraction of units, the chances
are high that the encoding will overlap and cause cross-talk
(Feldman et al. 1988). The biggest problem, however, is the
communication between subnetworks: because of the distributed
representation, only one "concept" at a time can be transmitted
between subsystems if each concept is a pattern on the
connections between the subsystems. Such a system is therefore
highly sequential because computation is based on passing
simple (numeric) messages. This communication problem does
not appear in Farah's relatively simple simulations but will be
relevant as soon as bigger networks with a large number of
subsystems are considered.
Work in computational neuroscience suggests better, alternative
ways of modeling: unsupervised or reinforcement learning
in sparsely connected networks, compact but still distributed
coding and communication via random links between subsystems.
Modeling that is constrained by recent results from
experimental neuroscience can make a stronger point for interactionism
than Farah's simulations.
ACKNOWLEDGMENT
Thanks to Shlomo Ceva for his comments on earlier drafts of this
commentary.
Clarifying the locality assumption
Clark Glymour
Department of Philosophy, Carnegie Mellon University, Pittsburgh, PA
15213
Electronic mail: clark.gtymour@andrew.cmu.edu
1. Distinctions. Farah's arguments turn on ambiguities in the
meaning of the "locality assumption." It is easy to state the
alternatives formally. A component C has input channels Iv
/2, . . . , /* from other components and possibly input channels
/fc+i, • • • , /*+,„ from the environment, where each channel is
viewed as a variable that can take on any of some range of values.
Component C likewise has output channels O,, . . .,0^ to other
components, and perhaps output channels O,+,, . . . , O,. to the
environment. In normal functioning, each component thus
determines an input/output function: O = Fc(/,, /2 . . .
f*+i> • • • > lk+nX where O is the vector of outputs. Ordinarily,
the set of inputs and outputs are assumed to be disjoint, but if F c
is understood to involve a time delay, however short, the sets of
input and output channels need not be disjoint. Since the inputs
/(, /2, . . . , If. are from other components, whose outputs are
functions of still other components and of the environment, and
so on, if we hold constant any entirely internal variables, the
value of O is also a function of some larger set of environmental
inputs, O = Hc ( £ , . . . Ep), where some of the E variables are
'/t+i> • • • > '«.+,„• When the system is not normal because some
component D other than C is damaged, there are corresponding
input/output functions for component C, which we can denote
byFc ,D (/,,/2 • • • lk>h+\< • • • Jk+J
respectively. Here are several logically distinct locality as-
sumptions:
(1) For any two distinct components, C and D,
FcOi, h • • • h. f*+i / * + J = W i > h • • • h(2)
For any two distinct components, C and D,
(3) For two particular distinct components, C and D,
FcVu h • • • h, h+>, • • • . / * + J = U / , , /, • • • /*,
h+i • • • , h+tii)
(4) For two particular distinct components, C and D,
//c (£,, . . . , £„) = //c ; D (£, £„).
(5) For a particular component C and for all distinct
components D,
Fc (/,, l2 . . . lk, Ik+l lk+m) = FCID(/,, /2 . . . lk,
(6) For a particular component C and for all distinct
components D,
I do not know which of these claims psychologists intend; we
rarely make ourselves clear. But one would be foolish to endorse
(2), which would be equivalent to thinking that even though the
battery is dead the car motor will turn the crankshaft which will
turn the wheels which will make the car move when you switch
on the ignition key. (6) may be a consequence ofwhat is meant by
the claim that module C is "informationally encapsulated."
Claims ofthe form (3), (4), (5), or (6) might be ofscientific interest
if particular components could be identified. In the absence of
clarity, it would be charitable to suppose that (1) is what is
usually meant by the locality assumption in general, and that (3)
is what is meant when people speak of locality for particular
modules. In any case, since (2) is so obviously and trivially false,
it has no scientific interest.
Unfortunately, Farah's examples only argue against (2). The
first of her examples gives a connectionist model in which
various disjoint collections of nodes are labeled as modular
components: visual semantics (vs), functional semantics (/s),
vision (v), and names (n). In the context of the model the two
latter serve as environmental inputs, so that normally,
Farah lesions vs and finds that,
Contrary to the locality assumption, when visual semantics is damaged
the remaining parts of the system do not continue to function as
before. In particular, functional semantics, which is part of the
nondamaged residual system, becomes impaired in its ability to
achieve the correct patterns of activation when given input from
vision or language. This is because of the loss of collateral support
from visual semantics.
What she has found is that (4) is not true when C =fs and D =
us and the E variables are v and n. Now of itself this is not of
much interest, since no one had contrary views about these
particular modules, and since the falsity of (4) for this case is
obvious from the functional structure. If the case is a counterexample
to some more general thesis, that more general thesis can
only be (2), since the example has no bearing at all on (1). And
because it is trivially false, (2) is of no interest.
The same considerations apply to the second example, which
provides a model of visual attention without a "disengage"
module. I do not object to the model Farah develops, but its
behavior when lesioned is only a counterexample to the absurd
localization thesis (2), and not to anything more interesting.
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 69
Commentary/Farah: Neuropsychological inference
Farah's third example, concerning relearning face recognition
after damage, is even more remote from any clear, interesting
general thesis about functional localization. It does show an
important capacity of neural net models to account for learning
phenomena that box-and-arrow diagrams do not address at all,
and that fact, not confusions about localization, ought to be the
lesson readers take from it.
Farah's models are interesting in themselves, and may even
be correct, or at least more correct than the alternatives she
discusses. I think she is also entirely right that connectionist
architectures form an enlightening set of models to account for
the data of cognitive neuropsychology. But the central line of
argument in the target article is very unfortunate.
2. What are functional modules? Farah's paper prompts a
question cognitive psychologists ought to try to be clear about:
In a connectionist architecture, what is a functional module or
component? A principal aim of the contemporary revival of
neuropsychology has been to get information about what modules
there are, what they do, and how they are or are not
connected. But if a connectionist architecture is correct, what is
a functional module?
One might say: a functional module is any collection of nodes
with an input set that is not the set of all other nodes and an
output set that is not the set of all other nodes. That proposal
allows distinct modules to share a subset of their nodes, which
seems reasonable, and keeps the function in functional. But
then what are the functional modules in a network in which
every node is adjacent to every other node (save possibly that
environmental nodes may not be connected directly to one
another)? For any set of internal nodes will receive input from
every other node and give output to every other node. Under
this definition, such a system has a single functional module.
Perhaps one should say instead that a functional module is any
set of nodes that form a clique - a set in which every node is
adjacent to every other node in that same set. That definition
also permits distinct functional modules to have a common
subset of nodes and preserves the formal content of "functional."
Then in a completely connected network we get a conclusion
opposite to the one in the previous paragraph: in a completely
connected network, every subset of nodes forms a functional
module.
Perhaps we should say that a functional module isn't specified
by input and output connections but by some feature of the
aggregate probabilities or strengths of influence a set of nodes
establishes between two other sets of nodes, an aggregate which
will be determined as much by the weights attached to links as
by the network topology. But then the notion of a functional
module seems to become vague, for strengths of influence and
probabilities are matters of degree.
What exactly can be determined about functional modules in
connectionist networks from the environmental input/output
behavior of normal and lesioned systems will depend on which
of these - or other - senses of "functional module" are adopted.
Until that is made clear, the combination of cognitive neuropsychological
data and terminology with connectionist computational
models offers endless possibilities for confusion.
And, finally, perhaps if the true architecture of cognition is
connectionist, we should stop talking about functional modules
altogether and just talk about networks and their topologies and
weights.
No threat to modularity
Yosef Grodzinsky and Uri Hadar
Department of Psychology, Tel Aviv University, Tel Aviv 69978, Israel
Electronic mail: yosef1@ccsg.tau.ac.il; uri-h@ccsg.tau.ac.il
In what aims to be a neuropsychological salute to connectionism,
Farah presents an argument with the following structure:
1. There is a ubiquitous assumption in neuropsychology
regarding the "locality" of functional lesions.
2. There is a family of models - of the connectionist variety that
violate this assumption.
3. Neuropsychological data are compatible with the latter
models.
4. Hence, the locality assumption is "probably not correct,'
and since it is the most basic tenet of the class of models
standardly assumed, this class of models is "dubious."
This argument contains three premises and a conclusion. Of the
premises one is probably correct (2), two are incorrect (1 and 3),
and the conclusion is a non sequitur (4).
1. Consider, first, the locality assumption as Farah sees it. In a
modular system, she contends, "each component minds its own
business and knows nothing about most of the other components.
What follows for a damaged system is that most of the
components will be oblivious to the loss of any one, carrying on
precisely as before." Hence, "selective deficit in ability A implies
a component of the functional architecture [of cognition]
dedicated to A." This is a view of locality all right, but we do not
believe there is even one "moclularist" who would subscribe to
it. Here is why.
Modules are connected. You can, after all, talk about what you
see or hear, and make the connection between the smell of
things and the way they look. Modularity, in its strictest sense,
requires that a module be unable to interfere with the action of
another, or gain access to its knowledge base. Yet the very
essence of the thesis is that while cross-modular exchange of
instructions is illicit, exchange of information (in one direction
at least) is a must. After all, what the system does is manipulate
symbols: accept representations as input, transform them
through a set of formal operations, and transmit them onward.
There may be many modules, yet they live in just one head.
Thus, the output of one module is input to the next one down the
line.
Returning now to neuropsychology, if one component is
damaged, its output (or lack thereof) will reflect the impairment.
Subsequent, unaffected modules will be fed abnormal input and
will, as a consequence, produce deficient outputs resulting,
potentially, in aberrant behaviors that may not be immediately
traceable to the damaged part. This is what makes work in
neuropsychology interesting and, alas, quite difficult. Modules
might thus be "oblivious" to the disruption of others, attending
to their business as usual; but clearly, if their input is now
irregular, so will be, most likely, the representations they
produce.
Farah makes no distinction between the action of a module
and the kind and quality of representations it spews out; and in
neglecting to do so, she misses the whole point about modular
systems. Yet the view expressed here is, so far as we know, the
standard view of modularity: a tiny disruption to one module
can, in principle, result in a huge impairment to the system as a
whole, precisely because each module works on its own; and
while its operation is insensitive to that of others, its output is
extremely sensitive to the results of the action of others, sensitive,
in other words, to input representations. This of course
runs contrary to Farah's claim, which confuses the separation of
actions - "informational encapsulation" - with links established
through information flow. It is for this reason that she interprets
data from dyslexia and aphasia in such an odd way. Phonological
dyslexia, for example, features a selective deficit in reading
nonwords. Under Farah's locality assumption, this would mean
there is a special processing component in every head, dedicated
to reading such sequences - hardly a plausible claim. Yet
the standard view is, of course, quite different: the graphemephoneme
route serves to explain both phonological and surface
dyslexia and is not custom-built for reading nonwords.
Another good example of a modular approach to dyslexia is
that of Shankweiler and Crain (1986), who focus on developmental
reading disorders. Seeking to steer clear from ad hoc claims,
70 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
they show how a large body ofdata from dyslexia - phonological,
syntactic, and other deficits observed in developmental dyslexia
- is accounted for by postulating a small bottleneck in early
phonological processing. Because this deficit occurs so early, it
projects all over, with detrimental effects on virtually every part
of the language-processing system that happens to be located
later. This model is explicitly modular, yet its strength and
generality derive from the fact that it does not assume locality
the way Farah does.
Similarly, one can demonstrate how the postulation ofa rather
limited deficit in one type of syntactic representation in agraminatic
aphasic patients can account for a wide variety of welldocumented
comprehension deficits in patients suffering from
this condition (see Grodzinsky 1990). Here Farah-style locality
shows up in its full weakness. She identifies a processing
component with each "ability," yet she does not specify what an
ability is. In the context of language comprehension, her locality
assumption would mean either that there must be a dedicated
processing component for the comprehension of sentences of
every structural type - a claim that is highly implausible for
anyone familiar with linguistic considerations - or that the data
from agrammatism (patterns of impairment and sparing that are
best described in syntactic terms) are unpredictable. Thus, the
locality assumption Farah argues against is neither held by
anyone, nor is it tenable when empirical considerations are
taken into account.
2. With Farah's second premise - that connectionist models
violate the locality assumption - we have no quarrel.
3. Farah's third claim, regarding compatibility of "neuropsychological
data" with connectionist theory, is made as if all
cognitive domains were alike (at least with respect to modularity):
Thus, demonstrations such as Farah's (that data from a
couple of domains are compatible with them) can "provide
existence proofs that principled inferences can be made in
cognitive neuropsychology without the locality assumption."
This is far from being the case, however, and claims regarding
certain domains cannot be carried over to all others (or even to
some central ones). The particular examples presented by Farah
come, ironically, from domains which on most accounts are not
encapsulated, hence nonmodular, since they appeal to knowledge
of the world, attention, and awareness. Yet for other
domains such as language (a rather central feature of the human
cognitive system), no such compatibility has ever been shown.
This has been discussed almost ad nauseam in the literature and
thus the arguments need not be reiterated here. Yet it is in such
domains that one should seek a demonstration of the type Farah
would like to argue for. We have yet to see how such models
handle selective language deficits such as agrammatism, in
which, as we said before, particular aspects of the syntactic
analysis of a sentence are disrupted, resulting in abnormal
comprehension patterns. We are unaware ofserious proposals of
this type.
4. Finally, we get to the non sequitur. It is a point of logic that
even if neuropsychological data are expressible in connectionist
models, this means little in itself. Theories, as everyone knows,
are vastly underdetermined by data, and the compatibility of
the available data with one of them does not, unfortunately,
deny its potential fit with another. Farah's attempt to turn a
seemingly positive point (the fit between connectionist theories
and her data) into a negative one (lack of fit with modular
theories) thus fails.
So, modularists need not worry: an attack based on a questionable
argument and doubtful premises does not put anything
of consequence at risk.
ACKNOWLEDGMENT
The preparation of this manuscript was supported by NIDCD grant
DC-00081 to the Aphasia Research Center, Boston University School of
Medicine.
Commentary/Farah: Neuropsychological inference
Go with the flow but mind the details
Glyn W. Humphreys and M. Jane Riddoch
Cognitive Science Research Centre, School of Psychology, University of
Birmingham, Edgbaston, Birmingham B15 2TT, United Kingdom
The idea that neuropsychological disturbances of cognition can
be interpreted in terms of models of normal cognition has a long
history and has been one of the driving forces behind the success
of cognitive neuropsychology for the past 20 years or so. Farah
takes issue with one assumption common to the application of
this idea, namely, that neuropsychological disturbances reflect
disruption to a single component of the normal cognitive system,
allowing other parts of the system still to function intact.
Following this "locality" assumption, a patient's deficit may be
used to define the nature of the (now impaired) functional
component in the normal processing system (see, e.g., Coltheart
1984 for an example of this argument).
Farah raises two questions: (1) Is the locality assumption
wrong, perhaps even positively misleading? (2) Can the discipline
of cognitive neuropsychology still make progress if the
assumption is abandoned? These questions are answered in the
affirmative, and we agree. However, we also wish to add cautionary
notes concerning the details of the arguments made in the
target article. To "go with the flow," ignoring cautionary details,
can threaten the baby when the bathwater is dispensed.
As evidence against the locality assumption, three pieces of
research are cited, all relying on simulation ofa neuropsychological
disorder in a connectionist model. The deficits concern:
apparent category-specific disorders of semantic knowledge,
problems in attentional disengagement, and covert knowledge
in prosopagnosia. In the first example, Farah argues that
modality-specific disorders of semantic knowledge can emerge
from a distributed memory system in which different forms of
semantic knowledge (visual/perceptual and functional knowledge
about objects) are highly interconnected and hence not
functionally independent. The locality assumption is wrong
because it leads to the inference that semantic knowledge is
separated into functionally separable processing systems (e.g.,
one concerned with visual/perceptual knowledge, one with
functional knowledge). In the second example, a simple connectionist
model with competitive attentional feedback systems in
each "hemisphere" is shown to mimic attention "disengagement"
problems when lesioned. Here the locality assumption
can lead to the inference that there is a disengagement module
in the attention system; the simulation shows that such a module
is not necessary. The third example shows that covert recognition
can emerge after partial damage to a recognition system (see
Shallice & Shaffran 1986 for an earlier version of this account);
covert recognition does not necessarily result from the disconnection
of intact recognition from a system involved with conscious
awareness of recognition. The locality assumption here
might lead to the inference of such a disconnection, and hence
(unnecessarily) to the inference that a specific system for conscious
awareness exists.
The difficulties for the locality assumption demonstrated by
these examples emerge from inferences about normal processing
based on functional deficits in neuropsychological patients.
The dangers in this have been stated before (see Seidenberg
1988 for one example), and the simulations reported by Farah
give the critical argument concrete force. Although, as noted by
Farah, many cognitive neuropsychologists have been circumspect
in their inferences concerning normal performance, and
although many have noted that patients need not have deficits
functionally localised to a single processing mechanism (e.g.,
Sergent 1987; Shallice 1988), such qualifying details have too
often been ignored.
Concerning Farah's specific examples, however, several cautionary
points can be raised in turn. First, consider the simulation
of category-specific deficits. To produce such deficits, Farah
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 71
Commentary/Farah: Neuropsychological inference
and McClelland (1991) selectively lesioned either the visual/perceptual
or the functional-knowledge units in their
model. Now, for this to happen in a real brain, these units would
need to be anatomically modular even if they are functionally
nonindependent because of cross connections. All is well providing
the anatomical and functional accounts are independent,
but this is likely not to be so. In real neural systems there is a
preference for short anatomical connections (e.g., Cowey 1985),
and this may in turn produce functional consequences: only
systems that are anatomically proximal may develop functional
interconnections (see Jacobs & Jordan 1992). Case studies also
show that patients with category-specific recognition deficits can
have intact visual/perceptual or functional knowledge (e.g.,
Riddoch & Humphreys 1987; 1992; Sheridan & Humphreys
1993). Such dissociations are not comfortable for a fully interconnected
distributed processing system. The distinction between
anatomical modularity and functional nonmodularity can be
questioned.
Second, consider the case of attentional disengagement. Like
Farah, we strongly suspect that disengagement describes a
functional operation rather than a distinct processing mechanism
in the brain (Humphreys & Riddoch 1993). It may nevertheless
be wrong to conclude that only one mechanism is
involved when people engage and disengage attention on objects.
A simple single-mechanism model such as the one implemented
by Cohen et al. (in press) cannot easily explain patterns
of dissociation in which one patient shows good orienting of
attention to signals (providing that attention is not previously
engaged on an object) but gross impairments in shifting attention
once engaged, whereas another patient shows the opposite
pattern of severity (see Humphreys & Riddoch 1993 for preliminary
data). We suggest that multiple mechanisms will ultimately
be needed.
Third, consider covert recognition in prosopagnosia. Recent
research suggests that there is no simple correspondence between
the severity of a recognition deficit and whether a patient
manifests covert recognition (McNeil & Warrington 1991), yet
this correspondence might be supposed if there were a direct
relation between partial damage and covert recognition, as in
the Farah et al. (1993) simulation. Again, inferences concerning
the validity of alternative accounts should be cautious until all
aspects of the relevant data set can be accommodated.
Our three cautionary remarks indicate only that moves towards
a complete understanding of both normal and disordered
cognition are fraught with difficulties for both interactive and
modular accounts. As applied to some disorders the locality
assumption has clearly been an oversimplification and may
cloud understanding of the underlying mechanisms, but applied
to others it may remain valid. What is surely right is that we
should look to convergence between approaches to provide
fuller understanding and that this understanding should include
both computational modelling and due attention to anatomical
constraints.
Do neuropsychologists think in terms of
interactive models?
Marcel Kinsbourne
Center for Cognitive Studies, Tufts University, Medford, MA 02155
Farah cites three of her published explanations of neuropsychological
dissociations to illustrate how productive it is to violate
what she calls the "locality assumption" and to promote parallel
distributed processing (PDP) simulations in clarifying the mechanisms
of such effects. All three are excellent ideas, but they do
not exemplify a new approach, and the locality assumption is not
a principled guideline for neuropsychology but more of a label
for unimaginative interpretation. I will discuss these points in
order.
1. Category specific semantic memory. Warrington suggested
that selective difficulties in naming animals or objects are
surface manifestations of differential damage to underlying
mechanisms that represent knowledge in sensory and functional
terms, respectively. Unfortunately, the patients who failed to
name animals could not do so through the functional route as
well as the visual, and this appeared to disconfirm the hypothesis.
Farah accomplishes an ingenious rescue by adding a postulate:
if, in a network, a representation is mostly activated
through one route and only slightly through another, the latter
would not in itself suffice to activate it. Animals are mostly
characterized visually, only somewhat functionally; so the naming
failure by both routes is explained.
This idea assumes that the lesion is confined to one of the two
relevant territories in such a patient. But brain damage does not
respect functional boundaries, and from the fact that categoryspecific
anomias are rare we infer that the hypothesized access
routes to naming must be close together. It is therefore more
than likely than an extensive lesion of one territory to some
extent overlaps the other. Assume that more functioning territory
is needed to activate a name representation through an
unusual than a usual route. This yields the situation in which the
subject cannot name animals through the functional route but
continues to be able to name objects through that route. No
doubt this outcome could easily be simulated.
2. Disengage deficit. Farah models Posner et al.'s (1984)
disengage deficit through mutually inhibitory interaction between
two sets of attentional units relative to the two target
locations in Posner's paradigm and derives a difficulty in disengagement
without needing to postulate a separate disengage
operation. Her model is an incomplete rendering of the wellknown
orientational bias model (Kinsbourne 1970; 1987), which
explains neglect symptomatology of the type studied by Posner
in terms of an imbalance between opponent processors subserving
lateral orientation in opposite directions. In a recent review
(Kinsbourne, in press), I listed many laboratories that have
tested this model in various ways over the years. None of us
neuropsychologists knew that we were infringing our alleged
locality assumption.
3. Unconscious priming of face Identity In prosopagnosia.
Farah presents a face-recognition network which, when injured,
yields various priming effects for known faces, but not their
names, simulating certain prosopagnosics. Assuming that naming
is a conscious act, this is an excellent application of the
general principle that for the contents of a representation to
enter consciousness, it need not be moved to some privileged
place (Kinsbourne 1988). The idea is that the depleted but
pretrained network retains biases in favor of previously experienced
patterns. This suggests the following prediction: there
will be no such dissociation between priming and naming for
face-name pairs repeatedly presented after the injury.
4. Modularity. Fodor (a philosopher, not a neuropsychologist)
only hypothesized impenetrable modules for a small minority of
the cognitive work of the brain. No one thinks that all specialized
areas of cortex are "impenetrable." Everyone admits
that the "modules" interact. The trick is not to overcome some
philosophic bias, but to determine how modules do it.
5. Locality assumption. Taking a surface dissociation and pinning
it on the brain is something I would call "neurologizing." It
is not a principled way of dealing with neuropsychological data
but a bad habit. At least since Hughlings Jackson in the late
nineteenth century, neuropsychologists have included interactive
mechanisms in their theorizing.
6. Is PDP modeling being oversold? Neuropsychologists derive
their good ideas from many sources and we learn that Farah
recently got some good ideas from principles of PDP modeling.
But in each of the cases cited, the idea does all the work. The
72 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Commentary/Farah: Neuropsychological inference
hypothesized mechanisms are so underconstrained that a simulation
could hardly fail.
Network theories of brain functioning have been around a
long time (e.g., Pribram 1971). The PDP method does promise
to be a nice way ofdemonstrating their usefulness, particularly if
the simulation predicts an effect quantitatively as well as qualitatively.
For that to be determined we need better constrained
theories than we have at this time.
Neuropsychology: Going loco?
Rosaleen A. McCarthy
Cognitive Neuropsychology Unit, Department of Experimental Psychology,
Cambridge University, Cambridge CB2 3EB, United Kingdom
Electronic mall: rm107@phx.cam.ac.uk
The locality assumption (LA), as presented in Farah's challenging
paper, consists of a cluster of thematically related ideas. As
articulated, the total set of LA postulates provides rather insecure
grounds for drawing neuroscientific inferences. However,
it is unlikely that any neuroscientist since the early phrenologists
can be blamed for subscribing to the entire LA set (or at
least at any one time). Certain aspects of the LA are, as the
author states, highly problematic; certain aspects are also ubiquitous
in cognitive neuropsychology, but the problematic and
the ubiquitous are not all ofa piece. I wish to suggest that LA can
be unpacked into a number of dissociable and distinct ideas:
some of these are clearly more tenable and plausible than
others.
A very basic notion of locality underpins the analysis of
cognitive function in separate domains such as spoken word
comprehension and face recognition. Independent though genetically
related models are widely assumed to be appropriate in
these cases (e.g., Bruce & Young 1986; Figs. 2 and 11 of the
target article). It is agreed that partitioning the problem space of
cognition into local sectors — whether on the basis of a priori
cognitive theory or even folk-psychological prejudice - is a
useful way of dividing labour. Nevertheless, independent
models do not necessarily imply independent signs and symptoms
in patients with neuropsychological deficit.
To take but one example, problems with face identification are
reasonably common in patients whose semantic knowledge of
animals is impaired. Of course, it would be possible to account
for both deficits and even their occasional dissociation within a
single network. (One might even venture to do so by having
more "visual" units associated with faces than animals in a model
such as Farah and McClelland's [1991]). However, cooccurrent
symptoms, whether for faces-plus-animals, or visual-plusfunctional
attributes of animals, are as likely to be based on
anatomical proximity of neural substrata as on cognitive relatedness.
Partitioning the problem-space into domains can direct
neurocognitive theorising in a way that avoids the traps of
argument from association (see e.g., Shallice 1988 for discussion).
This involves a degree of LA - but arguably to good effect.
At a finer and even less contentious level, LA represents a
variant of the cognitive information-processing tenet that complex
skills are made up of more specific elementary processing
components. The common ground between this level of the LA
framework and the position expressed in the target article is
illustrated by Farah's adoption of box-and-arrow conventions
(e.g., a separation is made between the domains of "vision" and
"semantics" in Fig. 2 and between "face input" and "semantics"
in Fig. 11). These models imply that word-picture matching and
face recognition are not performed by way of some undifferentiated
distributed net, but rather through the interplay of distinct
processing subdomains. If such componential informationprocessing
frameworks have any empirical psychological validity
then some set of independent variables must selectively
compromise their subcomponents. If these independent variables
happen to be based on pathology (rather than on cognitive
variables such as word frequency, semantic relatedness, or
visual degradation) then we are working with the weak form of
LA discussed by Shallice (1988) and McCarthy and Warrington
(1990).
In section 1.3, Farah points out that interactions between
neural subsystems may lead to higher-order effects and so
constrain inference about the organisation of cognitive function.
This concern, which is closely related to the issue of subtraction
(i.e., that the damaged system may be viewed as the normal
system, functioning normally, minus one or more components)
is critically dependent on theoretically informed empirical research.
The validity of the methodological paradigm of subtractivity
is an empirical problem for an experimental science. It
seems no more soluble by referring to parallel distributed
processing (PDP) models in the 1990s than it was by referring to
valve radios in the 1960s (Gregory 1961; Weiskrantz 1968).
Subtraction and its corollary, statistical independence, are not
assumptions: they are empirical hypotheses. There is ample
converging empirical evidence (behavioural, radiological, and
neuropsychological) that attests to the utility of the subtractive
hypothesis when applied to areas as diverse as object recognition,
face recognition, language, reading, writing, arithmetic,
and memory (e.g., Ellis & Young 1988; McCarthy & Warrington
1990). Of course, it may be inadequate for other domains, but
that is an empirical issue.
What can be problematic is any assumption that brain injury
invariably causes an uncomplicated (lower order) correspondence
between neurological and cognitive levels of organisation
(see sect. 1.2). This is the problem of inferring function from
deficit: this trap can be seductive but is conceptually quite
distinct from using subtraction as a methodological paradigm or
empirical framework. The subtractive methodology is related to
the use of factorial experimental designs and informationprocessing
models. Inferences from deficit are a set of more-orless
naive conclusions based on data.
LA is accused of holding that there are direct transparent
relationships between neural systems, neurological symptoms,
and functional architecture (sects. 1.1 and 1.2). It is this aspect of
the LA hypothesis that is the least defensible. However, this
aspect appears to be one that the target article (albeit in its more
optimistic moments) finds reasonably congenial. The sensoryfunctional
hypothesis of semantic deficits is "more in keeping
with what we already know about brain organization" than is a
theory based on semantic or taxonomic variables (e.g., Caramazza
et al. 1990). This may be the case, but it may also be
irrelevant: the theories are cast at different levels and one may
be explicable in terms of the other. Similarly, the fact that the
brain is a complex biological system that shows nonlocal effects
when injured (sect. 3.3.3) does not necessarily entail that
cognitive theories must mirror this interactivity. (For example,
in the case of blood flow, hyperperfusion in the region of an
infarct does not mean that the damaged areas of brain are
contributing more to the cognitive performance of the system.)
Locality at the cognitive level need entail organology at the
neural level (even with encapsulated input modules; Fodor
1983).
What about the target article's case for nonlocal cognitive
effects arising from local damage? The inference that a particular
conjunction of deficits is an inevitable consequence of the
interaction between processing components is open to direct
empirical evaluation. At this "micro" level there are already a
few challenges to the interactive position. For example, Hart
and Gordon's (1992) documentation of the selective loss of
knowledge of the visual attributes of animals appears to challenge
the Farah and McClelland (1992) model of semantic
memory; word-finding difficulties may be unaffected by visual
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 73
Commentary/Farah: Neuropsychological inference
complexity (e.g., Hatfield et al. 1977), contrary to Tippett and
Farah (1992); and Patterson et al. s (1989) model ofphonological
reading fails to account for the preservation of nonword reading
in surface dyslexia (McCarthy & Warrington 1986). These counterexamples
are far from being exhaustive. However, even a
comprehensive list would not undermine the enterprise of
computational or PDP modeling - any more than a failure to
demonstrate local effects would invalidate the use of labeled
graphs (a.k.a. boxes and arrows). Models can be wrong and that
is why we use them. Their power lies in their empirical vulnerability
and the extent to which hypotheses, such as those
aired in the target article, can be disengaged from speculative or
metaphysical assumptions.
If the target article were correct (in its more pessimistic
moments), the task of bootstrapping cognitive theory from
neuropsychology would be a pretty tall order. Everything interacts,
so the chances offindingany systematic patterns would be
limited. What is remarkable, therefore, is the degree of consistency
and coherence of the overall enterprise of cognitive
neuropsychology/neuroscience. Very substantial achievements
have been made over a short time. We have a theoretical
understanding of the profiles of breakdown in cerebral injury
that correspond to analyses of normal cognitive performance.
Furthermore, approximately similar deficits are associated with
damage to the same regions ofthe brain and arise in populations
with differing languages, cultures, and learning histories. More
recently, neural structure and cognitive function in the intact
brain have been brought into register through PET scanning
techniques - and the findings seem to correspond with what we
have, learned from studies of brain-injured subjects. Finally, in
some cases remediation can even be guided by the frameworks
of cognitive theory. This brief summary of achievements does
not look like the curriculum vitae ofa doomed or fundamentally
misconceived enterprise; fortunately, it seems more like the
prospectus for an exciting and energetic science.
Distributed locality and large-scale
neurocognitive networks
M.-Marsel Mesulam
Department of Neurology, Beth Israel Hospital, Harvard Medical School,
Boston, MA 02215
The field ofcognitive neuroscience is supposed to be engaged in
an epic struggle between the forces of Iocalizationism (or centrism)
and those of equipotentiality (or holism). Farahs target
article addresses this struggle. According to Farah, there is a
"locality assumption" in cognitive neuropsychology which implies
that damage to one component ofa functional architecture
leaves the other components intact. "In such an architecture,
each component minds its own business and knows nothing
about most of the other components. What follows for a damaged
system is that most of the components will be oblivious to
the loss of any one, carrying on precisely as before." Farah
argues that such a locality assumption is untenable. I agree. In
this commentary, I summarize some observations related to the
neurology of hemispatial neglect in order to outline an alternative
view of functional localization.
Centrist views of functional localization postulate the existence
ofa nearly one-to-one relationship between lesion site and
behavioral deficit. Clinical observations, however, show that a
specific deficit such as hemispatial inattention (neglect) can arise
following damage to a number ofdifferent cortical and subcortical
regions of the brain. Cortical lesions that consistently yield
hemispatial neglect, for example, have been encountered not
only in the posterior parietal cortex, but also in premotorprefrontal
cortex and the cingulate gyrus. Neuroanatomical
experiments show that the core cytoarchitectonic entities of
these three regions (area PG, frontal eyefields[FEF], and areas
23-24 of the cingulate gyrus) are linked to each other by
extensive and reciprocal monosynaptic connections. The additional
subcortical areas where lesions are known to cause neglect
(the superior colliculus, striatum, and the thalamic pulvinar
nucleus) are connected to at least two ofthese three cortical foci.
These considerations have led to the suggestion that spatial
attention is subserved by a distributed large-scale network with
three cortical components (or local networks), each providing a
slightly different coordinate system for mapping the environment
(Mesulam 1981).
Experimental observations suggest that the FEF and area PG
may have a collective mechanism for specifying whether a
location in space (and events within it) will become the target of
enhanced neuronal effects, visual grasp, manipulation, or exploration.
In the most figurative and anthropomorphic sense, it
could be said that area PG sculpts the subjective attentional
landscape, while the FEF and surrounding areas plan the
strategy for navigating it. The role of the cingulate gyrus is the
least understood aspect of this network. The pattern of neural
connections suggests that PG and FEF receive information
about the motivational (or Iimbic) relevance of sensory stimuli
mostly through inputs from the cingulate region. The cingulate
component could thus introduce a value system into the perceptuomotor
mapping of the extrapersonal space.
Implicit in the preceding account is a dichotomy between the
sensory and motor components of directed attention, coordinated
respectively by PG and FEF. These two areas are so
tightly interconnected, however, that such dichotomies between
action and perception become blurred. Although the
affiliations of area PG are mostly sensory and those of FEF
mostly motor, area PG also contains neurons thatfirein association
with saccades and reaching movements, and the FEF
region contains neurons with well-defined receptive fields
(Goldberg & Segraves 1987; Lynch et al. 1977). From a behavioral
point of view, a sensory representation is necessary for the
accurate guidance of exploratory movements just as exploratory
movements are necessary for realigning sensory receptors and
updating perceptual representations.
Although clinical observations show that motor and sensory
components of unilateral neglect are differentially affected after
frontal or parietal lesions, respectively, the dichotomy is not
absolute (Daffner et al. 1990). What we see is not the isolated
disruption of one or the other behavioral component but the
relative salience of one over the other depending on the site of
the lesion. The presence of tight interconnectivity between
FEF and PG also leads to the expectation that damage to one of
these two sites should induce physiological dysfunction in the
other, an expectation that has recently been confirmed (Fiorelli
et al. 1991). This phenomenon of"diaschisis," known to neurology
for more than 50 years, provides one of the many good
reasons for dismissing the locality assumption.
Each of the three cortical components in the attentional
network serves a dual purpose; that is, it provides a local
network for regional neural computations and a nodal point for
the convergence and reentrant accessing ofdistributed information.
All three core components are probably engaged simultaneously
and interactively by attentional tasks and it is unlikely
that there is a temporal or processing-level hierarchy among
them. The resultant phenomenon of directed attention is not
the sequential sum of perception plus motivation plus exploration
but an emergent (i.e., relational) quality ofthe network as a
whole.
A central feature of networks is the absence of a one-to-one
correspondence between anatomical site, neural computation,
and complex behavior. This is shown in Figure 1. Let behavior
alpha correspond to directed spatial attention. Its three major
neural computations, Al, A2, and A3, are distributed in sites I,
II, and III, which correspond to the FEF, area PG, and the
cingulate gyrus. Most but not all ofcomputation Al is performed
74 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Commentary/Farah: Neuropsychological inference
Figure 1 (Mesulam). Schematic illustration of the interrelationship
between behavioral and anatomical components (from
Mesulam 1990).
in site I (e.g., the encoding of exploratory movements is done
mostly in the FEF but to a lesser extent also in area PG). Each
site belongs to several intersecting networks (Mesulam 1990).
For example, function C is distributed in an intersecting network
that includes site II. The behavioral (or cognitive) components
of alpha are designated as al, a2, and a3 and may
correspond to exploratory behavior, perceptual representation,
and motivational mapping, respectively. The peak of a l is
approximately over site I, but there is also a skirt that extends
into the other two sites. The resulting topological plane (with
peaks al, a2, and a3) corresponds to the clinically observed
behavior. Recent anatomical observations indicate that the interconnections
among the relevant anatomical sites of a largescale
network are organized in a manner that can sustain parallel
distributed processing (Morecraft et al. 1993). These interconnections
and the process of diaschisis indicate that a perturbation
in one anatomical component will tend to be propagated
(along a spatiotemporal gradient) to the other components of a
network. The vertical organization of the anatomical, computational,
and cognitive planes is depicted in Figure 2. It is
important to point out that Farah"s "modules" reside mostly
within planes 2 and 3 whereas my "network components" are
located predominantly at the anatomical plane.
Figures 1 and 2 suggest that the anatomical mapping of
behavior is both localized and distributed but neither equipotential
(holistic) nor modular (insular or phrenological). According
to Figures 1 and 2, each site in association cortex belongs to
several intersecting networks so that an individual lesion, even
when confined to a single cytoarchitectonic field, is likely to
yield deficits in multiple domains. Posterior parietal lesions, for
example, cause deficits in complex visuospatial processing in
addition to unilateral neglect. Conversely, some lesions (or
electrical stimulations) may remain behaviorally silent under
certain conditions because alternative parallel channels may
become available. The model in Figures 1 and 2 helps to explain
how anatomical localization is compatible with the fact that
lesions in different parts of the brain can yield perturbations of
the same overall behavioral domain, why single lesions lead to
only partial deficits of a given behavior or to multiple behavioral
deficits, and why functional mapping studies are likely to detect
multiple areas of activation even when the subject is engaged in
a single task. For the more practical purposes of neuropsychological
assessment, this model predicts that no neuropsychological
task (or neurocognitive paradigm) can ever be entirely
specific for a single region of association cortex and that the
clinician need not look for multiple lesions just because the
patient shows more than one cognitive deficit.
This model does not deny the existence of local specializations
in the brain but it implies that individual behaviors are represented
in multiple sites and that each site subserves multiple
behaviors, leading to a distributed and interactive but also
coarse and degenerate (one-to-many and many-to-one) mapping
of anatomical substrate onto neural computation and computation
onto behavior. This distributed mapping may provide an
advantage for the rapid computation ofcomplex cognitive operations
and sets the network approach sharply apart from theories
PLANE3:
BEHAVIORAL
COMPONENTS
PLANE2:
NEURAL
COMPUTATIONS
PLANE /•
NEUROANATOMICAL
SITES
Cognition and
Comportment
Parallel
Distributed
Processing
Interconnected
Networks
Figure 2 (Mesulam). Schematic illustration of interrelationships among anatomical, computational, and behavioral planes (from
Mesulam 1990).
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 75
Commentary/Farah: Neuropsychological inference
that postulate a one-to-one relationship between behavior and
anatomical site. The neural connectivity among network components,
the intersection of networks, and the physiological process
of diaschisis clearly show that the version of the locality
assumption described in the target article is not compatible with
what we know about the organization of the real brain.
ACKNOWLEDGMENTS
I want to thank Leah Christie for expert secretarial assistance. This work
was supported in part by grant NS30863 from the NIH.
Computational levels again
Mike Oaksford
Cognitive Neurocomputation Unit, University of Wales at Bangor, Gwynedd
LL57 2DG, United Kingdom
Electronic mail: pss027@bangor.ac.uk or mike@cogsci.ed.ac.uk
My purpose in this commentary is to argue that Farah's critique
of the locality assumption unnecessarily represents "box-andarrow"
accounts of cognitive processes as being in conflict with
recent connectionist models of neuropsychological phenomena.
I argue that behind this putative dispute is a conflation of levels
of analysis of complex computational systems such as the human
brain. Although accounts of such levels are contentious, I will
stick with Marr's tripartite division as the best known, most
influential, and most clearly stated. Briefly, what functions need
to be computed in the performance of some task are specified at
the computational level; how those functions are to be computed
is described at the algorithmic level (this level also includes the
specification of the representations over which the algorithms
are defined); and how the algorithms are physically realised is
outlined at the implementational level. As emphasised by Marr
(1982, and, e.g., Chater & Oaksford 1990; Oaksford & Chater
1991; Rumelhart & McClelland 1985), but pace, for example,
Fodor and Pylyshyn (1988), these levels are not autonomous, but
constrain each other so that a complete psychological explanation
of any task performance must invoke all three levels of
analysis. I will now attempt to argue that the dispute Farah tries
to resolve in favour ofconnectionist systems need not arise and is
based on a failure to appreciate the importance ofall three levels
to psychological explanation. To do so I concentrate on the first
model she discusses, which accounts for the dissociation between
the knowledge of living and nonliving things.
Farah shows how a parallel distributed processing (PDP)
model with separate modules for visual and functional semantics
may account for the living/nonliving dissociation and for the fact
that patients with a visual knowledge deficit for living things also
show a deficit in functional knowledge of living things. In
accounting for the latter observation the network is only Iesioned
in the visual semantics module, demonstrating that a
single lesion in one part of the model may lead to suppressed
performance in another undamaged part. This is important,
because, in direct contradiction of locality, it demonstrates that
"the remaining unimpaired processes will work differently
when one component is not functioning normally."
This argument does not refute locality, however, if locality is
defined at the computational level and not at the implementational
level. According to locality, the observed behaviour involves
a normal model that is subject to the effects of the lesion.
Lesion effects are mapped out at the computational level by the
pattern of dissociations a patient reveals. So if a patient is
impaired on a task that requires function A but not on tasks
requiring functions B and C it can be assumed that the lesion has
affected A but not B or C, in which case a cross can be placed on
the box representing function A. The evidence hence implies
that a cross should be drawn through the visual semantics box.
To account for the deficit in functional knowledge of living
things, it must be assumed that functional semantics fractionates
into knowledge of living and nonliving things. Hence a
cross is drawn through the sub-box in functional semantics for
living things. This seems to be the local account to which Farah
objects.
And indeed it does seem unparsimonious. If nothing else, it
reestablishes appeal to the specific living/nonliving distinction
that the more general visual/functional distinction was intended
to avoid. However, it does appropriately summarise the patients'
pattern of deficit at the computational level. And, of
course, the computational level does not specify how a function
is to be implemented. (Note that because a task is decomposed
as requiring two functions to be computed, this does not mean
that, ipso facto, two anatomically distinct causal mechanisms are
required for their computation.) In particular, the local computational
level description provided above is consistent with
Farah's nonlocal implementation. This is because all the local
computational level model states is that functional knowledge of
living things is impaired but functional knowledge of nonliving
things is not, which is consistent with the observed pattern of
task performance.
Some confusion may arise because crosses would be placed on
both the visual semantics module and the functional knowledge
of living things submodule. All that this indicates, however, is
that these functions are impaired, not that the physical mechanisms
upon which these functions supervene have sustained
physical damage as a result of the lesion. The confusion is
compounded by the problem that although locality is best
treated at the computational level, Farah uses it at the implementational
level, adducing evidence from "the highly interactive
nature of brain organization" to refute it. Thus it seems that
two notions of locality are being discussed: computational locality
and implementational locality. The problem is that nonlocal
PDP implementations are consistent with the retention of
computational locality. Computational locality allows neuropsychological
evidence to bear on the functional decomposition of
the tasks that have been examined with normals. It is intended
to rule out the possibility that damage results in a wholly new
functional organisation - a possibility that would indeed invalidate
any inferences from neuropsychological data to normal,
computational level models.
In addition, Farah's models are themselves local at the computational
level. She argues that lesions to the visual semantics
module alter the function of the functional semantics module.
Qua computational level description that seems to be simply
false. Whereas the inputs to the module have changed, the
actual function it computes remains the same. To establish that
the function the module computes has changed would require
some attempt to define the functional equivalence of two systems.
An obvious first stab is that two systems compute the same
function if and only if, given the same inputs, they produce the
same outputs (at least this is adequate at the computational level
where it is only the functions in extension that need to be
specified - algorithmic equivalence is an altogether more complex
issue (see, e.g., Foster 1992). For Farah to establish that the
functional semantics module computes a different function she
would have to show that it produces different outputs after the
lesion to the visual semantics module than it did before the
lesion to the visual semantics module, given the same inputs.
Since the lesion to the visual semantics module simply alters the
range of inputs to the functional semantics module, it must
compute the same function before and after the lesion. In sum,
functionally, that is, at the computational level, Farah's models
are local, although at the implementational level they are
distributed and interactive. In this respect it is important to note
that the term "locality" invites confusion because of the association
with local versus distributed representation. However, this
representational point is not at issue here. Farah's models are
not "nonlocal," in her sense of the term, simply by virtue of
using distributed representations.
In conclusion, if classical "box-and-arrow" diagrams and PDP
76 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Commentary/Farah: Neuropsychological inference
models are viewed as descriptive of the same processes but at
different levels of analysis of a complex system, the dispute
Farah identifies dissolves. This is not to say that such an account
would meet with universal acceptance. There is a great temptation
to reify box-and-arrow diagrams as claims about actual
causal structure. However, carefully distinguishing between
these levels ofanalysis and recognising the necessity ofeach may
prevent another protracted and ultimately futile internal squabble.
Complete psychological explanations of cognitive phenomena
require explanations at each of Marr's three levels (Chater &
Oaksford 1990; Rumelhart & McClelland 1985). Hence, local
box-and-arrow computational level descriptions need not be
viewed as theoretical competitors to PDP implementations.
Parallel distributed processing challenges
the strong modularity hypothesis, not the
locality assumption
David C. Plaut
Department of Psychology, Carnegie Mellon University, Pittsburgh, PA
15213-3890
Electronic mall: plaut@cmu.edu
Farah presents convincing arguments that principles of parallel
distributed processing (PDP) provide more parsimonious explanations
of a number of neuropsychological phenomena than do
traditional modular accounts. She ascribes this to the fact that
PDP systems violate the "locality assumption" in that damage in
an interactive network can have nonlocal effects. On closer
inspection, however, Farah has misinterpreted the locality assumption
as it has been formulated in the literature. Furthermore,
Farah"s version of the locality assumption is violated by
modular systems as well, and thus does not provide a useful basis
for distinguishing PDP and traditional accounts. Rather, this
contrast is better understood at a more general level, in terms of
a rejection of the strong modularity hypothesis (e.g., Fodor
1983). In particular, the most fundamental contribution of PDP
modeling to neuropsychology is that it allows a principled
expression of nonmodular, interactive computation in which the
analysis of the effects of damage is tractable.
According to the strong modularity hypothesis, the cognitive
system is composed of informationally encapsulated components
that receive input from only a few other components and
produce all-or-none output in discrete stages. Informational
encapsulation entails that the knowledge required for a process
is available only to the component dedicated to that process and
that any partial results of the process are unavailable to other
components. Each of the central properties of PDP systems that
Farah lists (sect. 1.4, para. 2) contrasts in a specific way with
these properties of modular systems: (1) the knowledge involved
in a process is distributed in connection weights throughout the
network rather than being localized to a particular component;
(2) processing is graded and continuous rather than being staged
and all-or-none, making partial results in one part of the network
continually available to other parts; and (3) groups of units representing
different types of information are highly interactive,
instead of receiving inputs from only a few other components.
Furthermore, while the strong modularity hypothesis says little
about the nature of processing within each component, PDP
systems use a common set of computational principles both
within and between groups of units: processing takes the form of
graded interactions among distributed patterns of activity.
In arguing that PDP systems provide better accounts of
neuropsychological data than modular systems, Farah focuses
on what she calls the "locality assumption," which she interprets
as implying that the effects of damage are local; that "nondamaged
components will continue to function normally" (sect.
1.1, para. 1). This statement can be interpreted in two ways: (1)
nondamaged components behave normally, in that their output
to other components is unchanged, or (2) nondamaged components
compute normally, in that their input/output function is
unchanged. Farah clearly has interpretation (1) in mind. The
central claim of Farah's target article is that the advantage of
PDP accounts steins specifically from the occurrence of nonlocal
effects of damage within these systems, in violation of the
locality assumption. Yet clearly the nondamaged portions of the
networks compute normally but behave abnormally in response
to corrupted input from damaged portions.
The same is true, however, of nondamaged components
which receive input, either directly or indirectly, from a damaged
component in a modular system. For example, in de Haan
et al.'s (1992) model of face processing (see Fig. 10, sect. 2.3.2,
para. 1), no one would claim that the "response effector systems"
would continue to function normally if, say, "structural encoding"
were impaired. In fact, Farah acknowledges this point,
stating that the effects ofdamage in such a system are confined to
"lesioned components and the relatively small number of components
downstream" (sect. 1.3, para. 1, emphasis added). That
damage alters the behavior of intact components downstream
clearly violates Farah's interpretation of the locality assumption.
But note that the claim that there are relatively few such
components does not come from the locality assumption per se
but from more general assumptions about modular systems:
processing tends to be feedforward (staged) and each component
receives few inputs. In this regard, PDP systems differ
from modular ones only in a quantitative way: portions of a PDP
network typically receive a wider range of input than do components
in a modular architecture. In both frameworks, however,
nondamaged processes will be affected by corrupted input from
damaged processes, and thus PDP and modular systems are on
equal footing with respect to Farah's interpretation of the
locality assumption.
In fact, in the neuropsychological literature, what corresponds
most closely to Farah's interpretation of the locality
assumption (1 above) is Caramazza's (1986) "transparency assumption,"
according to which it must be possible to relate the
effects of damage on the behavior of the cognitive system to its
normal operation in a principled way. This relationship had to be
"transparent" in earlier formulations (Caramazza 1986), but
merely "tractable within the proposed theoretical frameworks"
in later ones (Caramazza 1992, p. 82). The locality assumption
was originally formulated in the context of the transparency
assumption, where it corresponds most closely to interpretation
(2) above - that the damage itself must be local.
My formulation of the transparency assumption implies that [neuropsycliological
evidence] £, can only be related to [a cognitive model]
M when the damage to the system is "local." This assumption may be
too strong as an in principle claim - nonlocal, very general modifications
of the system may still allow the possibility of relating E, to M.
However, in practice, given the tremendous complexity of the systems
we are dealing with, it may only be possible to draw meaningful
conclusions from impaired performance to normal cognitive systems
under a restricted sort ofcondition. (Caramazza 1986, p. 52, emphasis
in the original)
Thus, the standard locality assumption is simply a way to ensure
that the transparency assumption is tractable, and the transparency
assumption is simply a way to ensure that the effects of
damage are interpretable. In this light, PDP modeling in
neuropsychology is important, not because it is "not constrained
by the locality assumption" (sect. 1.3, para. 5) as Farah contends,
but rather because it provides a rich, nonmodular theoretical
framework in which it is nonetheless possible to relate
normal and impaired behavior in a principled way.
Critically, all the advantages of Farah's PDP accounts can be
most naturally understood as arising from ways in which the
nature of computation in these systems violates various aspects
of the strong modularity hypothesis. In the simulation of both
semantic memory impairments (Farah & McClelland 1991) and
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 77
Coimnentaryi'Farah: Neuropsychological inference
impaired attentional allocation (Cohen et al., in press), the
ability of the networks to account for the data arises out of graded
cooperative and competitive interactions among portions of a
network that are not meaningfully interpretable as informationally
encapsulated components. Furthermore, Farah acknowledges
that the success of the simulation of impaired face
processing (Farah et al. 1993) stems less clearly from violating
her interpretation of the locality assumption. On the other
hand, the fact that residual knowledge after partial damage can
support performance on implicit tasks stems directly from
violating a central aspect of the strong modularity hypothesis:
knowledge is not encapsulated in separate components but
distributed throughout the network (see Hinton & Shallice
1991; Plaut & Shallice 1993; in press, for similar results).
Viewing PDP systems as challenging the strong modularity
hypothesis rather than Farah s locality assumption also provides
a better understanding of the finer-grained analyses she mentions.
In Hinton and Shallice's (1991) simulation of deep dyslexia,
visual and semantic errors cooccur because the knowledge
of how visual representations relate to semantic representations
is distributed throughout the network rather than being confined
to a "visual" component and a "semantic" component,
respectively (see Plaut & Shallice, in press, for further results
and discussion). In Patterson et al. s (1989) simulation of surface
dyslexia, poor performance on low-frequency exception words
and the occurrence of regularization errors occur because the
knowledge of all spelling-sound correspondences is embedded
in the same set of weights rather than being split into "lexical"
and "nonlexical" components, and the robustness of a given
correspondence in the face of damage depends on its frequency
of occurrence (but see Behrmann & Bub 1992 for criticism of the
adequacy of the account). In Mozer and Behrmann's (1990)
simulation of neglect dyslexia, the lexicality effects after visual
damage arise simply from the fact that lexical knowledge can
reconstruct corrupted word input but not corrupted nonword
input. The only sense in which damage has nonlocal effects in
any of these simulations is the same one that applies to modular
systems: intact components downstream from a lesion are affected
by corruption of their input.
In summary, I strongly agree with Farah that PDP principles
provide a way of characterizing cognitive processes that is
fundamentally different from more traditional, modular frameworks,
and that systems which embody these principles can
generate more satisfactory accounts of a wide range of psychological
and neuropsychological phenomena. However, I disagree
with her about the specific aspects of PDP systems which
distinguish them from modular systems. Both PDP and modular
systems exhibit nonlocal effects of damage and thus violate
Farah's interpretation of the locality assumption. However, the
distributed, interactive, graded processing in PDP systems
contrasts sharply with the encapsulated, staged, all-or-none
processing in systems adhering to the strong modularity hypothesis.
It is exactly these distinctions, and not a violation of Farah's
locality assumption, that are fundamental to the strengths of the
PDP approach in cognitive neuropsychology.
ACKNOWLEDGMENTS
I would like to thank Marlene Behrmann, Jay McClelland, and Tim
Shallice for helpful comments on an earlier draft of this commentary.
Local and distributed processes in
attentional orienting
Michael I. Posner
Psychology Department, University of Oregon, Eugene, OR 97403
Electronic mail: mposner@oregon.uoregon.edu
Farah argues that lesion data have usually been interpreted
according to two principles of localization: (1) the effects of the
brain damage are local and (2) and nondamaged parts of the
system operate normally. To show how studies of brain injury
and neuroimaging combine to provide a different form of understanding
of localization, I would like to consider the finding that
parietal damage affects attention to visual locations.
Farah's target article provides an alternative explanation for
my suggestion that the ability to disengage attention is damaged
by a lesion of the parietal lobe (Posner 1988). When we first
made this suggestion it was not at all clear that there would be a
local mechanism related to the task Farah describes. Although
lesions of the parietal lobe did influence the ability to disengage,
it was certainly possible, even likely, that this was due to a
nonlocal mechanism. Indeed, reaction time data from patients
with lesions of the parietal lobe, thalamus, and midbrain showed
that each of these lesions had some influence on the task,
although they did not appear to involve the "disengage" operation
(Posner 1988). Our description from the start was in terms of
an interactive network in which parietal mechanisms were in
close coordination with thalamic and midbrain areas.
Recently the idea of localized mechanisms in the parietal lobe
has been supported by PET (positron emission tomography)
studies using variants of the model task first used for patients
(Corbetta et al. 1993). It seems clear that when normal subjects
shift attention from one location to another, whether to report
targets or merely because they are free to process transient
information, there are strong increases in blood flow within a
restricted area of the superior parietal lobe. For left visual
attention shifts only the right parietal lobe is active whereas for
right visual field attention shifts both left and right hemispheres
are active. This is strong evidence for a very local effect in
normal subjects. Perhaps this could be the "attention" box in the
Farah architecture. Yet this brain area was not active during
many other tasks that involved attention to color, form, motion,
or location but did not require a shift of attention from one
position to another. The PET data suggest that the parietal lobe
is crucial when subjects disengage from one location to move to
another. They do not separate the disengage operation from the
move operation, although Robinson et al. (1991) has recorded
from parietal cells that seemed to support an attentional operation
related to disengagement from a receptive field location.
Does this mechanism require connections from a location in
the opposite visual field, as suggested by the connectionist
model Farah presents? It is noteworthy that Luck et al. (1989)
have shown that when the corpus collosum is severed, the
search for a conjunction target occurs within each visual field.
There is reason to believe that conjunction search involves
covert shifts ofattention between locations, so this result implies
that the mechanisms of shifting attention do not depend on
connections across the midline, as implied by the Farah model.
However, the unified visual-orienting system of the normal
subject is split by the lesion. Our initial experiments involved
two horizontal locations, one in each field, but we were able to
show that parietal damage affects all locations in both visual
fields on those occasions when the target is in a contralesional
direction relative to the current focus of attention. If each
position in a visual field can serve as a cued location, Farah s
model would have to involve not a few connections but many
hundreds of them. Would it scale up to "handle" this problem,
and if so, would it provide any fresh insight? These are the kinds
of questions to ask in determining whether one would prefer a
connectionist model to evidence for a local mechanism coming
from a convergence of research between imaging and brain
damage studies.
A further factor shows the great advantage of connectionist
networks. Even if there is a local occurrence of a disengage
operation, it is important to understand the communication
between that operation and directly related ones. A disengage
function would not be useful unless it could influence information
accumulating at quite distant sites about the exact form of
the stimulus to which attention is switched. According to La-
78 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Commentary/Farah: Neuropsychological inference
Berge (1990), this involves connections from the parietal system
to the inferior temporal cortex via the pulvinar nucleus of the
thalamus. The expectations that lead to attention to a location
operate in a distributed network. It appears, however, that the
connections are between areas performing identifiable subroutines
or operations. We must understand both the local
computations and their coordination in real time to understand
the network functions. Noninvasive electrical and magnetic
recording, if coordinated with PET or other spatial methodologies,
allow us to study the temporal order of anatomically
limited computations (Posner & Rothbart, in press).
To understand brain injury we must understand that the
reduction of an operation at one part of the network can have
important consequences for other parts of that network. For this
reason no extreme form of modularity that postulates encapsulated
vertical networks passively activated by input will do. If we
only had data from brain damage and no way to image the
normal brain we would have great difficulty in determining what
was the effect on the local computation and what was the remote
effect of the damage. A combined approach to normal and
pathological functions instead relies on anatomical and circuit
tracing methods to supplement patient studies.
Perception and its interactive substrate:
Psychophysical linking hypotheses and
psychophysical methods
Robert Sekuler
Department of Psychology, Brandeis University, Waltham, MA 00254;
Department of Biomedical Engineering, Boston University, Boston, MA
02215
Electronic mall: sekuler@binah.cc.brandeis.edu
Farah s architectural criticism put me in mind of John Donne's
sermon more than three and a half centuries ago: "No man is an
island, entire of itself; every man is a piece of the continent, a
part of the main; if a clod be washed away by the sea, Europe is
the less, as well as if a promontory were. . . . " With a little
imagination one could construe Donne as preendorsing Farah's
cautionary message about a highly interconnected and interactive
brain.
Farah began by arguing that no part of the brain is an island,
entire of itself. Worried that this fact might spell the demise of
neuropsychology, Farah saved the day (and perhaps the field) by
showing that the inconvenient complexities of anatomy and
physiology can be dealt with in a principled and enlightening
manner. It is certain that neuropsychologists will weather these
inconveniences. But what about other researchers? For example,
what about the various species of psychologists who study
normal rather than brain-damaged subjects? Should they assume
that the problem is someone else's and thus disregard
Farah's paper? The answer is "most certainly not." In my view,
Farah s thesis is crucial to much of contemporary psychology.
To one degree or other, many of psychology's subdomains are
concerned with possible connections between psychological
phenomena and the body. For some subdomains, including
perception, theorizing about mind-body connections occupies
the intellectual foreground; arguably, it's where the action is
now. For other subdomains, including personality, the real
impact of such theorizing waits for a moment in the future; even
then, of course, it may never be front and center.
Though the timetables may differ, sooner or later researchers
in most areas of psychology will have to confront the interactive
brain. This confrontation will be difficult. After all, psychology
now assumes a brain that is barely recognizable as the interactive
one Farah urges us to embrace. If Farah's admonitions hold
for fields outside neuropsychology, and I think they do, much of
psychology plainly needs straightening out. To see what I mean,
consider some implications for the study of perception by
normal, nonimpaired observers.
Perceptionists take great pride in propositions that link perceptual
and physiological states. These propositions have played
a central role in guiding the field's development. In the modern
era, psychophysical linking propositions can be traced back one
hundred years to G. E. Miiller. Later, these propositions were
operationalized by Boring (1942) and systematized by Teller
(1984). Although one can imagine linking propositions that
recognize the force of Farah's argument, all linking propositions
currently in use reflect two assumptions: first, that traffic in the
nervous system is one-way, and second, that it is possible to
make a causal link between a perceptual state and activity at one
neural locus, or at most a few neural loci. If these assumptions
were examined and abandoned, the resulting linking propositions
would be dramatically different from those currently in
use.
Much of perception ignores the massive evidence for rampant
parallel and reentrant pathways that characterize every mammalian
sensory system. For example, even the briefest glance at
an up-to-date wiring diagram of the mammalian visual system
(Felleman & van Essen 1991) is enough to convey the complexities
inherent in the hundreds of interconnections that link the
system's many sites. To date, though, there have been few
systematic attempts to prospect for the perceptual interdependencies
entailed by the reinforcing webs and overlapping tangles
of the wiring diagram. The reasons for this theoretical
immaturity are undoubtedly heterogeneous, but they may well
include the undeniable fact that the simple view of the brain
makes for a better story, a narrative that is easier to express and
certainly easier to comprehend (Kelley 1992).
If backward notions about psychophysical links have retarded
perception's advance, psychophysical methodology also deserves
some of the blame. Here I have two particular issues in
mind. One likely consequence of the mind's normal functional
architecture is that any stimulus, no matter how simple, brief, or
impoverished, generates a number of distinctly different effects
in the nervous system. These multiple effects develop at different
rates, yield different end products and, as a result of the
system!s wiring, may also be differentially susceptible to influence
by the observer's expectations, by training, and by other
nonsensory variables.
In her discussion of prosopagnosia, Farah showed that seriously
impaired face recognition can coexist in the same person
with near-normal face recognition. Which side of the coin one
sees depends upon whether face recognition is assayed via
explicit or implicit measures (sect. 2.3). In most fields of
psychology, an array of diverse measures is essential to capture
the gamut of diverse effects that are initiated by any single
stimulus.
But psychophysics, visual, auditory, or otherwise, is particularly
handicapped in this regard. Standard psychophysical
methods are designed to quantify conscious experience - that's
what Fechner was aiming for. All the classical methods depend
upon the observer's conscious experience and equally conscious
decision. Some techniques can open a window onto nonconscious
perceptual processing (Kunst-Wilson & Zajonc 1980;
Mandler et al. 1987), but for most students of perception these
results are off the intellectual radar screen, out in the field's
periphery. Although these studies are intriguing, their outcomes
are treated as exceptions or oddities rather than as signs
of influences that are probably ubiquitous, though hard to
measure. To paraphrase John Donne (slightly incorrectly), it
seems to me that psychologists, including perceptionists,
should not have to ask for whom Farah's theoretical bell tolls: it
tolls for all of us.
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 79
Commentary/Farah: Neuropsychological inference
Locus-pocus (which and whose locality
assumption?)
Carlo Semenza
Dipartimento di Psicologia Generate, Universita di Padova, 35139 Padua,
Italy
Electronic mail: psico28@ipdunivx.unipd.it
It may be an easy prediction that a direct comparison between
modular and connectionist accounts of neuropsychological dissociations
will become commonplace in forthcoming years.
Farah's opening of a forum on this subject is therefore welcome
and of major interest. Her target article, however, would have
been more effective, and, probably, the position she takes more
appealing, if not centered on a critique of what she calls the
"locality assumption." The way this matter is presented misleads
the reader throughout Farah's discussion because, at present,
nobody would subscribe to the locality assumption as Farah
seems to intend it. Thus, although she can readily criticize the
locality position, her whole argument is unduly undermined.
As formulated by Farah (without citing anyone else), the
locality assumption states that the effects ofbrain damage on the
functional architecture are local, that is, the nondamaged components
of the architecture continue to function as they did
before the damage. According to Farah, such an assumption
would be justified in terms of informational encapsulation, the
key attribute of modularity. Indeed, the overall message of
Farah's paper is that since in a few neuropsychological deficits
the locality assumption does not seem to lead to the more
parsimonious explanation, and should therefore be abandoned,
the modularity assumption, from which the locality assumption
follows, should likewise be rejected. This inference is fallacious:
I assume that several commentators will pick this up so I will not
elaborate further on the subject; nor will I consider the merit of
alternative explanations for the specific cases Farah has discussed.
What I would like to point out, instead, is that the
locality assumption and the closely related transparency assumption
(also misrepresented in Farah's paper) have been
formulated otherwise. In particular, the inference of the form
"selective deficit in ability A implies a component of the functional
architecture dedicated to A" has not merely been cautioned
against but rejected as logically untenable, because it is
valid only under certain conditions.
Semenza et al. (1988) specifically argued, for example, that
the identification of a deficit (effect) D does not imply that any
separate processing component P exists. P may merely correspond
to a quite loose definition of processes that are supposed
to be part of normal performance. Yet, for the observed effects
there may be a cluster of alternative architectural solutions and
impairments; hence ifD occurs selectively, it may be viewed as
an independent phenomenon, but this in no way entails that P is
an independent process. The interpretative framework of the
locality assumption in Farah's formulation is founded on a
confusion between the dissociation of phenomena (which can
actually be observed), the dissociation of processes (which are
generally unspecified), and the definition ofinherent operations
(which, in fact, is based on an a priori conception ofa given task).
This framework is based on an illusion of transparency that
steins from arbitrarily mapping a priori concepts onto an interpretative
situation.
The assumption of transparency was indeed ambiguously
formulated at the very beginning (e.g., Caramazza 1984), in a
way that could be understood as compatible with the locality
assumption Farah criticizes (i.e., that there is a transparent
relationship between deficit D and processing components P
that are supposedly removed as a consequence of brain injury).
This interpretation of the transparency assumption, however,
seems to entail a paradox (Semenza 1993): what becomes transparent
(thus more understandable) after a brain lesion is that
which is lost! A weaker but more correct formulation may stress
the fact that brain damage allows one to better determine the
nature of processes that are opaque in normals' error-free
performance. The paradox would disappear: what may be transparent
is what is left. Caramazza's (1992) statement that transparency
requires that the behavior of the damaged system be
understandable in terms of the functional architecture of the
normal system is just a necessary proviso; that is, dissociations
remain meaningless without a theory as opposed to just a
statement of the transparency assumption itself.
Under any assumption, however, it seems unlikely that the
performance of neurological patients merely represents a combination
of intact and impaired patterns of behavior. In particular,
contrary to Farah's beliefs, that nondamaged components of
the architecture continue to function as they did before damage
does not follow from the modularity assumption. Indeed, under
the modularity assumption, the working of nondamaged modules
may undergo considerable modification. Suppose patients
have lost a module totally or partially, generally used to perform
a task: they may nonetheless want to try to carry on the task
(patients often do not even know there is anything wrong with
them). To do so, they may use other modules that, perhaps less
satisfactorily, allow the task to be completed. This possibility
makes things more complicated, but it may help research. The
functioning of residual modules could even be highlighted by
brain damage; overworking may somehow make them more
transparent to the observer (Marin et al. 1976; Saffran 1982;
Semenza et al. 1988). When this is not the case, it is true that the
researcher's life is harder, because a number of methodological
heuristics (see Shallice 1991) must be employed to make the
process used by the patient more transparent. The task is not
impossible, however.
In conclusion, I have tried to present a fair account of the
locality assumption, one that may correspond more closely to
people's thinking than the version presented by Farah. I think
that this account is much less prone to her criticisms. I assume
that for the specific examples she gives, where, on her account,
modularity seems to lead to less preferable explanations, she
will be directly answered by the authors of the competing
theory, who, I suspect, are still, like me, awaiting better reasons
(or magic) for believing one theory or the other.
Throwing out the neuropsychological data
with the locality bathwater?
Philip Servos3
and Elizabeth M. Oldsb
"Department of Psychology, University of Western Ontario, London,
Ontario, Canada N6A 5C2 and "Department of Psychology, Stanford
University, Stanford, CA 94305-2130
Electronic mall: a
servos@cogsci.uwo.ca; "olds@psych.stanford.edu
Farah's point is well taken that one should be aware of the
possible pitfalls ofthe locality assumption in neuropsychological
research. Her parallel distributed processing (PDP) models
provide elegant, distributed alternatives to various hypotheses
that depend on the locality assumption. Although her basic
arguments are sound, the extent to which Farah objects to any
form of the locality assumption remains unresolved.
One problem with Farah's arguments is that she seems to
address only a very extreme version of the locality assumption.
Surely few neuropsychologists would claim that a given structure
wholly and independently subserves a given function,
especially the reasonably high-level functions Farah discusses.
The incredibly rich interconnectivity of the brain would be
enough to convince anyone otherwise. Clearly, a given structure
would project to and receive inputs from various brain regions,
both proximal and distal, which might well play important roles
in the function under scrutiny. Most of us would accordingly be
content with the claim that a given damaged structure is impor-
80 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Commentary/Farah: Neuropsychological inference
tant, or critical, for a given disrupted process. If a functional
deficit frequently (or always) arises following damage to one
brain region, and not when damage occurs to other brain
regions, it seems reasonable to assign a critical role to that brain
region in the processes underlying that function. We can make
progress in this way even though we cannot be absolutely sure
there is a one-to-one mapping between structure and function.
This weaker version of the locality assumption seems to be the
one most neuropsychologists would adopt (Farah's claims to the
contrary notwithstanding). It seems surprising, then, that even
though Farah outlines several weaker versions of the locality
assumption early in the target article, she proceeds to address
only the extreme version of it.
Another problem with Farah's arguments against the locality
assumption is that, in the extreme, they preclude much if not all
neuropsychological research. Farah seems to be making the
strong claim that because it can be difficult to ascertain whether
a given brain region is wholly responsible for a given function,
we should avoid using the locality assumption and hence any
approach that makes use of it. We agree that a strict modularity
of function is probably incorrect and that cognition in general is
more distributed and interactive than some might claim. However,
that does not mean that a given cognitive process involves
such diffuse and nonlocalized processing that it is futile to use
neuropsychological techniques to identify the brain structures
underlying it. Furthermore, we are not sure what would replace
the locality doctrine, given that most corroborative techniques
(e.g., neurophysiology and functional neuroimaging) also make
use of this framework. At present, PDP and other modeling
techniques do not yield solutions that demonstrate the specific
neuroanatomical loci for particular brain processes, although
they have clearly shown potential as powerful tools for computationally
testing theories of human cognition; they may also be
able to guide neuropsychological research by providing models
of the underlying processes (e.g., see Gluck & Rumelhart 1990).
Obviously, the plausibility and relevance of such models are
increased when they incorporate details about the neural architecture
ultimately responsible for the processes in question.
Farah is clearly not denying the importance ofneural constraints
in modeling brain function but it is unclear how she would like to
see this sort of data collected, ifnot by techniques that make use
of the locality assumption.
Although Farah argues against a hard version of the locality
assumption and is quite sympathetic to the distributed framework,
it is unclear to what extent she embraces the latter
perspective. Is she, for example, willing to entertain an extreme
version of the distributed framework - something akin to Lashley's
notion of equipotentiality? We suspect not. Both extreme
positions seem untenable. This then places her in a position that
is not unlike some weaker version of the locality assumption that
most neuropsychologists would hold anyway. Moreover, is she
contending that the extent of interactivity is constant across all
kinds ofcognitive processes, orjust for the kinds ofexamples she
chose - examples for which locality-based explanations may be
particularly inappropriate?
In addition, though Farah is quick to reject the concept of
modularity, she still seems to accept it implicitly to some extent.
For example, in one passage she states that "it is well known that
different brain areas are dedicated to representing information
from specific sensory and motor channels." So, at some level, at
least for what might be called lower functions, she implies that
there may be some functional modularity in the brain. She also
seems to make use of modularity in her own work in that each
model she develops accomplishes a specific task. That is, although
the effects of damage to a given system are less local than
some neuropsychologists might feel comfortable with, they are
still local to the system ("module"?) she is modeling. This
suggests that her distributive logic may not apply equally well to
all levels of brain organization; that is, at some level, modularity
may exist. Thus, although Farah raises an extremely important
issue in cognitive neuroscience - the problem of establishing
which brain regions are considered essential for a given cognitive
process and which are irrelevant - her models do not
provide clear answers (although, to be sure, this is not a trivial
task). She opposes the idea of processes being encapsulated and
instead believes in the interactivity of structures, but it is
unclear to what degree she holds that such interactivity exists.
We are certainly not arguing here for modularity or any
extreme form of the locality assumption. Farah's arguments to
the contrary are quite strong and elegant in this regard. However,
there needs to be further clarification of what locality
represents and when and to what extent it is relevant in the
discourse of structure/function relationships. Discounting
neuropsychological data collection just because some particularly
extreme form ofa locality assumption is not feasible seems
a little like throwing out the baby with the bathwater. Instead,
neuropsychological research should obviously be continued,
but we should consider deeply the possibility that many mechanisms
may be more distributed than we thought, in the ways
that Farah and others have described. That is, there may be a
reasonable compromise: we should probably continue to use
some form of locality assumption to guide empirical research,
along with techniques that stress nonlocalist assumptions to
interpret the data (e.g., Rumelhart & McClelland 1986). Farah's
arguments are quite compelling, in that they push neuropsychologists
toward the "distributed" as opposed to the "local"
end of the interpretive continuum of cognitive functions. What
remains to be discovered is where exactly on this continuum we
should set our feet.
The real functional architecture is gray, wet
and slippery
Steven L. Small
Cognitive Modelling Laboratory, Department of Neurology, University of
Pittsburgh, Pittsburgh, PA 15261-2003
Electronic mail: sls@cs.cmu.edu
The target article by Farah argues against the view of the mind as
a set of "relatively independent information-processing subsystems"
and the assumption of this view in the design of
neuropsychological studies and the interpretation of their results.
I am sympathetic to Farah's conclusion, as are many
neurologists, speech and language pathologists, and computer
scientists. However, a number of her arguments are weakened
by missing neurobiological and computational links.
1. Anatomical localization. Neurologists and psychologists
have periodically attempted to explain the relationship between
local brain processes and global ones. Advocates of strong
anatomical localization of function (Benson & Geschwind 1989;
Broca 1861) produced much data from a clinico-anatomical
perspective, attempting to correlate particular cognitive behaviors
(i.e., clinical syndromes) with particular anatomical areas in
the human brain. This has typically involved the study of
patients with naturally occurring brain lesions and has required
the correlation of anatomically or physiologically described
neuronal loss with descriptions of behavioral loss (Damasio &
Damasio 1989; Kertesz 1983). Many neurobiologists have questioned
this localization approach (Freud 1891; Jackson 1878;
Lashley 1950; Marie 1906) and various locality assumptions have
been the subject of extensive debate for more than a hundred
years.
Over the years, descriptions of neuropsychological behavior
have improved dramatically, as the three empirical studies
discussed by Farah illustrate. Anatomical analysis has likewise
advanced, from a reliance on postmortem brain dissection to
high quality neuroimaging, including dynamic imaging of cerebral
blood flow and metabolism (Raichle 1989).
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 81
Commentaryi'Farah: Neuropsychological inference
A disheartening aspect of this new discussion of localization is
that the anatomy and physiology of the brain have been left out.
The term "locality" now refers to locations within an artificial
"functional architecture," rather than the brain.
2. Brain lesions. Whereas one can only debate philosophically
the effects of damage to abstract architectures, one can empirically
study the effects of neurological lesions on the brain. Brain
lesions come in a variety of types, however, from small areas of
infarction caused by occlusions of blood vessels to infiltrating
neoplasms that compress and injure adjacent brain areas to
diffuse and/or focal neuronal loss. The biological effects of these
different types of insults are disparate, and should influence the
conclusions one draws from patients who manifest them.
Farah describes several patients with category-specific deficits,
for example, and mentions their underlying neurological
diseases: several patients had herpes simplex encephalitis,
which typically affects parts of the temporal lobes, frontal lobes,
and limbic system, causing hemorrhagic infarctions in a patchy
distribution throughout these areas (Damasio & van Hoesen
1985; Price 1986). Another patient had a "head injury," and
presumably had axonal shearing (Auerbach 1986) in the fasciculi
of the centrum semiovale. A third had a degenerative disease
thought to be relatively more localized to left temporal lobe than
the rest of the brain, probably involving diffuse neuronal loss in
that area (Green et al. 1990).
Does knowing this increase our understanding of the cognitive
manifestations of category-specific naming impairments? I
suggest that it does. By talking not only about distributed
representations (as Farah does) but also their instantiation in the
anatomical architecture (which Farah doesn't), one can appreciate
the impact of different lesions to brain computations. What
sort of computational architecture allows for category-specific
impairments in the face ofone of three different types of damage
yet produces no such deficit in the majority of patients with any
of these injuries? That challenge is not addressed in discussions
of functional architectures that do not account for data on the
biological architecture.
3. Computational systems and metaphors. The advent of computation
has led to an ability to describe processes in a formal
manner, and information processing psychology has exploited
this by using computation both to describe and simulate cognitive
processes. Psychological theory could thus be tested by
simulating behavior in a computer model, which could serve as a
formal characterization of the underlying process. An astonishing
aspect of the target article is the implicit assumption that a
description of an abstract model is equivalent to a description of
the physical process.
The modern computer is based on one type of architecture,
the "von Neumann" machine, which consists of a central processing
unit (CPU), a memory, an input device, and an output
device. The CPU retrieves two pieces of data from memory,
performs a computation, and stores the results back into the
memory. Early information processing studies described human
mental computations by analogy to this sequential machine.
Later investigators, interested in the parallel processing features
of human thought, hooked up (conceptually) a number of
such machines, ending up with a computational framework that
fits Farah's definition of a "functional architecture." Such a
machine incorporates information encapsulation in modules,
independent computations, and a low frequency of interaction.
There was no reason a priori to understand the brain as such a
collection of interacting von Neumann computers, and as Farah
points out, there remains no such reason.
4. Connectlonlsm. A crucial question is the role of the connectionist
(or parallel distributed processing, PDP) models (Feldman
& Ballard 1982) in providing a different framework for
understanding cognitive behavior. As I am sympathetic to the
goals of connectionist modelling, I will mention only two points
in line with my previous discussion.
First is that connectionism (PDP) is a language for describing
theories about the mind or brain, not a theory in its own right.
Thus a discussion of PDP as true or false does not make sense.
Are the representations and methods of PDP useful adjuncts to
other descriptive techniques in conveying theoretical notions in
cognition? Do computer simulations based on these methods
teach us things we could not learn (or not as easily learn) any
other way? I don't view PDP as a religion, requiring faith in its
"truth," but I nonetheless agree with Farah that the representations
and methods of PDP are important descriptive tools and
that connectionist simulation has extraordinary value to inform
about cognitive and brain processes.
Second, one of the main appeals of connectionism is that its
basic units of discussion are "neuron-like. " Computationally,
this means that rather than describing systems in terms of large
bulky modules of computation, with poor ability to communicate
and relatively isolated functioning (i.e., distributed von
Neumann architecture), connectionism allows the description of
systems in terms of small units of computation such that their
pattern of intercommunication to a large extent comprises the
nature of the computation. Fault tolerance is a byproduct of
these designs. Such a computational paradigm makes sense
neurobiologically, and connectionist models can thus make use
of neuroanatomical constraints - and should.
ACKNOWLEDGMENTS
Thanks to Margie Forbes, Anthony Harris, and Gloria Hoffman for help
with the preparation of this commentary. The Cognitive Modelling
Laboratory is funded by the National Institute of Deafness and other
Communication Disorders, under grant no. DC00054. Their support is
gratefully acknowledged.
The functional architecture of visual
attention may still be modular
Carlo Umilta
Dipartimento di Psicologia Generate, University di Padova, 35139 Padua,
Italy
Electronic mail: umilta@ipdunivx.bitnet
To counter Farah's case against the existence of modules in the
functional architecture of visual attention, I will make the
following points: the "disengage" operation is not a particularly
good example of a possible modular component of that architecture.
Domain specificity is as important as informational encapsulation
in the search for attentional modules. To be domain
specific, attentional mechanisms must interact with perceptual
mechanisms, thus producing assembled modules. A model like
that of Cohen et al. (in press) could simulate egocentric neglect
or allocentric neglect, but not both.
The "disengage" module. In the classical paradigm introduced
by Posner (1980; Farah's Fig. 5), when the target stimulus
appeared at the uncued location, attention disengaged from the
cued location, moved to the location where the stimulus had just
appeared, and engaged at the new location. Parietally damaged
patients are very slow in responding to stimuli appearing at the
uncued location on the side contralateral to the lesion. This
observation has led to the notion of a selective deficit in their
ability to disengage attention (assuming it can be demonstrated
that the other two operations are not impaired).
This notion rests on the assumption that attention is reoriented
following an invalid cue. The evidence that reorienting of
attention occurs, however, isnotverycompelling(e.g., Henderson
& Macquistan 1993). It can be argued that in normal subjects
the costs incurred after an invalid cue are due to an attentional
gradient that peaks at the cued location and diminishes as spatial
distance from this location increases (e.g., Downing & Pinker
1985). The attentional gradient may fall off very steeply on the
contralesional side in parietally damaged patients. In this way,
one need not invoke a lesion of a disengage operation.
82 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Commentary/Farah: Neuropsychological inference
This is not to deny that mechanisms for disengaging and
orienting attention exist. Perhaps these mechanisms function on
the basis of competitive interactions, as modelled by Cohen et
al. (in press). They are cognitively penetrable, however, and
thus violate the criterion of informational encapsulation. In the
example provided by Farah (Fig. 5), an abrupt event in the
periphery of the visual field (the cue) automatically elicits a shift
of attention. Observers also have internal control over spatial
allocation of attention, however, so that they can voluntarily
shift attention in accordance with a cognitive cue (e.g., Umilta
1988). In addition, an attentional shift that would be triggered
by a peripheral cue can be inhibited voluntarily (e.g., Yantis &
Jonides 1990).
In conclusion, showing that the disengage deficit does not
necessarily depend on a lesion of a disengage module is not
relevant to Farahs argument. Perhaps, parietally damaged patients
do not have a disengage deficit. In any event, whatever
mechanism is lesioned, being cognitively penetrable, it cannot
meet one of the main criteria for modularity.
Domain-specific forms of neglect. Evidence suggesting the
existence of modular components in the functional architecture
of visual attention originates from other sources. One has to use
a different criterion for modularity, however: domain specificity.
A typical attentional deficit in parietally damaged patients is
neglect. Dissociations between visual and acoustic neglect (e.g.,
De Renzi et al. 1989) and between perceptual and motor neglect
(e.g., Tegner & Levander 1991) have been reported.
Within the visual modality, neglect can be confined to very
specific domains. Mulligan and Marshall (1991) reported evidence
of left neglect for near but not far space. In peripersonal
space their patient showed severe neglect on conventional tests,
including the line bisection task. However, when line bisection
was performed in extrapersonal space, by a pointing light or by
throwing a dart, neglect was abolished or attenuated. The
patient did not show personal neglect either.
Guariglia and Antonucci (1992) described the opposite dissociation
in a patient who had severe personal neglect in the
absence of neglect for peripersonal space (extrapersonal space,
in their terminology).
Halligan and Marshall (1992) went even further, arguing that
dissociations can occur within peripersonal space. Two of their
patients showed a classic double dissociation for two tasks (target
cancellation and line bisection) that are both performed in
peripersonal space.
The patient described by Cohen and Dehaene (1991) showed
neglect dyslexia only for numbers. He exhibited a spatial error
pattern akin to neglect dyslexia, making most of his reading
errors on the leftmost digit of any number. Apart from that, the
patient had no clinical indication of spatial neglect.
Another patient described by Young et al. (1990) had severe
neglect in recognizing the left half of normal faces, chimaeric
faces, and half-faces presented in isolation. By contrast, he did
not experience difficulty in recognizing the left side of everyday
objects or of car-fronts. Furthermore, there was no evidence of
neglect on item-cancellation and reading tasks.
In conclusion, if one takes domain specificity as a clue to
modularity, there is enough evidence that the architecture of
visual attention may indeed be modular. Sometimes attention is
seriously impaired in one domain but continues to function
normally in other domains.
Assembled modules. Based on domain-specific forms of neglect,
one can argue that isolable mechanisms exist that are in
charge ofallocating attention within rather restricted perceptual
domains. These attentional mechanisms must interact with the
perceptual components that share the same domain.
For example, a mechanism for allocating attention within
peripersonal space must be interconnected with a perceptual
mechanism for representing peripersonal space. The functional
architecture of the visual attention system proposed by Farah
(Fig. 7) contains these highly interconnected attentional and
perceptual subcomponents. This type of architecture seems to
violate the criterion of informational encapsulation.
Moscovitch and Umilta (1990; 1991), however, have argued
that modules can be assembled from a collection of more basic
subcomponents and that these assembled modules do not violate
the most important criteria of modularity as proposed by
Fodor (1983; see also BBS multiple review: 8(1) 1985), that is,
domain specificity, informational encapsulation, and shallow
output.
A functional architecture like the one outlined in Figure 7
may just depict an assembled module, with perceptual and
attentional subcomponents. This assembled module performs
specialized functions, does not interact with other modules, is
not influenced by semantic systems, and its output is not
semantically interpreted: it is domain specific, informationally
encapsulated, and delivers a shallow output.
Object-centered neglect. The so-called disengage deficit does
not usually occur in isolation. It manifests itself along with
neglect and/or extinction (e.g., De Renzi 1982). In fact, it might
be argued that the disengage deficit is the cause of extinction
and neglect (e.g., Posner et al. 1984). Patients with rightparietal
damage show extinction and neglect because they
cannot disengage attention from the right side of space and they
direct attention to the left side (e.g., Mark et al. 1988). A model
like the one proposed by Cohen et al. (in press) could easily
simulate extinction and neglect if the imbalance introduced in
the system is such as to render it impossible for stimuli on the
lesioned side ever to win the competition.
In this way, however, neglect would always occur in a fixed
coordinate system. In fact, a central concern is the coordinate
system(s) in which neglect occurs. It is true that parietal patients'
neglect often occurs in an egocentric space, where coordinates
can be retinotopic, head-centered, or body-centered, but
clinical evidence suggests that neglect also occurs in an allocentric
space, the coordinates of which are object-centered.
While reading texts, neglect patients may omit the left side of
individual words rather than the left side of the page (Schott et
al. 1966). A similar phenomenon can be observed when patients
copy a series of drawings that are horizontally aligned (Gainotti
et al. 1972; Ogden 1987). They sometimes reproduce only the
right side of every object in the display, including objects that
are on the extreme left.
Caramazza and Hillis (1990) described a patient who was lefthanded
and had neglect for the right side of space after a left
parietal lesion. She made reading and spelling errors only on the
end part of words, irrespective of whether words were presented
horizontally (i.e., the right part), vertically (i.e., the
bottom part), or mirror reversed (i.e., the left part).
In a study by Driver and Halligan (1991), a neglect patient was
asked to judge whether two elongated shapes, shown one above
the other, were the same or different. When the principal axis of
each shape was vertical, the patient neglected differences on the
left. When the shapes were both rotated 45° clockwise or
counterclockwise, she continued to neglect differences on the
left of the objects' principal axes, even if the differences fell on
the right of her egocentric axes.
I do not see how Cohen et al.'s (in press) model could possibly
simulate both egocentric and allocentric neglect. The task
would probably be much simpler for a model based on a modular
architecture. One perceptual-attentional module would represent
space egocentrically and allocate attention in egocentric
space. The other perceptual-attentional module would act likewise
for allocentric space. One need only assume that these two
modules can be lesioned independently.
ACKNOWLEDGMENT
This paper was supported by a grant from the Consiglio Nazionale delle
Ricerche (FATMA Project).
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 83
Commentary/Farah: Neuropsychological inference
Playing Flourens to Fodor's Gall
Tim van Gelder
Department of Philosophy, Indiana University, Bloomington, IN 47405
Electronic mail: tgelder@ucs.indiana.edu
The clash between neuropsychological localizers and their distributionist
opponents goes back to the dawn ofneuroscience. At
the turn of the nineteenth century, Gall was arguing that "the
brain is composed ofas many individual and independent organs
as there are forces of the soul" (Spurzheim 1815, p. 272).
Flourens countered that "there are not . . . different seats for
the different faculties, nor for the different sensations"
(Flourens 1846, p. 35). Gall and Flourens were just two sweeps
of a pendulum that has continued swinging to this day. Thus,
almost two centuries later, Fodor [1983] resuscitates Gall's
localizationist tendencies under the name "modularity," and
Farah here returns with the inevitable distributionist backlash.
Localizationists tend to assign particular higher functions or
capacities to particular "organs" or "modules" in the brain;
distributionists tend to see such functions as corresponding only
to the operation of many brain components. Localizationists
tend to see the brain's functional units as operating relatively
independently of each other; distributionists tend to regard the
brain's components as highly interactive. There are thus two
complementary ways in which localizers tend to be localist: they
localize particular functions to particular components, and they
see particular components as acting "locally," that is, noninteractively.
(Note, for example, how Gall insisted that to each of the
forces of the soul there correspond brain organs that are both
individual and independent.) Distributionists' denials are likewise
complementary: functions are not local to particular brain
components, and components do not act locally, but rather
interactively.
Farah is conducting a classic distributionist defense against
excessive localizationist tendencies. She shows how there need
be no proprietary components, organs, or locations for (1)
memories of living things as opposed to nonliving things, (2) a
"disengage" component in visual attention, and (3) visual processing
as opposed to visual awareness. She does this by explaining
the relevant data by means ofan architecture in which brain
components are interactionist, that is, nonlocal in their effects.
In doing so, she shows how foolhardy it can be to simply
assume that components are local in their effects. In fact, she
presents this as her primary theoretical result: that what she
calls the "locality assumption" is unreliable. Yet, surely, by the
very same demonstrations she is showing just as effectively that
the other locality assumption - that specific higher functions
correspond to particular dedicated components - is also unreliable.
The only criticism I would make of Farah's generally
brilliant target article is that she emphasizes one achievement at
the expense of the other.
This point can be given a sharper outline by focusing on the
form of inference that Farah is undermining. She claims that
"the locality assumption licenses quite direct inferences from
the manifest behavioral deficit to the identity of the underlying
damaged cognitive component, of the form 'selective deficit in
ability A implies a component of the functional architecture
dedicated to A'" (sect. 1.1). Ifwe lay out this inference explicitly,
it looks like this:
Premise 1. There is a selective deficit in ability A.
Premise 2 (Farah's locality assumption, LA). The effect of
damage on a component of the functional architecture is local;
that is, "nondamaged components continue to function normally"
(sect. 1.1).
Conclusion. There is a component of the functional architecture
dedicated to ability A.
The main thrust of the target article is that inferences of this
form are unreliable, and Farah lays the blame at the feet of the
LA. Neuropsychologists reach poor conclusions when they rely
on the LA; it is often a better hypothesis that brain components
are basically interactive.
Now, the point I am making is that there are really two locality
assumptions. Farah isolates one as the LA, makes it explicit in
the above form of inference, and successfully undermines it.
The other is hidden in the above form ofinference but is equally
unreliable. If this is right, then inferences of the above form
should sometimes lead to false conclusions even when the LA is
valid, because of the failure of this other assumption.
Here is an example. One day a caller to National Public
Radio's Car Talk radio call-in program informed the experts,
Click and Clack the Tappet brothers, that she had a problem
with her accelerator. When asked to elaborate, she said that the
car worked normally in all respects except that it had difficulty
accelerating. Click and Clack were ofcourse rather amused and
informed her that cars do not have accelerators (as opposed to
accelerator pedals); the problem was, most likely, with her
carburetor.
Now, the LA is, by and large, true ofcar engines. Not only do
most components interact directly with only one or a few other
components; if there is damage to a component, undamaged
components continue to function normally. Yet the inference
from selective deficit (poor accelerating) to dedicated component
(accelerator) still fails. The caller was relying on a further
hidden assumption: that each identifiable function of the car
must be accounted for by a dedicated component. It was this
assumption, not the LA, which led to her mistaken conclusion
that she had an accelerator which was malfunctioning. This
assumption can be formulated the following way:
Premise 3 (The other locality assumption). For a given specifiable
ability of a system there must be a component of the
functional architecture responsible for that ability.
Without this assumption, the inference from a selective deficit
in ability A to a component dedicated to A simply fails to go
through, since the ability A may be one that corresponds only to
the operation of many components (which may each have only
local effects). If this assumption is false or unreliable, it will lead
to unreliable conclusions.
When neuropsychologists make inferences of the kind Farah
rightly criticizes, they are typically making both locality assumptions.
Farah's models and arguments successfully demonstrate
that both assumptions are unreliable - and probably false
in the case of the brain. The twin locality assumptions are at the
very heart of the localizationist tradition. In undermining them
both, Farah is truly playing Flourens to Fodor's Gall.
Prosopagnosia, conscious awareness and
the interactive brain
Robert Van Gulick
Department of Philosophy, Syracuse University, Syracuse, NY 13244-1170
Electronic mail: rnvangul@sunrise.bitnet
Farah makes a convincing case against the methodological
necessity, if not against the truth, of the locality assumption. In
each ofthe three cases she considers, she provides a serious and
plausible alternative to the standard explanations without relying
on assumptions of locality or Fodor-style modularity. Since,
as she rightly observes, both sets of inferences fit the existing
data, the choice between the competing models must be based
either on further data or on other empirical considerations, such
as simplicity, or coherence with established principles of brain
organization. In the latter regard, she finds her alternative
nonlocalist explanations superior to their standard competitors.
However, the sorts of considerations she invokes (sect. 3.1)
weigh rather lightly on the empirical scales. With respect to
both visual attention and prosopagnosia she appeals to the fact
84 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Commentaryi'Farah: Neuropsychological inference
that her model has fewer components. Though parsimony
counts for something, it is a far from reliable guide to truth.
Reality unfortunately often turns out to be more complicated
than we would prefer, and nature's designs in brain organization,
as elsewhere, are often far from ideally simple. Thus the
truth, as opposed to the necessity of the locality assumption,
remains very much an open question.
Several special questions arise with respect to Farah's analysis
of prosopagnosia. She notes that at least some researchers (de
Haan et al. 1992) relying on the locality assumption have
attempted to explain the dissociation between covert and overt
face-recognition tasks as the result of damage to the conscious
awareness system that prevents it from accessing the results of
the face-processing module, which itself continues to proceed
normally in covert recognition. Farah claims that in her alternative
model the face components, when not damaged, do the
work of both the face-processing module and the conscious
awareness system in the standard model, and that when they are
damaged they, by themselves, replicate the clinical pattern of
severely diminished performance on overt recognition tasks
combined with partially preserved covert performance. Most
important, Farah states that the ability of the model to account
for this dissociation "depends critically on this violation of the
locality assumption" (sect. 2.3.4).
However, there are at least four problems with Farah's position.
First, the inference she is criticizing is open to objection
quite independently of any challenge to the locality assumption.
Inferences based on single dissociations are notoriously risky.
The preservation of ability A in conjunction with the loss of a
different ability B can at best be taken as weak evidence that
abilities A and B depend on distinct components, even if one is
assuming localism. There is always the rival hypothesis that A
and B depend on the same components but B requires a higher
level of functioning of one or more of those components than A
does. In its damaged state the relevant shared component is
simply no longer able to function at the level required for the
more demanding B-type tasks (Shallice 1988). Double dissociations
in which the converse patterns of loss and preservation are
found in different patients thus provide much better evidence
that the abilities depend at least in part on distinct components.
Second, it is this very inferential weakness that is exploited in
Farah's criticism of de Haan et al. In her alternative model, the
face units, which are close to constituting a component in the
more standard sense, are damaged to such a degree that they are
no longer able to meet the demands of overt recognition but
still function well enough to meet the lesser requirements of
covert recognition. Farah's model seems to be on a par with the
sort of resource limitation hypothesis that would (or at least
should) be standardly entertained as an alternative explanation
of single dissociations by those working within the locality
assumption.
Third, Farah's final claim is thus called into question. In what
sense does her explanation depend critically on violation of the
locality assumption? It would seem it does not. Admittedly, the
preservation of some residual function in the faces unit is
explained by the distributed nature of the PDP-type representation
it uses, but that is a different issue. The locality issue in
dispute concerns not whether information is represented in a
local or distributed fashion within components, but whether the
other components of the system themselves continue to function
in the same way after damage to a single component as they
did before. I fail to see how Farah's model of prosopagnosia
requires violation of the locality assumption in the latter sense.
Consider relearning after damage. Clearly, what is relevant is
that even in its damaged state the faces component retains
enough of its earlier distributed representation to allow for its
reconstruction with training more quickly than it could if it had
retained no portion of that representation. However, this all
concerns what happens within thefaces component itself; it does
not involve interactively induced changes in the functioning of
other components.
Fourth and last, it is not clear that Farah's model in its intact
state accounts for all the abilities of normal subjects. Remember
that normal subjects report introspective and conscious awareness
of recognizing familiar faces. Those reports and the conscious
awareness that underlies them need to be explained, as
does their joint absence in prosopagnosics. A network's ability to
match a face with a name or an occupation is not the same as
having a conscious experience of recognizing the person. Farah's
model is of course not designed to simulate conscious awareness,
nor does it do so. But a fully explanatory account of face
recognition does at some point have to address that phenomenon.
Normal subjects do consciously experience familiar faces as
familiar, and that fact needs to be explained.
In this context it may be helpful to think about conscious
awareness in a way that is in keeping with the interactive spirit of
Farah's approach. In the model she criticizes, the conscious
awareness system is treated at least implicitly as yet another
module, a distinct component, to which inputs are passed by the
face-processing module. However, there are good reasons to
doubt the existence ofany privileged location or unit ofthe brain
serving as the conscious awareness module or what Dennett and
Kinsbourne have called the "Cartesian Theater" (1992). The
formation of conscious states is more likely to involve the
integration of local representations from many specialized brain
regions into an interactively unified representational state, what
Kinsbourne refers to as "an integrated field theory of consciousness"
(1988; 1993). Local representations are not passed on to
any supermodule; they are "recruited" for incorporation into
global coherent unified states. One of the functions of such
states would be to bring isolated items of information, such as
the visually processed image of a face, into contact with a wide
range of other items of information in a way that subserves the
sort of flexible and relatively open-ended range of behavioral
responses we typically associate with conscious awareness. Such
a theory might well be combined with Farah's model, in which
the role of a given representational subsystem can shift depend.
ing on which other systems it is interacting with. Moreover, the
lack of conscious face recognition in prosopagnosics might result
from the fact that the residual representations after damage are
now too attenuated to be recruited into preexisting global
patterns, although with retraining the relevant threshold might
be achieved again soon - or at least more quickly than during
initial learning. Such interactive and global theories of conscious
awareness are admittedly speculative, but conscious awareness
does eventually require explanation, and such theories seem to
show a natural affinity with the interactive models Farah
proposes.
The symbolic brain or the invisible hand?
Ren6 van Hezewijk and Edward H. F. de Haan
Department of Psychonomics, Utrecht University, 3584 CS Utrecht, The
Netherlands
Electronic mall: hezewijk@fsw.ruu.nl; dehaan@fsw.ruu.nl
Not even a connectionist can do without some sort of computational
(or competence) theory (Marr 1982) of what it is that the
brain must do, wherever or however it does it. In this commentary,
we discuss first whether parallel distributed processing
(PDP) as a general conceptual framework can do a better job
than the old-fashioned symbolic models. We will then address
two problems with the specific PDP implementations of the
living-nonliving dichotomy and covert face recognition.
The locality assumption in neuropsychology borrows partly
from common sense and partly from sophisticated symbolist
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 85
Commentary/Farah: Neuropsychological inference
theories of what a person's competences should be. When a
particular competence has become disrupted after neurological
disease, the search for the functional (and physiological or
anatomical) nature of the dysfunction begins. Connectionist
explanations for dysfunction are either parasitic on the commonsense
and symbolist characterizations of cognitive (dys)function
or must find a way to derive from their brain-style models what
the impairment could be. The latter (independent) way is the
hard - if not impossible - way. We have never seen an example.
So the first option remains. In our view, this means that the PDP
approach, interesting as it is, must drop its pretense of being a
completely independent alternative conceptual framework. It
cannot be much more than an "implementational theory" of
cognitive (dys)function, complementary to competence theories.
Some of the consequential claims will have to be toned
down as well; for example, it remains an empirical question
whether the connectionist idealizations are supported by physiological
and anatomical research. Also, if assumptions such as
the locality assumption are falsified, this has repercussions for
PDP modeling when it is embedded in the symbolic approach.
Finally, conclusions concerning PDP models are "local" too, in
the sense of not predicting more dysfunctions or different ones
from those the symbolic models predict. In other words, unless
connectionist theory (PDP-style) independently infers cognitive
(dys)functions from changes at the brain level, it will produce
only ad hoc explanations of symbolically defined cognitive
dysfunctions (for the precise meanings of ad hoc see Lakatos
1970).
Our second point is that PDP models do not seem to be able to
distinguish between impaired networks (lesioned models) on
the one hand, and networks that have learned impaired behavior
on the other. One might just as well program a PDP model to
produce the same performance as that observed by Farah and
McClelland (1991), Farah et al. (1991), and Farah et al. (1993),
for this would clearly not result from damage but from learning
to produce the desired results. This is the consequence of the
"programmatic ad hocness" one often finds in PDP-style modeling.
PDP lacks clear theoretical answers (logically prior to
experimenting with and calibrating the network) to the following
questions: (1) How many units does one need? (2) How many
layers does one use? (3) What learning rule does one use? (4)
How many trials does it take to have the network learn the job it
has to do? (5) Who or what defines the task? And in the case of
lesioning the model: (6) Which units are damaged, and (7) how
many units? The answer to the fifth question is found outside the
PDP program itself and lies in the symbolic approach. The other
questions were not answered by Farah in the present article and
cannot be answered by the reader by inferring from the (PDP)
theory. We suggest, and will believe until shown otherwise, that
this is left to the discretion of the network programmer, the
"invisible hand" in PDP-style modeling.
This is not to say that there are no ad hoc practices in the "boxand-arrow
approach." However, in this approach it is customary,
if not obligatory, to test an explanation with new predictions for
both impaired and unimpaired subjects. All we can see in the
reports of PDP models is how anything done by the traditional
approach can be done with the PDP approach as well. Regarding
the empiricist claim for "sufficiency of theory," Farah is of course
right that no theory can ever do more than fit the known data at
the time. However, what happens next? It seems to us that PDP
modelers just ask themselves: "What is the next phenomenon to
model?" whereas (realist) symbolic modelers would continue:
"So what are the predictions from this model and how can I test
them?" In this sense, the PDP approach can be characterized
as "abortive," whereas the symbolic approach has inherent "excess
content" (Popper 1963; Lakatos 1970). The locality assumption
may be a weak spot of the classical symbolist approach;
however, the "keep it local and address one issue (defined
symbolically) at a time" assumption is a weak spot in PDP-style
connectionism.
Our third point is that the lesioned PDP models used by
Farah to demonstrate nonlocality should be tested for recovery,
be it spontaneous, supervised, or by deviation. Some patients
suffering from the dysfunctions Farah discusses recover, while
others do not. We wonder whether the lesioned models show
certain patterns of recovery. A related question concerns
whether, assuming that PDP models are able to describe the
observed neuropsychological data without using the locality
assumption, they do a better job overall. For example, one of the
great triumphs of PDP-style modeling is the "graceful degradation"
that damaged models show; but is there always (only)
graceful degradation in the neuropsychological reality?
Our fourth point concerns the assumptions necessary to make
the neuronal idealizations of the PDP approach possible. Inhibitory
and activating connections are realized in the same connections
in PDP models. But antidromic connections do not exist in
the real neural anatomy. Also, the often used learning strategy of
backpropagation is biologically implausible. Grossberg (1987)
has shown how complicated the necessary neural hardware is
that is needed to implement backpropagation (but see Davis et
al. 1989, for an alternative viewpoint). PDP-style modeling uses
a sweeping simplification of nature. Therefore the PDP model
shown in Farahs Figure 7 is not as simple as suggested.
A fifth and last general point is the following. Farah states that
"the effects of damaging one component should be relatively
local." This assumes the rather rough and unsophisticated version
of modularity of Fodor (1983). A more sophisticated interpretation
leads to different predictions. For example, Jackendoff
(1987) suggests in his intermediate level theory (ILT) that
informational encapsulation is relative to a certain representational
level that is more refined and better defined than Fodor's,
and that informational encapsulation need not correspond to
strict cerebral encapsulation (= localization) of processes. For
example, one would predict that if there are relatively local
impairments somewhere in "lower vision" (e.g., in those neuronal
substrates that compute primal sketches), this only affects
higher vision (e.g., 2|D sketch, the spatial or 3D model,
conceptual structure) insofar as the information used at the
higher level originates in the lower level. The symbolist approach,
for example, Jackendoff's ILT, makes it possible to
predict the kinds of interactions that can be found between
different representational levels in the more sophisticated
sense. So the real issue is not only the degree of interactivity or
nonlocality but also the nature (or content) of the interactions.
PDP-style modeling and theorizing does not have much to offer
in this sense.
Finally, we would like to focus on two of the three specific
implementations used by Farah to argue her position in the
target article. First, in her discussion of the selective impairments
in knowledge about living and nonliving things she states
that the PDP model can accommodate the existing neuropsychological
data. We are curious to know whether this also
includes the findings of Young et al. (1989), who found that the
patient MS was severely impaired in overtly retrieving knowledge
about living things compared to nonliving objects, but that
this difference disappeared when his knowledge was probed in
an indirect priming experiment. Are we right that this might
require the "invisible hand" of the programmer, or can the
model cope as it stands?
De Haan et al. (1992) were using the concept of "modules"
(quotation marks in the original) to describe the dissociation
between autonomic responding, information processing, and
conscious awareness. Their patient demonstrated covert facerecognition
effects on both physiological and behaviorial indices
in the absence ofconsciously acknowledged recognition of faces.
The rather unsophisticated use of modular organization was
intended to describe this puzzling phenomenon. We are very
keen to learn how the dissociation from awareness can be
modeled in a distributed network. Is it the ghost in the PDP
machine?
86 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Commentary/Farah: Neuropsychological inference
The localization/distribution distinction in
neuropsychology is related to the
isomorphism/multiple meaning distinction in
cell electrophysiology
Gerald S. Wasserman
Department of Psychological Sciences, Purdue University, West Lafayette,
IN 47907-1364
Electronic mail: codelabtuipsych.purdue.edu
I wish to offer here the "bottom up" observation that the
neuropsychological concepts that form the basis of Farah's
excellent target article have their counterparts in concepts now
percolating up through neuropsychology's cellular substrate.
There are two links: on the one hand, if one holds that a
particular function is localized to a particular place in the brain,
then one must also hold that the cells resident in that place can
only be involved in supporting that function. On the other hand,
if one holds that functions are distributed to many places around
the brain, one unit also hold that any given place in the brain will
tend to mediate more than one function. Hence, the distribution
assumption would lead one to expect single cells to support
more than one function.
The latter half of this proposition was clearly articulated by
Farah, using parallel distributed processing (PDP) terminology,
in section 1.4 of her target article, where she wrote: "Different
entities can therefore be represented using the same set of
units, because the pattern of activation over the units will be
distinctive."
The fact that certain properties are exhibited by PDP models,
however, does not necessarily limit what goes on in the real
nervous system. The present commentary therefore draws attention
to the fact that investigations of the cellular elements
which collectively constitute the various "places" of neuropsychology
have recently led to serious discussions of this issue on a
microscopic level: Specifically, do real individual nerve cells
contain information which relates to one function or to several?
Elsewhere (Wasserman 1992), I have provided an extensive
review1
of this cellular discussion. What follows is a brief
summary of that review, omitting citations.
Isomorphism. The cellular counterpart of the locality assumption
has been named the isomorphism hypothesis. It is generally
introduced in standard texts in the form of a laconic ostensive
definition focusing on the special case of spikes propagating in an
axon. Discussion is often narrowly couched in terms of "frequency
coding," with the frequency of axonal spikes the index of
information resident in that axon. This amounts to a tacit
assertion that an axon conveys information only about one thing.
This is an old view which was first clearly stated when the
advent of electronic amplification made it possible to record
from single nerve cells. That technology forced a consideration
of the antecedent question posed by the fact that cellular
sensory responses differ in form from the stimuli which evoked
them. In conjunction with certain psychobiological correlations,
this led to the conclusion that sensations were isomorphic with
the waveforms of cellular sensory responses. The original meaning
was that the magnitude of a sensation was indexed by the
magnitude of the cellular responses and the time course of a
sensation was indexed by the time course of the cellular
response.
The isomorphism concept developed over the years by incorporating
more recent discoveries. Of particular importance
were the manifold indications that neurons often do not respond
unless an appropriate spatiotemporal pattern of stimulation is
delivered. The isomorphism concept thereby became generalized
to the concept that high activity in a given nerve cell was a
strong indication that one particular pattern of stimulation was
present.
The various manifestations of the isomorphism hypothesis
share the notion that a nerve cell is a univariate device whose
activity signals some one thing of particular functional significance.
The more the cell responds, the more of that function is
present. It then becomes the business of the investigator to
determine the role of a given cell by inquiring into the nature of
the function signaled by its level of activity.
Patterning in neuronal signals. Problems developed fairly
early in the history ofcellular electrophysiology, however, when
investigators tried to fit the complexity of real neural responses
into the Procrustean bed of the isomorphism notion. One of the
earliest findings, for example, is that changing wavelength
changes the pattern of response in some color-coding neurons.
Even today, appreciation of the deeper significance of this wellknown
fact is often blunted by characterizations of these complex
patterns which constrain them to fit into a univariate metric.
Over time, many complex response patterns have been characterized
in many neurons, and these patterns have been demonstrated
to be under the influence of multiple sensory variables.
This suggested that the pattern of a nerve cell's response
carries information that is not encoded in its overall activity
level.
Similar problems became evident on the output side. It
became abundantly clear - from studies of synaptic transfer in
both muscles and neurons - that the efficacy of transmission
depended critically on the pattern of presynaptic activity as well
as on its quantity.
Multiple meanings. These problems gradually led many
scholars to consider the possibility that the complex pattern ofa
neuron's activity might be capable ofsignaling information about
more than one aspect of sensory input or motor output. It is now
not uncommon for this notion to be expressed in terms of the
"multiple meanings" that may reside in a single cell's activity.
At first, this discussion was primarily formal and hypothetical,
with a limited empirical base. More recently, careful quantitative
investigations have demonstrated that multivariate properties
are very common in neurons. Particularly interesting are
reexaminations of certain classical findings of visual physiology,
which have been illuminated by multiple-meaning theory. Both
the contrast-sensitive receptive fields of retinal cells and the
orientation-sensitive receptive fields of cortical neurons have
been thoroughly scrutinized in this way. At both levels of the
visual system it has been demonstrated that important information
about the stimulus resides in the temporal waveform of a
cell's activity. Because of this, simple univariate assessments of
the overall responsiveness of such cells will necessarily produce
ambiguous results.
Pattern predicate. This interpretation of the data predicates
that the nervous system must be able both to create and to
process structured patterns in neuronal responses. This suggestion
has led to very interesting results. Two may be of special
significance to neuropsychology. First, neural mechanisms appear
to exist which can convert the temporal pattern of activity
occurring in a single part of one neuron into a spatial pattern of
activity with differential effects appearing in different places.
Because of this finding, bare evidence of connectivity may be
profoundly incomplete. Second, consciousness itself - as indexed
by the effects of anesthetics on neuronal responses - may
depend on the pattern of activity in neurons, not on their
activity level.
These recent cellular findings will surely influence the conceptual
nervous system on which much of neuropsychology has
been erected. Even if the strongest postulates of multiple
meaning theory, as reviewed in Wasserman (1992), are ultimately
subject to extensive revision, neuropsychologists interested
in the locality issue may want to consider the evidence that
has recently been uncovered by these seminal cellular inves-
tigations.
NOTE
1. Wasserman (1992) is also available by e-mail from the connectionists
archive by anonymous file transfer protocol (ftp). To retrieve it, log
on and do the following (where % stands for your own system's prompt):
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 87
Commentary/Farah: Neuropsychological inference
%ftp archive.cis.ohio-state.edu
Name: anonymous
Password: your e-mail address
ftp> cd pub/neuroprose
ftp> binary
ftp> get wasserman.mult mean.ps.Z
ftp> quit
%uncompress wasserman.mult mean.ps.Z
%lpr -s wasserman.mult mean.ps
If the printer for this job resides on a remote machine, this large (i.e.,
graphics-intensive) file may require that an operator issue the print
command directly from the remote console.
What counts as local?
Andrew W. Young
Department of Psychology, Science Laboratories, University of Durham,
Durham DH1 3LE, England
Electronic mall: andy.young@mrc-apu.cam.ac.uk
Selective impairments have attracted great interest because
they provide a powerful source of evidence for testing psychological
theories. The argument is that an adequate psychological
theory of how a particular ability is organised should be able to
account for the patterns of impairment found after brain injury.
To the extent that it fails to do this, the theory should be revised
or abandoned. The force of this approach is clearly seen in
Warrington and Shallice's (1969) finding of preserved long-term
memory despite poor immediate recall, which is incompatible
with the view that perceived stimuli must pass through a period
of short-term storage before they can enter long-term memory,
and in Marshall and Newcombe's (1966) demonstration of semantic
reading errors ("ill" read as "sick," etc.), which imply that
reading cannot be exclusively mediated through recoding print
into sound.
Since these pioneering investigations, neuropsychological
studies have often been used both to test and to derive models of
the functional architecture of human cognition using an approach
widely described in terms of a metaphor of brain injury
as a cruel and somewhat haphazard natural experiment that can
occasionally carve nature at its mental joints.
• Farah argues that interpreting deficits in this way involves a
"locality assumption," in which "the removal of one component
would have only very local effects on the functioning of the
system as a whole." She invites us to think this "naive," suggesting
that it has led to "a mindless reification of deficits."
Those of a historical bent will recognise that we have been
here before; the work of the nineteenth-century diagram
makers was dismissed by people who did not accept that particular
patterns of deficit could be attributed to the loss of particular
cortical centres, or even that there were distinct patterns of
deficit at all (McCarthy & Warrington 1990; Shallice 1988).
Eventually, this globalist critique was recognised as overstated,
and the localist approach was revived with more stringent
standards of inference and evidence.
A crucial problem is that "local" is never defined in the target
article. Yet what counts as local depends entirely on ones point
of view. To a person on Mars, or even in London, Durham might
well be in the locality of Sunderland, but it does not seem so
from here.
This is important because, to the best of our knowledge, the
locality assumption is indeed appropriate at what might be
considered coarse deficit scales. For example, I know of no
evidence to suggest that visual deficits are inevitably accompanied
by hearing loss, or that receptive aphasias necessarily
create problems in moving your toes. The fact that neurons are
highly interconnected influences this no more than the interaction
of the molecules in the atmosphere implies that when I
breathe here in Durham any consequent breeze will be detectable
in Sunderland. Farah would seem to agree, since she
comments that "different brain areas are dedicated to representing
information from specific sensory and motor channels." This
is locality without invoking the label.
, Since locality already applies to coarsely defined deficits, the
issue to be resolved only concerns the level at which it might no
longer be useful because evidence of interactions between finegrained
deficits starts to emerge. Yet the target article treats this
issue as if it could be determined by theoretical fiat, and as if the
adoption of parallel distributed processing (PDP) models somehow
settled the necessary theoretical choices. It does not.
Consider Figure 1. This is the first PDP model of an entire
personality; SAMSON. Conveniently, we happen to know quite a
lot about its behaviour because it is the same model as Figure 11
in the target article, with the labels changed. In this model, we
can simulate the effects of shaving Samson's head by reducing
the activations of the hair length units. Notice that when we do
this the model's strength begins to fall and it can no longer
engage in Delilah-lusting or temple-shattering behaviours. Yet
if the hair length units can subsequently gain in activation, its
strength returns.
The point is this: connectionist models provide a powerful tool
for implementing and exploring potential accounts of certain
neuropsychological findings, and especially certain types of
dissociation. They do not substitute for evidence, however. It is
evidence which must determine the correct choice of components
to be modelled, and evidence which will ultimately
determine the extent to which one can rely on locally based
descriptions of mental abilities. A simulation can only be judged
by the extent to which it is compatible with a broad range of
existing evidence and capable of generating predictions to be
tested.
As SAMSON shows, the level of description at which an interpretation
is attempted is as crucial in simulation as it is in
neuropsychology. There is a risk of overinterpreting what
computer models are doing and losing sight of difficult questions,
as Searle (1984; 1992) has pointed out. We so easily slip
into reading our own ideas about attending into the boxes
labelled "attention" in Figure 7 of the target article. Similarly,
the model shown in Figure 11 does not really recognise faces,
and it isn't conscious either. What it does is to show that
impairing a particular type of system can leave it able to perform
some functions and not others. This is certainly a pertinent
observation, but the same point has already been made by
researchers who have seen it as a modest step forward, not a
solution (Burton et al. 1991). For example, a striking feature of
prosopagnosic patients who show covert recognition of familiar
faces is that they do not seem to act on this in everyday life; they
Hidden Strength Moral Fibre
Hair Length Behaviour
Figure 1 (Young), SAMSON (Simulation of Alopecia and Masculine
Strength with an Organised Network).
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Commentary/Farah: Neuropsychological inference
do not greet familiar people in the street without knowing why.
Such observations are consistent with the commonsense conception
that conscious recognition is involved in intentional
actions, and one wants an account of how this happens, yet the
type of model shown in Figure 11 has little to say about this.
Locality, then, is an empirical issue, not an overriding assumption,
and what is to count as local depends on some notion
of the appropriate scale of theory required. Connectionist
models can have many elements, but at present the brain has far
more. A degree of interactivity of deficits is to be expected, but
this may only happen at finer-grained levels of analysis than the
target article implies.
Modularity need not imply locality: Damaged
modules can have nonlocal effects
Edgar Zurifa
and David Swinney"
'Department of Psychology, Brandeis University, Waltham, MA 02254 and
Aphasia Research Center, Boston University School of Medicine;
b
Department of Psychology, University of California, San Diego, La Jolla,
CA 92093
Electronic mall: zurif@brandeis.bitnet
Farah takes a skeptical look at several accounts in which behavioral
deficits are taken to reveal the local effects of disrupted
cognitive components. We agree with her on the inadequacy of
these accounts and think that in each case her interactionist
descriptions may well be better. However, we disagree with her
view that the accounts she criticizes are based on a modular
cognitive architecture of the sort proposed by Fodor (1983; and
she seems unaware of the existing empirical tests for modularity).
We especially disagree with her argument that encapsulated
modules are not useful in neuropsychological explanation
because they do not interact enough.
Contrary to Farahs views on the matter, modular components
of Fodors sort are not necessarily less interactive than
those that figure in maximally interactive PDP frameworks. The
difference between interactive and modular systems turns, not
on the amount of interaction, but on when interactions among
constituent processes take place. In the interaction account,
interactions seem to occur as available, whenever potentially
useful; in the modular account, they occur only at the endpoints
of the constituent computations (Fodor 1983; Fodor et al. 1992;
Forster 1979; Garrett 1981). This being so, the effect of a
damaged process can be as nonlocal or as local in a modular
system as in an interactive one - it depends on the overall layout
of the components, how they share resources, and so on (see,
e.g., Forster 1979).
Farah has it otherwise, however. She stipulates that if interactions
occur only at endpoints, they must be limited. To justify
her claim, she aims her nonlocality arguments at targets that, as
we have already suggested, are rather flimsy (or at least they
seem that way in Farahs accounts of them).
Consider the face-recognition case. The finding is that patients
can recognize faces without being aware that they have
done so. As Farah states it, the locality position here is that a
functional lesion outside the face-processing module prevents
the module from transferring its product to conscious awareness.
This is hardly a test of locality or modularity, however; all it
does is restate the phenomenon.
Farah, by contrast, puts some details into her interactive
model of face recognition, but the contrast she provides is not
between an interactive and a modular account. Rather, it's
between an interactive account and one that fails altogether to
consider the details (and the time course) of possible interactions
- fails even to provide the necessary ingredients for
thinking about interactions of the sort considered by Farah.
As for the semantic memory case, the partitions entered for
the locality position are very incompletely drawn. The livingnonliving
distinction has little organizational impact; generic
concepts that serve as unique beginners of separate hierarchies
seem, at the least, to distinguish plants, animals, and persons
(Miller & Fellbaum 1991). And the effort to transform the livingnonliving
distinction into an equally unalterable one between
sensory and functional information does not work, As Farah
points out, the two sets of categories are simply not coextensive.
And neither set seems to bear the burden of current theoretical
analyses of lexical conceptual structure - analyses that seek to
tie together conceptual structure and grammar and that test
semantic distinctions against large amounts of lexical data, in
short, analyses that go beyond simple intuitions about defining a
word (Levin & Pinker 1991).
More pointedly, however, the partitions in the so-called
locality model of lexical semantics seem to define modules only
in the weak sense that Farah claims to have no quarrel with; the
modules are nothing other than expressions of the fact that
different kinds of knowledge are accommodated in the lexicon.
These partitions do not seem to require the property of cognitive
impenetrability. It's one thing to create a partition to
account for relatively selective naming impairments, quite another
to show that each of the categories the partition defines is
encapsulated and has only minimal interactions with the rest of
the system. These are empirical matters that do not seem to
have been settled by Warrington and her colleagues.
There are, however, instances in which disruptions to encapsulated
modules have been isolated, and these disruptions have
been shown to have distinctly nonlocal consequences. What we
have in mind turns on characteristics of lexical activation during
the course of sentence comprehension: immediately upon hearing
a polysemous word in a sentence, the normal (neurologically
intact) listener activates all of that word's meanings, not just the
one relevant to the sentence context. Only after a time delay of
approximately a second does context exert its effect; only after
that time does context damp all of the word's meanings save the
relevant one (e.g., Swinney 1979). The general lesson here is
that sentence processing does not consist of a set of maximally
interactive processes. Rather, the lexical activation device
seems momentarily informationally encapsulated - in short, it
behaves as a module.
More directly to the present point, lexical activation follows
this modular course in Wernicke's aphasia too, but not in Broca's
aphasia (Swinney et al. 1989). It is not that the lesion that
underlies Broca's aphasia causes "unencapsulation." Rather, it
seems to cause a "module-internal" problem - the Broca's
patients remain uninfluenced by sentence context but appear to
activate word meanings in a slower-than-normal fashion (Swinney
et al. 1989; also Prather et al. 1991).
In an effort to determine how this modular disruption might
ramify within the comprehension system, we have lately focused
on the real-time syntactic formation of within-sentence
dependency relations - on the linking of antecedents and
anaphors (including here the reactivation of moved lexical elements
at the site of their extraction). This syntactically directed
lexical reactivation must be implemented under strict time
constraints (immediately upon encountering the structural licensing
conditions; Swinney & Fodor 1989; Swinney & Osterhout
1990). The results under these circumstances are as
expected: the Broca's patients fail to reactivate lexical elements
within the normal time frame - they are unable, that is, to
establish syntactically indicated dependency relations in a normal
manner (Zurif et al., in press). Moreover, this lexical
reactivation problem shown "on-line" connects directly to independent,
"off-line' analyses of sentence comprehension limitations
in Broca's aphasia: it accounts for the repeated observation
that comprehension is particularly difficult for these patients
when one element in a sentence must be interpreted with
respect to another element in that sentence (e.g., Ansell &
Flowers 1982; Caplan & Futter 1986; Caramazza & Zurif 1976;
Grodzinsky 1986). The more general point, of course, is that
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 89
Response/Farah: Neuropsychological inference
within a modular system, disruption to one module can have farreaching
(nonlocal) consequences.
The above particulars hold only for Broca's aphasic patients.
In line with their normal lexical activation functions, Wernicke's
patients show normal patterns of syntactically governed lexical
reactivation. That is, they establish intrasentence dependency
relations within the normal time frame (Zurif et al., in press). So
to the extent that Broca's and Wernicke's aphasia implicate
different lesion sites, the modular lexical activation disruption
and its specific syntactic consequences have lesion localizing
value. And this is another feature of a modular system (Fodor
1983). What also warrants emphasis is that localizing signs of this
sort emerge most clearly in "on-line" analyses (see Zurif &
Swinney, in press, for a detailed discussion of this last point).
In any event, Farah's test-case "modules" seem to be isolated
as a means of redescribing patterns of sparing and loss following
brain damage, and that does not guarantee the linchpin characteristic
of a module, namely, its encapsulation. Evidence for
encapsulation should emerge as a result of charting mandatory
and fixed operating characteristics of one or another part of a
system. From a processing perspective — and since she cites
Fodor on the definition of a module, this seems to be Farah s
perspective as well - a module is informationally encapsulated
only over the time course of its operation. Whether modules of
this sort have local or widespread effects when damaged is a
matter that should not be stipulated in advance of actually
measuring the consequences of their disruption.
Author's Response
Interactions on the interactive brain
Martha J. Farah
Department of Psychology, University of Pennsylvania, Philadelphia, PA
19104-6196
Electronic mail: mfarah@cattell.psych.upenn.edu
R1. Modularity, the locality assumption and
neuropsychology
R1.1. Implications for modularity. Many of the commentaries
touched on the issue of modularity. Four main
points were made. First, several commentators noted
that my alternatives to modularity are themselves modular,
in the sense of having components that represent
different kinds of information. For example, Servos &
Olds state that I seem both to reject and accept the
concept of modularity; they quote my statement that "it is
well known that different brain areas are dedicated to
representing information from specific sensory and motor
channels." Young quotes this same passage and says "This
is locality without invoking the label." Butterworth also
notes the apparent inconsistency and asks whether I
believe there are "regional specialties" or just undifferentiated
"mass action." The confusion stems from two
different meanings of the word "modular," which I distinguished
in section 3.3.1. The first meaning is "informationally
encapsulated," and it is this sense of modularity
that is challenged by failures of the locality assumption.
The second meaning is "specialized processors," for example,
those subserving visual and functional knowledge,
and this is not challenged by failures of the locality
assumption. Of course, as Glymour points out in the
second section of his commentary, to the extent that
different modules influence each other, the nature of the
information they represent becomes less distinct. Less
distinct does not mean indistinct, however, and distinctions
that are a matter of degree are not necessarily vague.
Second, it was pointed out by several commentators
that Fodor (1983) restricted his claims of modularity to
peripheral systems, among which he included, for example,
vision and language (Butterworth, Chater, Kinsbourne,
Umilta, Zurif & Swinney), whereas my discussion
of modularity is not so restricted. This is true. Fodor's
main defining criterion for modularity, informational encapsulation,
describes the architectures for which the
locality assumption holds; it was not my intention to
discuss his substantive claims about which systems will
and will not conform to that criterion. Although I think
this is reasonably clear in the introduction (sect. 1.1), I
admit that elsewhere I slipped from what should have
been "the hypothesis that Fodor's definition of modularity
holds for the cognitive architecture" to "Fodor's modularity
hypothesis." Zurif & Swinney offer a further
criticism of my account of Fodorian modularity, claiming
that the difference between modular and interactive systems
turns, not on the amount of interaction, but on when
interactions among constituent processes take place. This
is not consistent with my reading of Fodor (1983), for
example, his statement that in informationally encapsulated
systems, "of all the information that might, in
principle, bear upon a problem . . . only a portion (perhaps
only quite a small and stereotyped portion) is actually
admitted for consideration" (p. 70). Perhaps our views
can be reconciled by noting that holding back sources of
information that could in principle be used by a processing
component until that component has completed its
computations is not different from simply holding them
back forever, as far as that component's behavior (inputoutput
function) is concerned.
A third point concerned the scope and limits of informational
encapsulation. Glymour formulates the issue
clearly, distinguishing among a number of alternative
claims that could be made concerning the encapsulation
of modules and consequent locality of the effects of
damage. There could be locality for the effects of damage
to any one component on any other component (his
Equations 1 and 2), or for the effects of damage to
particular components on particular other components
(Equations 3 and 4), or for the effects of damage to any
component on the functioning of a particular component
(Equations 5 and 6). Furthermore, the locality or nonlocality
of the effects of damage could be measured
relative to the direct input to a nondamaged component
(odd-numbered equations) or relative to the input to the
system as a whole from the environment (even-numbered
equations).
Which of these is the version of locality that I discuss?
Although Glymour suggests it might be (1), it is none of
the odd-numbered possibilities. A violation of this type of
locality would involve a component changing its inputoutput
function, and as Oaksford and Plaut both point
out, this does not occur in any of the examples I discuss.
Nor, I might add, would one ever expect such a change on
the grounds of parallel distributed processing (PDP) or
90 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Response/ Farah: Neuropsychological inference
any other existing proposals for the nature of human
information processing. Plaut phrases this distinction
between odd- and even-numbered possibilities in terms
of the "behavior" (output to other components) versus the
"computation" (output given particular inputs) ofa component,
and correctly states that "clearly the nondamaged
portions of the networks compute normally but behave
abnormally in response to corrupted input from damaged
portions."
Glymour claims my arguments apply only to his version
(2), which would indeed be unfortunate if true,
because it requires absolutely no communication among
components, a nonsensical extreme of informational encapsulation.
Grodzinsky & Hadar and Zurif & Swinney
also point out that even strong modularity requires some
intermodule communication if the system is to do anything.
I agree, and the distinction proposed in the target
article is between architectures in which there is abundant
versus minimal intercomponent communication
(e.g., sects. 1.1, 1.3). This quantitative distinction is
important for the kinds of qualitative inferences we draw
about the cognitive architecture from patients' behavior. I
will review the reason for this claim in the context of
Glymour's discussion of the Farah and McClelland (1991)
model of semantic memory.
Glymour correctly points out that the violated version
of the locality assumption in this case is of type (4), but he
says that this is not interesting for two reasons. Let me
first dispense with the second reason, that the behavior of
the model is "obvious from [its] functional structure." The
same point was raised as a criticism by Diederich, who
complained that "the effect of damage to the networks can
easily be explained by the network structures." This line
of criticism strikes me as bizarre, because it suggests that
it is not desirable for theories to explain phenomena too
plainly. It is also ironic in the present case because PDP
models have recently been criticized on the grounds
that, although they may account for the data, the way they
do so is frequently obscure (McCloskey 1991).
As his first reason for finding violations of type (4)
locality uninteresting, Glymour states that no one held
contrary views about the encapsulation of the particular
modules in question. If this were true, then I agree that
this example would not represent a failure of locality in
any interesting sense. However, the most straightforward
account of how functional semantic information is accessed
through a verbal query involves communication
between verbal systems and functional semantics, not
communication between visual and functional semantics.
This is the belief concerning encapsulation that is violated
in our account. In this sense the account is contrary to
accepted or default views.
A fourth point in the commentaries concerning modularity
is that modular architectures may also exhibit
nonlocal effects of local damage. There are two ways that
this might happen. One way is discussed by Plaut and is
closely related to the previous point, that informational
encapsulation is a matter of degree. Plaut explains that
components will behave abnormally, given abnormal input,
whether they are in a modular or an interactive
architecture. Of course, components will less often receive
abnormal input following local damage in modular
architectures, because in general their components have
relatively few sources of input. Plaut questions whether
the locality versus nonlocality of the effects of brain
damage per se is the key distinction that neuropsychologists
should consider, as opposed to interactive versus
modular architectures. These appear to metobe different
formulations of the same distinction, and in fact the title
and text of the target article address both. Each formulation
has the disadvantage that it requires us to rule out a
silly version: the "silly locality assumption" is violated by
any change in behavior of any nondamaged component,
including the relatively small number of downstream
components in a modular architecture. The corresponding
"silly modularity hypothesis" is that components are
not just encapsulated from most other components, but
from all other components.
In contrast to effects of local damage on the small
number of downstream components in a modular architecture,
Semenza and Chater point out that such an
architecture could manifest nonlocal effects of damage by
compensatory strategy shifts. Chater offers the example
of a subject who, after losing his lexical route to reading,
might rely on phonological and semantic routes that were
not previously used. In such a case the output of nondamaged
components is not changed; rather, the components
whose outputs control behavior have changed. To
the extent that we have prior knowledge of the components
involved (as we do with semantics and phonology)
and to the extent that our methods allow us to identify
the components whose outputs are controlling behavior
(which, again, is the case for this example), this type of
nonlocal effect will be more tractable within an assumed
modular framework than the violations of the locality
assumption which were the focus of the target article.
R1.2. Is the locality assumption ever right? Many commentators
saw the need to emphasize more strongly than
I had done that the locality assumption may be right in
some cases. I agree with this, and would like to distinguish
two ways in which it is true. First, as stated in
sections 1.4 and 3.3.3, there may be some cognitive
domains in which the locality assumption generally holds
true. Second, even in domains in which it does not
generally hold true, there may be many specific instances
in which it is not violated. Note, however, that, in the
latter case, we would not want to say the locality assumption
is true, any more than we would want to say the
assumption that cats are black is true just because some
cats are black. My goal was to argue that as a general
assumption, the locality assumption is wrong.
For example, Butterworth points out that although
some abnormal performances are best explained using
the assumptions of PDP as opposed to the locality assumption
it does not follow that all are. This is true, but
not a criticism of my position. Similarly, Young offers
counterexamples to the claim that everything interacts
with everything, citing as an example the fact that language
impairment does not affect toe wiggling. The claim
that is up for discussion is a different one, however: that
many things interact with many things, including things
that are not logically necessary or intuitively relevant,
such as the interaction between visual and functional
semantics when functional semantic information is being
accessed from a verbal query.
Grodinsky & Hadar draw a line between domains that
might be compatible with PDP, and at least one domain
BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1 91
Response/Farah: Neuropsychological inference
that they view as surely incompatible, namely, language.
They contrast this position with an inaccurate characterization
of my own: "Farah's claim . . . is made as if all
cognitive domains were alike (at least with respect to
modularity)." As I said in the target article, it is indeed
possible that some domains, such as language, will conform
to different information-processing principles. On
the substantive issue of whether interactive or encapsulated
accounts of language are correct, and the consequent
validity of the locality assumption in neurolinguistics,
I differ from these commentators only in being more
agnostic than they appear to be on the basis of currently
available evidence.
R. Campbell emphasizes the heuristic role of the
locality assumption in neuropsychology as a reason to
retain it. Hypotheses about dissociations have to come
from somewhere, and the locality assumption can provide
a good starting point. I agree, although the problem
remains that this heuristic will bias us toward noninteractionist
hypotheses. Carey & Milner view this as an
acceptable risk for neuropsychologists working on vision,
because of independent evidence that the visual system
has a modular organization. There is certainly abundant
evidence for modularity in the sense of specialized functions
(see sect. Rl.l), but there is also evidence of significant
interactivity, particularly among the systems
involved in visual attention (e.g., the competitive phenomena
alluded to by Kinsbourne). McCarthy suggests
that one's a priori conceptions of cognitive or perceptual
"domains," such as faces and animals, can also be a
heuristic in formulating hypotheses, so that one is not a
slave to the locality assumption. I agree with this too,
although it is no panacea because our conceptions of
domains are not guaranteed to be correct, and indeed
often rely on prior locality assumption-based neuro-
psychology!
The truth of the locality assumption is clearly an empirical
issue, but as I pointed out in the target article (sect.
1.3), it is not one that lends itself to a single critical
experiment. Rather, it can be decided only by evaluating
the whole body of known neuropsychological phenomena
with respect to alternative explanations that involve modular
and interactionist architectures. Because neuropsychologists
have only recently begun to consider the
latter kinds of explanations, and because we lack good
heuristics for generating such explanations, we may be in
a state of uncertainty for some time. The current evidence
seems to bracket the likely answer somewhere between
the extremes of"local damage always has local effects" and
"local damage never has local effects." How often the
locality assumption is right and whether there are certain
domains where it is most likely to be right are important
open questions. Finally, it is worth noting that progress
on these questions will be closely coupled with progress
on questions of interactionist versus encapsulated architectures
for explaining normal cognition, questions that
have occupied many of the finest minds on both sides of
the issue. With respect to the present commentaries,
work such as that described by J. Campbell, Clark, and
Sekuler suggests a narrower rather than a wider range of
applicability of the locality assumption. Physiological
studies of normal brains are also relevant, and the evidence
cited by Posner favors the locality assumption in
the case of disengaging attention.
R1.3. Straw man characterization of neuropsychology?
Although many commentators explicitly granted that the
locality assumption is ubiquitous in neuropsychology,
some disagreed with this generalization. Semenza states
that "at the present time, nobody would subscribe to the
locality assumption as Farah seems to intend it," •
Grodzinsky & Hadar say they "do not believe there is
even one 'modularist' who would subscribe to it," and
Butterworth can think of "no one who has maintained, in
print, that all components of the brain's functional architecture
are informationally encapsulated." They go on to
highlight the implausibility of the locality assumption,
making a compelling case that no sane neuropsychologist
would hold this assumption and that the type of neuropsychology
I discuss must therefore be a "straw man."
These commentators are probably right that most neuropsychologists
would hesitate to endorse a bald statement
of the locality assumption and the generalized
informational encapsulation that is entailed by it. The
relevant issue, however, concerns whether the research
practices of these same neuropsychologists implicitly depend
upon the locality assumption. There are undoubtedly
many unexamined background assumptions in psychology
and some do seem utterly wrong when stated
explicitly and taken to their logical conclusions (e.g.,
recall the unpalatable implications of the "language of
thought" hypothesis discussed by Fodor, including the
conclusion that most concepts, including "trumpet," are
innate). My claim is that the locality assumption is widely
used in neuropsychology, however uncomfortable some
neuropsychologists might be when confronted with an
explicit statement of it, and in support of this I offered a
variety of examples of research findings whose accepted
interpretations hinge on the locality assumption. Let me
add that these examples were chosen because they are, in
my eyes and in the eyes of the field, examples of excellent
and highly respectable neuropsychological research, not
straw man examples.
Burton & Bruce point out that a growing number of
neuropsychologists have found alternative means of interpreting
their data without the locality assumption, using
all or just some of the principles of PDP. Happily, this is
true! Nevertheless, these cases remain very much the
exception rather than the rule. It seems unfair to suggest
that "in (at least) the case of covert recognition in prosopagnosia,
Farah seems to have focussed selectively on an
example of 'old-fashioned' cognitive neuropsychologising."
The "old-fashioned" theory to which they refer bears
a 1992 publication date and resulted from the collaboration
of two of the leading groups working on covert
recognition (de Haan et al. 1992). This hardly constitutes
picking on a straw man.
Carey & Milner suggest a different way in which I may
have portrayed neuropsychologists as less prudent than
they really are. They contend that neuropsychologists do
not draw inferences about the normal cognitive architecture
from dissociations, contrary to my description of
cognitive neuropsychology. Rather, neuropsychologists
are led to propose hypotheses on the basis of dissociations,
which must then be tested with new data, neuropsychological
and otherwise. The distinction here between
data that suggest hypotheses and data that test
them seems difficult to sustain. For example, what if a
dissociation is observed after a certain hypothesis about
92 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
Response/Farah: Neuropsychological inference
the cognitive architecture has already been suggested by
some diflerent data? Do we then describe our change of
attitude toward that hypothesis in the light of the new
dissociation as "making an inference" from the new dissociation?
Surely we are at least making an inference about
the likelihood that the hypothesized architecture is correct,
which is really all we are ever doing, although in
some cases these probabilities are higher than in others.
In the above case, however, can we not also infer something
about the likelihood of a given architecture on the
basis of the dissociation that also suggests it? It seems
clear that we can, and do. Imagine that we do not know
about any of the converging evidence gathered by Milner,
Goodale, and others for the architectural distinction between
visual recognition and visuomotor guidance (e.g.,
Goodale et al. 1991) and we are offered a bet concerning
whether these two functions are subserved by distinct
systems. Perhaps one would not hazard a large sum on the
existence of the two systems, even if the potential pay-off
was great, but one would certainly be more inclined
toward the bet if one knew about the dissociation shown
by Goodale et al.'s (1991) case DF.
Although I do not concede Carey & Milner's point
about neuropsychological inference - I have just argued
that we can and do draw inferences about the cognitive
architecture on the basis of dissociations - I certainly
grant them the importance of continued testing of our
inferences or hypotheses. In addition, I agree that in
some cases new tests will reveal when an inference based
on the locality assumption is wrong. However, we cannot
wait for all the relevant evidence that could possibly
arrive between now and the end of time and then draw our
conclusions. We are working "on-line," and a strong and
well-documented dissociation in even one patient is often
grounds for an inference. The following question is therefore
still relevant: Should we make inferences using the
locality assumption?
R1.4. Speaking of straw men .. . Some criticisms were
directed toward ideas that are either very distorted or
extreme versions of what I presented in the target article,
or are explicitly denied in the target article. For example,
Young correctly identifies the key issue as being whether
interactions modulate system behavior at what he terms
the "coarse grain" level of cognitive-psychological description,
but he directs his critique at my alleged failure
to seek evidence on the issue, saying "the target article
treats this issue as if it could be determined by theoretical
fiat." I direct the reader to section 1.3 to see that this is
precisely the opposite of my position.
Servos &'Olds say that my arguments "preclude much
if not all neuropsychological research," and imply that
neuropsychology is "futile." Whereas I certainly believe
that abandoning the locality assumption complicates life
for neuropsychologists, one of the main points of the
target article is that neuropsychology can be done without
the locality assumption. At the root of this difference may
lie another more general difference between their reading
of the target article and the intended meaning. They
take the main issue to be localization of function, not
identification of what the functions are; and they further
adopt the following criterion for localization of function:
"If a functional deficit frequently (or always) arises following
damage to one brain region, and not when damage
occurs to other brain regions, it seems reasonable to
assign a critical role to that brain region in the processes
underlying that function." This is analytically true, because
of what it means to play a "critical" role, and I would
not dream of arguing against it. Had I argued against it,
however, I would understand why someone would think
me pessimistic about the prospects for neuropsychology!
Butterworth characterizes the target article as an attack
on both Shallice and Caramazza. The target article attacks
the locality assumption. Although I maintain that most
neuropsychologists have used the locality assumption,
including myself as well as Shallice and Caramazza, neither
of the latter specifically champions it. Section 1.1 of
the target article reviews the relationship between certain
published statements of their methodological precepts
and the locality assumption.
R2. Problems with PDP
I use PDP as an alternative set of working assumptions in
place of modularity in neuropsychology. To the extent that
PDP yields more sensible, parsimonious accounts than
modular accounts (and, eventually, confirmed predictions),
this lends support to PDP as a description of
human information processing and its neural implementation.
However, many commentators found PDP so
questionable as to be dangerous to use even in this
relatively agnostic way.
R2.1. Constraining PDP. One criticism is that PDP models
are too unconstrained to be explanatory (Bullinaria, Burton
& Bruce, R. Campbell, Carey & Milner, Grodzinky
& Hadar, van Hezewijk & de Haan, Kinsbourne, Small).
For example, Carey & Milner point out that networks are
powerful enough to do all kinds of things that may be
remote from what the brain does and how it does it. Van
Hezewijk & de Haan suggest that, for this reason, PDP
models will have to be parasitic on common sense and
prior theoretical ideas to confer substantive theoretical
content to them. Small captures a key idea behind these
worries when he likens PDP to a language for describing
theories, one that is not in itself true or false. With due
respect, this key idea is wrong! The principles summarized
in section 1.4 are empirical claims, which could be
true or false. Furthermore, any models that incorporate
these principles are constrained by them. For example, a
model that has distributed representations will show
generalization and cross-talk, both psychologically relevant
model properties, whether the modeler wants them
or not. Likewise, interactivity commits the modeler to
nonlocal effects of local damage.
Although PDP is not a neutral, general-purpose modeling
medium but constrains models in ways that affect their
ability to account for psychological phenomena, it is also
only one source of constraint. In this sense, commentators
such as van Hezewijk & de Haan are right in stating
that PDP models must also incorporate ideas external to
PDP, from common sense or psychology. For example, in
the semantic memory model, we imposed the additional
constraints that there are modality-specific forms of semantic
knowledge and that vision and language each
interact with semantic knowledge but do not interact
directly with each other (in other words, one cannot name
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Response/Farah: Neuropsychological inference
something one sees without knowing what it is). This does
not make PDP models, in van Hezewijk & de Haan's
words, "ad hoc." Models are supposed to incorporate
theoretical ideas. Indeed, incorporating theoretical ideas
that have some independent motivation, as opposed to
tailoring the model just to fit the data, keeps models from
being ad hoc. Furthermore, it seems unfair to say that
"PDP modelers just ask themselves: 'What is the next
phenomenon to model?' whereas (realist) symbolic modelers
would continue: 'So what are the predictions from
this model and how can I test them?'" On what do the
authors base this? Although the generation and testing of
new predictions is less common than one might like with
all types ofmodels, there are numerous examples of PDP
models that have motivated new empirical research. For
example, the McClelland and Rumelhart (1981) interactive
model of context effects in letter perception led to
new empirical tests of the model (Rumelhart & McClelland
1982). The Seidenbergand McClelland (1989) model
of word reading has motivated a series of new studies of
reading in normal humans (Jared et al. 1990). PDP
models and associated hypotheses are on at least equal
footing with other hypotheses in neuropsychology with
respect to their risk of being ad hoc. If anything, the
principles mentioned in section 1.4 add additional constraints
to PDP models.
Kinsbourne suggests that a specific way to increase the
constraints on PDP models would be to require them to
account for quantitative as well as qualitative aspects of
the data. Although more specific predictions are ofcourse
desirable, this does not negate the value of achieving
qualitative predictions. Furthermore, qualitative and
quantitative predictions are on a continuum, and although
most PDP models do not capture the precise
values, distributions, and so on, of the dependent measures,
they often predict some quantitative characteristics.
For example, the model ofsemantic memory impairment
predicts that more pronounced dissociations should
be observable with living than with nonliving things
(compare Figs. 3A and 3B) and that the dissociation
between retrieving functional knowledge of living and
nonliving things should be smaller in a given patient than
the dissociation in other measures ofknowledge (compare
Figs. 3a and 4). The model of impaired attentional disengagement
predicts the quantitative pattern of the four
relevant means (Fig. 9). The model of covert recognition
predicts not only that covert recognition will be partially
preserved after damage to the visual face-recognition
system but that it will remain relatively preserved at
levels ofdamage at which overt recognition is close to or at
chance (compare Fig. 12 and Figs. 13-15). Finally, it
should be pointed out that this comment, too, applies
equally well to non-PDP hypotheses in neuropsychology.
We typically predict differences in a given direction, or
patterns of means, but not precise effect sizes.
Kinsbourne also suggests that as long as the models are
qualitative, they are superfluous: "The idea does all the
work." It is of course true that the models are only of
interest as tools for developing and testing hypotheses,
but they are important tools. Some network behavior can
be reliably intuited without simulations, and indeed Kinsbourne
has been doing this since pre-PDP modeling days
(e.g., Kinsbourne 1977). Nevertheless, not everyone for
whom the ideas are relevant has developed the necessary
intuitions. In addition, intuition can handle only limited
complexity, and even in simple cases it can be wrong!
Bullinaria proposes ten additional constraints on the
way PDP models should be used in neuropsychology.
This list raises interesting and important issues for modelers
to consider, and any model that satisfied all of these
constraints would certainly be admirable. However, it
would be wrong to dismiss a model simply on the grounds
that it fails to satisfy some of them. Models should be
evaluated with respect to the question we want to answer
with them. So, for example, if we have a question about
the computational pressures toward division oflabor in an
architecture, then Bullinaria's rule 3 is relevant. If, however,
our question is the more standard one in neuropsychology,
specifically, Could an architecture with suchand-such
components in such-and-such a configuration
account for the observed dissociations? then insistence
that the architecture be learned is gratuitous. Similarly,
although I agree with Bullinaria, Shallice, and the many
other writers who have pointed out that strong double
dissociations provide the clearest evidence concerning
the normal architecture, I do not agree with rule 1 that
other types of dissociation or even associations are not
worthy ofmodeling. Ifone wants to understand a particular
system, one will work with whatever evidence is
available about that system and one will simply be mindful
of the alternative explanations permitted by it.
R2.2. What parts of PDP are doing the work? It is pointed
out by Burton & Bruce that the different principles of
PDP are to some extent separable. Theses commentators
question the value of distributed representation, asking
what explanatory work distributed representation does
and whether the choice of a specific type of distributed
representation or combination of distributed and local
representation, rather than the general principle of distributed
representation, is what makes the models work.
They also complain that distributed representations are
inherently difficult to interpret and that their units have
no referents, lending "mystique" but not clarity to the
models. I maintain that the concept of distributed representation
does explanatory work and is far less mysterious
than Burton & Bruce seem to think.
First, a point ofclarification: the units of both local and
distributed representations have interpretations. In a
local representation, the referent is some item in the
represented domain. In a distributed representation it is
some "microfeature" (Hinton et al. 1986) of the items,
which may or may not correspond to a nameable or
intuitive feature. Another way of expressing this is that
any unit has a meaning in the sense of some extension in
the represented domain. Thus, semantic knowledge in
the Farah and McClelland model is indeed distributed. It
is even distributed in the model ofcovert face recognition,
as "actor" and "politician" are features of the semantic
representation of people. (Of course, the representation
ofoccupation is local; whether a representation is local or
distributed can only be defined relative to what it is
representing.) Location is clearly local in the model of
visual attention, but could be (and we hope eventually
will be) distributed.
What explanatory work does distributed representation
do? It seems clear that the distributedness of the
semantic representations across visual and functional
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knowledge is a key constituent of our account of impaired
functional knowledge of living things. What about the
covert recognition model? Burton & Bruce, as well as R.
Campbell and Young, compare this model to an earlier
interactionist model of covert recognition proposed by
Burton et al. (1991), which used local representation. The
contrast is helpful in bringing out the role of distributed
representation. Burton et al.'s model accounted for priming
effects, one of the three types of covert recognition
effect described in section 2.3.1. Both models account for
this effect in the same way, by subthresliold activation of
units downstream from the visual face-recognition system.
The PDP principles that are doing the explanatory
work here are graded representation and interactivity.
However, the model with distributed representation can
also account for the two other qualitatively different types
of covert recognition effect, which the local model does
not address. By allowing for partial damage to the visual
representation of all faces, distributed representation
makes it possible to account very naturally both for
savings in relearning and for the preservation of the
perceptual processing advantage for familiar faces. In fact,
the use of distributed representations even allowed our
model to account more fully for the priming data; the
observed asymmetry between interference and facilitation
emerges naturally from the influence of other parts of
the distributed representation on the activation of the
occupation features in our model. (For further discussion
of the relations between the two models, see Farah et al.
1993.) In response to the question of whether these
advantages derive from distributed representations in
general or the specific set used in this model, no special
tailoring was needed to obtain these findings; for both the
semantic memory model and the covert recognition
model the architectural assumptions were quite minimal
and the representations themselves were generated
randomly.
The fact that all three of these qualitatively different
covert recognition effects were accounted for by the
properties of distributed representation in a single fairly
simple model supports the explanatory value of distributed
representation. It also counters Burton & Bruce's
charge that the use of PDP in neuropsychology represents
punctate modeling of isolated phenomena.
Chater raises a similar question about interactivity. He
points out that many of the connectionist models used in
cognitive psychology and neuropsychology are feedforward
models in contrast to the three recurrent models
featured in the target article. Perhaps it is not interactivity
per se but other aspects of PDP models that are responsible
for their success. It is true that many PDP models are
feedforward, although this is often due more to the
feasibility of training recurrent nets than to a principled
choice. Nevertheless, it is fair to ask: Does interactivity
deserve any credit for simulating the phenomena of interest?
In the semantic memory model, the interactions
among the different parts of the representation are critical
for producing an impairment in functional knowledge
when visual knowledge is damaged. In the attention
model the inhibitory interactions between the attention
units and the recurrent connections from attention units
to perception units are also critical. In the model of covert
face recognition, the simulation of at least some of the
phenomena depends on the network having attractor
states. Finally, the Hinton and Shallice model mentioned
by Chater also has recurrent connections, which are
important in the genesis of its error patterns.
R2.3. Levels of analysis. The general concept of levels of
analysis came up in a number of commentaries, frequently
with the suggestion that PDP's apparent superiority
to modular accounts hinges on a confusion between
levels of analysis. Two rather different senses of the
phrase "levels of analysis" are used in these commentaries.
In some cases (Chater, McCarthy, Young) it refers
to the "grain size" of an account of causal mechanism.
Young makes an analogy between the interactivity of
neural information processing and cognitive functioning
on the one hand and interactions between molecules in
the air and global atmospheric phenomena on the other.
Young's analogy is in many ways insightful and helpful in
clarifying the crucial issue. The analogy makes clear that
causal mechanisms can be described at each level of
analysis, fine-grained and coarse-grained. It also implicitly
poses the key question: How autonomous are the
coarse-grained accounts of mechanism with respect to the
fine-grained ones? According to Young, the answer, with
respect to molecular and atmospheric phenomena, is that
the coarse-grained level is autonomous. Weathermen do
not have to know about people's breathing patterns because
small local pressure changes become undetectable
over meterological distances. Young's analogy, however,
serves as an argument against interactionism in neuropsychology
only if we assume that the answer for one type of
system and set of levels is the same for every other. This is
clearly not true. Even if Young's analysis of atmospheric
behavior is correct, it remains an open empirical question
whether the interactivity that he grants is present at he
fine-grained neuronal level will also affect behavior at the
coarse-grained level of neuropsychological phenomena.
Far from claiming to settle this issue by theoretical fiat,
the clearly stated goal of the target article was to address
this empirical issue by comparing mechanistic accounts of
neuropsychological deficits based on PDP with accounts
based on assumptions of minimal interactivity.
McCarthy makes a point similar to Young's, when she
says "the fact that the brain is a complex biological system
that shows nonlocal effects when injured does not necessarily
entail that cognitive theories must mirror this interactivity.
(For example, in the case of blood flow, hyperperfusion
in the region of an infarct does not mean that the
damaged areas of brain are contributing more to the
cognitive performance of the system.)" Although facts
about brain function are clearly more relevant to this
empirical issue than facts about other systems such as the
atmosphere, the particular counterexample chosen by
McCarthy does not concern cerebral information processing
but cerebral haemodynamics. Blood flow can be used
as an index of regional cerebral information-processing
activity, but no one would mistake it for a mechanism of
information processing.
"Levels of analysis" was also used by Oaksford to refer
to a different distinction, which also appears in Mesulam's
framework for understanding attentional impairments.
This is the distinction between the description of behavior
(normal or pathological) and a causal mechanism to account
for the behavior. Oaksford claims that the description
of behavior, which he calls a "computational" acBEHAVIORAL
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count, is the proper subject matter for box-and-arrow
models, as tempting as it may be to ascribe causality to
these models. For example, he proposes a box-and-arrow
model for semantic memory impairments with one lesion
in the visual semantics box and a second lesion in a box
labeled "functional semantics for living things." He points
out that such a model "does appropriately summarise the
patients' pattern of deficit at the computational level.
And, of course, the computational level does not specify
how a function is to be implemented. (Note that because a
task is decomposed as requiring two functions to be
computed, this does not mean that, ipso facto, two anatomically
distinct causal mechanisms are required for
their computation.)"
It would be folly to think that lesions to a cognitive
mechanism would have local effects on behavior in the
sense of being local to behavior in some task. This would
require a one-to-one mapping of task-defined abilities and
components of the cognitive architecture, a possibility
that Mesulam correctly dismisses in his discussion of the
mapping between behavioral and computational "planes."
Rather, the locality assumption concerns the relation
between lesions and their effects on nonlesioned components
of a causal mechanism. The distinction can be
illustrated using Grodzinsky & Hadar's discussion of
phonological dyslexia. They state that in this case the
locality assumption implies the existence of a component
dedicated to reading nonwords. As described in section
1.2, the locality assumption implies the existence of a
grapheme-to-phoneme translation mechanism. Nonword
reading is a task-defined ability; grapheme-to-phoneme
translation is a more plausible candidate for a component
of the cognitive architecture, used during the reading of
both words and nonwords.
Van Gelder identifies the erroneous assumption behind
Grodzinsky & Hadar's reasoning as "the other locality
assumption" - that for every task-defined ability
there is some dedicated component of the cognitive
architecture. Van Gelder suggests that many neuropsychologists
hold this assumption as well as the first
locality assumption. I think this is not quite fair. Although
psychologists may sometimes have too much faith that
their tasks effectively isolate and test a single underlying
cognitive component, they are generally aware that the
relation between tasks and components is potentially
complex and as neuropsychologists they take themselves
to be studying the loss of components rather than taskdefined
abilities.
R2.4. Biological realism of PDP. Several commentators
discussed the biological realism of PDP models. Some
found the glass half empty, others found it half full.
Mesulam argues that PDP captures important features of
brain functioning. Wasserman appears to agree, although
he points out that the functioning of individual neurons
may be much more complex than the units of PDP models
suggest. In particular, he suggests that features of distributed
representation at the network level may also be
found at the individual neuron level. Carey & Milner also
see PDP models as a step in the right direction, but they
express concern over the large proportion of biologically
unrealistic features of these models. As an example, they
focus on the back-propagation learning algorithm (which
was not, in fact, used in any of the three models of the
target article), pointing out that it is very implausible as a
model of real learning in the brain. Van Hezewijk & de
Haan make the same point. This is, of course, true, and
has motivated many modelers to explore more biologically
plausible learning algorithms. But even this glass is
at least a quarter full: in many cases, including the first
two models of the target article, one is not interested in
modeling learning per se, and the so-called learning
algorithm is just used to set the weights in the network so
that it will perform the tasks of interest. The term "learning"
has irrelevant psychological connotations in these
cases and it might be less confusing to call such algorithms
"weight-setting algorithms." Unless there is some systematic
relation between the way the necessary weights
are found and the aspects of model performance under
study, which in general we have no reason to expect, it is
harmless to use unrealistic learning algorithms.
In the first of their cautionary remarks, Humphreys &
Riddoch point out that in order for components to be
separately lesionable, they must be anatomically separate.
They see this as incompatible with the connectivity
hypothesized in the models of the target article because,
in their words, "only systems that are anatomically proximal
may develop functional interconnections." Although
it is certainly true that short-range connections are more
abundant than long-range connections, as argued in the
anatomical and computational references they cite, it is
also true that there are functionally important long-range
connections. To mention just a few well-worked-out examples,
consider Goldman-Rakic's (1987) findings on the
anatomy and function of the circuits linking prefrontal
cortex to parietal and temporal cortices, the corticalhippocampal
circuitry involved in learning and memory
(e.g., Squire 1987), and indeed the findings from animals
and humans on the circuitry of attention described by
Mesulam and Posner.
Small points out that I have not availed myself of
potentially important clues to the nature of patients'
deficits from lesion location and etiology. In fact, with just
the set of patients to whom Small refers, my colleagues
and I have used neuropathological information as one
source of evidence about the functional nature of the
deficit (Farah et al. 1991, pp. 191-92). However, the
inclusion or omission of such evidence does not seem
directly relevant to the biological plausibility of PDP, nor
to the issue of whether interactionist accounts are more
appropriate than modular ones. Beyond this, I find little
on which to disagree with Small. The brain reportedly is
grey, wet, and slippery. Furthermore, most of Small's
brief overviews of localization in neurology, history of
PDP versus Von Neumann architectures, and so on,
sound right to me. This leaves me wondering what the
"missing neurobiological and computational links" are
that weaken my arguments in his view.
Diederich criticizes PDP models on the grounds that
they fail to incorporate many known features of brain
function, such as the structure of different types of neurons,
their patterns of connectivity, their sheer numbers,
and so on. I would certainly not argue against striving for
more biological realism in PDP models. However, it
would be hasty to conclude that the kinds of models
discussed in the target article are worthless or misleading
because they fall short of full biological realism. It is
a commonplace that models have theory-relevant and
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theory-irrelevant attributes. It is also rather a cliche that
science must often simplify nature in order to understand
it. PDP models should be viewed as simplifications of the
brain, having enough theory-relevant attributes of the
brain to be informative on many questions but clearly
leaving out or even contradicting many known aspects of
brain function.
Among the theory-relevant aspects of PDP models are
the use of distributed representations, which have been
identified in numerous brain systems (e.g., Sparks et al.
1990; Young & Yamane 1992), the large number of inputs
to and outputs from each unit, the modifiable connections
between units, the existence of both inhibitory and excitatory
connections, summation rules, bounded activations,
and thresholds. PDP models allow us to find out
what aspects of behavior, normal and pathological, can be
explained by this set of theory-relevant attributes. Of
course, some behavior may be explainable only with the
incorporation of other features of neuroanatomy and neurophysiology
not currently used in PDP models. This
seems quite likely, and the discovery of such instances will
be extremely informative with respect to the functional
significance of these features of our biology. However,
note that this problem does not apply to cases in which the
current models perform well. In such cases, the only
danger I can see associated with nonrealism is that the
model's success might depend on a theory-irrelevant
simplification. For example, scale is generally treated as
theory-irrelevant, but it is possible that certain mechanisms
will work only for small networks or small amounts
of knowledge. We must be on the lookout for such cases,
but we must also recognize that, barring a malevolent
god, it is unlikely that the success of most models will
depend critically on their unrealistic features.
R3. Discussion of specific models
R3.1. Semantic memory. Two points are made by Butterworth,
one about the semantic memory model and one
about scholarly credit for the ideas embodied in the
model. Concerning the modality-specific semantic memory
model, he states that it is not "formally different" from
the category-specific alternative, in that there are two
components of semantic memory with different specializations
interposed between various more peripheral systems.
In this sense of "formal" equivalence, he is right.
But this seems a strange criterion for comparing models.
The Ptolemaic and Copernican theories of planetary motion
would also be equivalent by this criterion: there is
one body in the middle with others orbiting around it. In
both cases, the difference in the identity of the "forms" in
the "formal" description makes a big difference! In the
present case, one semantic memory model has categoryspecific
components and the other has modality-specific
components.
Butterworth's second point is that McClelland and I
were saying nothing new in our model of semantic memory
impairment. In support ofthis he furnishes quotations
from the writings of Warrington and McCarthy (1987) and
from Shallice (1988) indicating their use of the idea of
distributed modality-specific representations. Readers of
the target article (sect. 2.1.2) as well as the original report
of the model will see that these contributions were explicitly
acknowledged. What is new in our model, and not a
part of the earlier theorizing, is the idea that any portion
of this representation needs collateral support from other
portions to be accessible. This allows the model to explain
impaired access to functional knowledge of living things
after damage to visual semantics.
Kinsbourne offers an alternative explanation of the
phenomena based on the notion of "usual" versus "unusual"
routes to naming. Although it seems to account for
the data at hand, it also seems to predict the existence of
subjects who are selectively impaired in functional knowledge
of living things, while showing preservation for
visual knowledge of all things (because visual knowledge
is intact) and functional knowledge of nonliving things
(because as a less "unusual" route for nonliving things,
they will require less "functioning territory"). To my
knowledge no such subjects have been reported.
Both McCarthy and Humphreys & Riddoch point out
the existence of patients whose impairment in knowledge
of living things affects only visual knowledge. This seems
to present a challenge to the interactive model, as loss of
visual knowledge should influence access to functional
knowledge. The impairment of functional knowledge,
however, will always be less pronounced than the impairment
of visual knowledge when visual knowledge is damaged.
For example, even when visual semantics is completely
eliminated, model performance with functional
semantics is only moderately impaired (Fig. 4). Therefore,
at low enough levels of damage to visual semantics, a
functional semantic impairment may be undetectable.
Van Hezewijk & de Haan ask whether the semantic
memory model could accommodate the finding of preserved
priming by unrecognized living things. Priming
will be observed any time there is partial representation
of an item within the to-be-primed set of units. Failure to
name living things frequently occurs with partial representation
of the item (for example, with enough features
active to distinguish it from all but one or two of the foils).
Hence the model would not just be able to accommodate
such findings; at all but the most severe levels of damage,
the model would necessarily show priming for living
things that it fails to name.
Clark applauds the distributed and interactive features
of the semantic memory model but expressed disappointment
that it retains the distinction between visual and
verbal input/output representations, on the one hand,
and specifically "semantic" representations on the other. I
agree that one of the appeals of viewing knowledge as
distributed across multiple brain systems is that the ensemble
of specific types of representations could function
as "semantics." Our model is consistent with such a view if
one interprets the semantic layer as containing the relatively
more abstract components of the visual and motor
systems, which are nevertheless part and parcel of those
systems. However, we did not really attempt to do justice
to this interesting idea, because our goal was to account
for the finding of impaired functional knowledge about
living things.
R3.2. Disengagement of attention. Posner raises a number
of challenges to the Cohen, Romero, and Farah model
of attentional disengagement, whose goal was to explain
the "disengage deficit" without a dedicated "disengage
component." Posner marshals data from split-brain and
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Response/Farah: Neuropsychological inference
parietally damaged patients, positron emission tomography
(PET) studies of normal humans, and single-unit
recording studies of monkeys, none of which our model
currently accounts for. I will review each of these and
discuss whether a suitably updated model could account
for them without becoming grossly ad hoc.
The finding concerning visual search in split-brain
patients is not in conflict with the basic idea of the model
but only with an incidental feature ofits implementation,
specifically, the use ofjust two location representations.
We do not wish to claim that the competitive interactions
underlying the allocation of attention are confined to
those between the left and right visual fields. Although
only two locations were represented in the model, this is a
simplification of an array of numerous units with topographically
organized receptive fields. In this hypothetical
model, severing the inhibitory connections between
the representations of two regions of space would be
expected to end cross-region attentional interactions but
would leave the within-region interactions essentially
unchanged. This is what was found with split-brain patients.
Posner also raises the question of whether the
parietal lobe controls the allocation of attention to particular
locations in space, or whether it also controls
the ability to disengage attention in order to move it
in the contralateral direction. Although there are conflicting
data about this (e.g., the Corbetta et al. 1993
study cited by Posner found evidence of location-based,
not direction-based, attention), it is certainly true that
the current model would not be able to account for
phenomena involving directional attention. However,
the basic idea ofcompetitive interactions between different
possible attentional allocations could in principle be
extended to competition between directions of attentional
movement.
Posner describes a recent PET study of visuospatial
attention in which parietal activation was found during
shifts ofattention from one lateral position to another but
not during static attention to the central visual field
(Corbetta et al. 1993). On the face of things, this disconfirms
our hypothesis that the parietal lobe subserves
attention per se, rather than its disengagement. However,
as Posner acknowledges, the result does not necessarily
indicate the activity of a "disengager"; it could
reflect the movement of attention.
Admittedly, all of these responses to the evidence
reviewed by Posner involve various adjustments to the
model or alternative interpretations of the data. Nevertheless,
I think it is fair to say that none ofthe proposed
adjustments or reinterpretations are outlandish, and
therefore none ofthefindingsdiscussed so far definitively
rule out the Cohen et al. hypothesis. Alas, thefindingsof
Robinson et al. (1991) pose a more serious challenge. He
has recorded from parietal cortex in monkeys performing
the Posner task, and found that some cells respond primarily
when attention must be shifted from a distant
location to the cell's receptive field. This is exactly how
one would expect a "disengager" to act if one were
recording from it. We await the full report of this conference
abstract and recognize that in the light of this and
possibly other results cited by Posner, our explanation of
the disengage deficit may be wrong.
Finally, Posner makes two more general points that
deserve comment. The first is that his own theorizing
about attention involves a distributed circuit, not a local
center. This is true, and serves to raise an interesting
distinction between different types of network hypotheses.
One can imagine a circuit comprised of numerous
encapsulated components, each computing its function
on the basis of a relatively small number of inputs, and
afterward sending just one discrete output to some small
number ofrecipient components. This would be a distributed
circuit, but diametrically opposed to the PDP networks
described in the target article. The network theories
of many neuroscientists such as Posner, Mesulam, Heilman(e.g.,
Heilmanetal. 1985), and Goldman-Rakic(e.g.,
1987) do not make clear which type ofnetwork is hypothesized.
In none of these cases, however, are principles of
PDP, such as interactivity or distributed and graded
representation, called upon to do explanatory work. The
second general point raised by Posner is that a combination
of methods, including testing ofclinical populations,
brain imaging of normals, and when possible, animal
experimentation, provides the most solid base for theorizing.
I have always agreed with this, and seeing what new
light can be shed upon the mechanisms of attentional
disengagement in this manner reinforces my enthusiasm
for converging methods.
In contrast to Posner, Kinsbourne endorses the Cohen
et al. (in press) model of attentional disengagement, and
traces the key idea ofcompetitive interactions back to his
own theorizing of twenty years ago. My colleagues and I
acknowledge his seminal idea in the original article and
are happy to do so here as well.
Humphreys & Riddoch also wish to go on record as
having questioned the need to hypothesize a distinct
mechanism for disengaging attention. They suggest, however,
the need for some mechanism used in disengaging
attention but not for orienting it.
Umilta argues that visual attention is already known to
involve interactivity, so that further demonstrations do
not significantly change our conclusions about modularity
and the locality assumption with respect to the visual
attention system. The interactivity to which he refers is
the influence of conscious volition on the allocation of
attention. The interactivity hypothesized in the Cohen et
al. model is the influence of attention to one stimulus on
attention to other stimuli. Umilta's point is certainly
relevant to the issues of encapsulation and locality, but
given that these issues are matters of degree, it is still of
interest to discover other dimensions of interactivity in
this system.
Umilta also mentions evidence from the hemispatial
neglect syndrome of multiple visual-attention systems,
affecting different coordinate systems (viewer-centered,
environment-centered, object-centered) and different
stimulus types (faces, numbers, the human body). He
suggests that these dissociations call for an encapsulated
account of multiple attentional modules. Although this
may be the correct conclusion, it seems far from irresistible
on the basis ofthe data cited by Umilta. For example,
assuming interactivity between the representation of the
visualfieldon the one hand and both spatial attention and
object representations on the other, as proposed in Farah
(1990, Ch. 6), partial degradation of particular object
representations might be expected to synergize with a
partial unilateral damage to the spatial-attention system
to produce detectable neglect for just certain objects.
98 BEHAVIORAL AND BRAIN SCIENCES (1994) 17:1
R3.3. Covert recognition. Most of the comments on covert
recognition concerned the range of phenomena the
model can explain. In addition to the findings already
accounted for, what other features of prosopagnosia and
covert recognition could be captured by the model (with
modest extensions to simulate the relevant additional
tasks) and what phenomena are, in principle, out of the
model's reach? Davidoff & Renault raise two specific
questions along these lines. First, they point out that
piosopagnosics appear to be impaired in their processing
of unfamiliar as well as familiar faces and that this finding
is inconsistent with localist models of face recognition in
which each familiar face has a local representation. They
suggest that the way O'Reilly, Vecera, and I modeled face
recognition with distributed face representations might
be better able to account for this finding and ask whether
it could be extended to demonstrate this explicitly. In
fact, the model already demonstrates this, in the sense
that its speed of perceptual analysis (settling time) for
unfamiliar faces as well as familiar faces is slowed after
damage. This is attributable to the fact that unfamiliar
faces are represented in the same distributed network as
familiar faces.
Davidoff & Renault also ask whether the model could
be extended to account for psychophysiological measures
of covert recognition involving galvanic skin response
(GSR) and the P300 component of the event-related
potential. Although it is not clear how such phenomena
would be modeled by us, the limitation is not intrinsic to
our model but to the current lack of informationprocessing
interpretations for these psychophysiological
measures. If Davidoff & Renault can give us an explicit
account of how GSR and P300 emerge from network
information processing (analogous to the way in which,
say, naming responses are derived from network behavior
in the simulations we report) then we will be in a position
to test our model against the findings they cite.
Humphreys & Riddoch discuss the relation between
the severity of prosopagnosia and covert recognition and
the ability of the model to account for a lack of correlation.
The most straightforward prediction of our model
is that overt and covert recognition should be correlated,
whereas the alternative model with distinct "facerecognition
" and "consciousness" components does not
predict a correlation. They cite an article by McNeil and
Warrington (1991) as evidence against the predicted correlation.
Let me address this evidence in particular, and
the prediction more generally. The article in question
describes three patients who were tested on various
perceptual tasks, forced choice face-recognition tasks,
and a savings-in-relearning task. McNeil and Warrington
showed that performance on face-perception tasks and
face-recognition tasks is not necessarily correlated: two
cases showed relatively poor perception of faces with
some degree of recognition, and one case showed better
(but still impaired) face perception but no evidence of face
recognition. This study does not directly address the
relation between overt face recognition and covert face
recognition. Even ifwe were to consider the forced choice
face-recognition tasks to be tests of overt recognition
(contrary to McNeil and Warrington's interpretation),
performance on these tasks is correlated with, not dissociated
from, degree of savings in relearning.
Although it is fair to say that our model of covert
Response/Farah: Neuropsychological inference
recognition predicts a correlation between overt and
covert recognition, the prediction is that patients with
mild prosopagnosia will manifest covert recognition. The
model shows that chance overt recognition can nevertheless
be accompanied by some degree of covert recognition,
so that one would expect to find severely prosopagnosic
patients both with and without covert recognition.
Van Gulick begins by pointing out that our account of
covert recognition is roughly what classical neuropsychology
tells us to expect, given that the relevant dissociation
is only a single dissociation. I agree with this in part, but
think there is still something informative about the model
above and beyond the notions of resources and differential
task difficulty. For one thing, the model is more
explicitly mechanistic than concepts such as "difficulty" or
"resource." It is not necessarily an alternative to these
concepts, but more a cashing out of them in explicit
mechanistic terms. In addition, whereas it is post hoc to
hypothesize differential resource needs to explain dissociated
overt and covert recognition, the model shows how
the nature of overt and covert recognition requires that
they be differentially susceptible to network damage. Van
Gulick also points out that the locality assumption does
not seem relevant to the differences between various
explanations of covert recognition. The locality assumption
is indeed less directly relevant in the case of covert
recognition than in the other two cases, as discussed in
section 2.3.4.
Van Gulick, as well as Young and van Hezewijk & de
Haan, all point out another aspect offace recognition that is
not simulated by the model, namely, conscious awareness.
It never occurred to me that this needed pointing out! The
model is intended to explain the dissociation between
performance on overt and covert recognition tasks. However,
although the model does not simulate consciousness
in the way that it simulates naming, savings in relearning,
and so forth, it is nevertheless relevant to the issue of
consciousness. To the extent that conscious awareness is
correlated with overt recognition, we can view the model
as telling us something about the neural informationprocessing
correlates of conscious awareness. The elucidation
of these correlates is probably the main contribution
that empirical science can make toward the
understanding of consciousness (Farah, in press). According
to the model, the likelihood of a face's identity being
consciously experienced is a function of the quality of the
face representation. As the representation becomes more
degraded, the likelihood of conscious awareness diminishes.
As Van Gulick points out, this view fits well with
Kinsbourne's (1988; 1993) "integrated field theory of consciousness,"
because degraded representations are less
able to pull the rest of the network into a state that is
consistent with their content. Indeed, this is exactly what
we see in the model: in naming, for example, a degraded
face representation is unable to pull the name units into a
state consistent with it, that is, the state of representing
the face's name, even though it can support performance
in various covert recognition tasks.
R4. A closing thought: Science by rules and
science by seat-of-the-pants
Neuropsychology is a very self-conscious science. We do
not just concern ourselves with hypotheses about cogniBEHAVIORAL
AND BRAIN SCIENCES (1994) 17:1 99
References/ Farah: Neuropsychological inference
tion and the brain; we also form hypotheses about how
those hypotheses are formulated and how they should be
tested. Clearly, I am no longer in a position to complain
about this state of affairs! Yet I would like to distinguish
between two approaches to metatheoretical issues in
neuropsychology and suggest that one of them is counterproductive.
Although some evidently interpreted my
target article as an example of this approach, its broadest
goal was in fact to challenge this approach.
I am sympathetic to the general practice of reflecting on
what we do as neuropsychologists and attempting some
analysis and justification of it. This seems useful, as well as
intrinsically interesting. The approach I wish to challenge
is the codification of our scientific practices into hard-andfast
rules. Familiar examples of these include "single
dissociations are inherently ambiguous and therefore not
to be used as evidence," and "there is no way to group
patients a priori as having the same functional lesion and
therefore group study designs are invalid." These rules
call our attention to important considerations but it is
wrong to view the consequences of these considerations
in such black-and-white terms. Progress has been made
on the basis of single dissociations and group studies. This
alone is proof that such rules would be counterproductive
if followed strictly. Good neuropsychology makes use of
an unbounded set of background facts, heuristics, and
intuitions in going from observed behavioral impairment
to hypotheses about the functional architecture. It is
much like flying by the seat of one's pants.
In criticizing the locality assumption, I wish to broaden
rather than constrain the ways we think about the effects
of local lesions in the functional architecture and the
range of hypotheses we consider when interpreting the
behavior of brain-damaged subjects. I certainly do not
wish to add new rules to a Hoyle's Neuropsychology, such
as "the effects of brain damage are never local to the
damaged component, and therefore an X impairment can
never be interpreted as evidence for an X component," or
"one must construct a computional model before making a
neuropsychological inference." However, thinking about
highly interactive systems does not come naturally, and it
is easy to overlook viable alternative hypotheses because
one's intuitions do not encompass the behavior of such
systems under damage. My goal is to persuade neuropsychologists
to consider such alternative hypotheses,
and when necessary to educate and check their intuitions
with computational models.
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