Artificial Intelligence Department
School of Computer Science and Engineering
The University of NSW
February 22, 1998
Research into problems solving methods (PSMs) has identified numerous possible benefits for this approach. However, given the current state-of-the-art in PSM evaluation, these benefits cannot yet be demonstrated. This paper critically evaluates the published PSM research to argue that further evaluations are now required. In particular, PSMs should be comparatively evaluated in order to test if PSMs offer a comparatively better approach to expert systems development.
There are two kinds of truth, small truth and great truth. You can recognize a small truth because its opposite is a falsehood. The opposite of a great truth is another truth. Neils Bohr
Problem solving methods (PSMs) are one of the main topics in modern knowledge acquisition. This paper argues the PSM literature is mostly exploratory research; i.e. for the most part it has yet to answer the numerous questions it has found concerning knowledge engineering.
Cohen [Cohen, 1995] distinguishes between exploratory research and evaluation research: exploratory research enters a new area and finds questions while evaluation research tries to answer those questions. PSM research results (e.g. [Linster, 1992, Schreiber & Birmingham, 1996]), are rarely presented as comparative empirical results; i.e. some experiment is run multiple times with some variation between each trial (exceptions: [Corbridge et al., 1995, Gil & Tallis, 1997a, Motta & Zdrahal, 1996, Runkel, 1995, Zdrahal & Motta, 1996]). That is, PSMs have found questions, but not answers.
This is not because such empirical evaluations are impossible to explicate or collect. Numerous examples exist in the none-PSM knowledge engineering literature where a thorough empirical analysis has been performed (e.g. [Gordon & Shortliffe, 1985, Hayes, 1997, Lee & O'Keefe, 1996, Menzies et al., 1992, Preston et al., 1993, Reich, 1995, Vicente et al., 1995, Waugh et al., 1997, Weiss et al., 1978, Yost, 1992, Yu et al., 1979]).
This lack of empirical evaluation does not mean that the problem solving method research is somehow fatally flawed. The real strength of the PSM programme, in my view, is that it lets us define questions about knowledge engineering which can be evaluated. That is, the PSM literature should be viewed as defining a evaluation programme that should keep us quite busy for many years to come. In this respect, PSMs are a tremendous success (in terms of the above Bohr quote, PSMs are a great truth).
Nor does this lack of empirical evaluations mean that PSM researchers are guilty of poor science. While this paper will be critical of many of the experiments in the PSM literature, it must be stressed that it takes time to design a good experiment. Better experimental designs are created via recognising the flaws in older designs. We cannot get to the better designs without the earlier versions. Hence, the current generation of PSM experiments are essential initial steps towards a viable empirical evaluation programme.
I will proceed as follows. Firstly, some briefing notes are presented on empirical methods which set the stage for a review of the list-of-claims made in the PSM literature (e.g. [Angele et al., 1996, Benjamins, 1995, Breuker & de Velde (eds), 1994, Chandrasekaran et al., 1992, Chandrasekaran et al., 1992, Clancey, 1992, Eriksson et al., 1995, Marques et al., 1992, Motta & Zdrahal, 1996, Schreiber et al., 1994, Shadbolt & O'Hara, 1997, Steels, 1990, Swartout & Gill, 1996, Tansley & Hayball, 1993, Wielinga et al., 1992, Wielinga et al., 1997, Gil & Melz, 1996]). In my view, these papers claim explicitly or tacitly that PSMs support the following:
However, the evidence for these claims is not based on Cohen-style evaluation research. Further, as we shall see below, a case against all these claims can be made.
The conclusion drawn from this analysis must be stated with care. To cast this article as an attack on PSMs would be inappropriate. Rather, it is a review of the evaluation criteria used to assess PSMs up until this time. This paper does not disprove the efficacy of PSMs. Rather (in the case of Claim 5) it merely shows that:
Hence, the conclusion from this article is that the utility of PSMs is still an open research issue. Given the prominance of PSM research in the knowledge acquisition field, this conclusion suggests that better evaluation studies are urgently required. This paper does not offer experimental designs for those evaluations (my own view of such designs are recorded elsewhere; see [Menzies, 1995, Waugh et al., 1997, Menzies et al., 1997, Menzies & Cohen, 1997, Menzies, 1996b]). Before we can declare some evaluation design to be good, we need an initial discussion on what constitutes a good evaluation. Further, we need strong motivation to pursue evaluations since, generally speaking, evaluations involve a lot of work. The aim of this paper is hence to review evaluation principles and motivate further work in this area. However, some general suggestions for improving PSM evaluations are offered at the end of the article.
This article assumes that the reader is familiar with PSMs (for an short introduction to PSM-based approaches, see [Linster & Musen, 1992]).
One way to assess a system is to carefully measure its behaviour in some experiment. Standards for careful observations of software experiments have been extensively researched. This section summarises the portions of that research which will be used in our subsequent discussion. For a full discussion, see [Fenton, 1991, Cohen, 1995]. For introductory remarks to experimental methods, software measurement, and the evaluation of expert systems, see [Reich, 1995, Fenton et al., 1994, Gaschnig et al., 1983]. For examples of good empirical evaluations, see [Yu et al., 1979, Corbridge et al., 1995, Menzies, 1996b, Vicente et al., 1995, Sanderson et al., 1989]. For examples of very good empirical evaluations, see [Hayes, 1997, Yost, 1992].
Certain basic principles for measurement should always be observed.
Basili [Basili, 1992], characterises software evaluation as a goal-question-metric triad. Beginners to experimentation report whatever numbers they can collect without considering the goal of the research project, what questions relate to that goal, and what measurements could be made to address those questions. Fenton [Fenton, 1991] offers a theoretical and pragmatic analyses what makes for a good measurement. Good measurement programs must measure how a product was generated (process measures); what was generated (product measures); and what resources (e.g. time, skill level of developers) were used in the production.
Fenton's comments on resource measurements caution us that a piece of software should be tested on a different population to those used in developing it. In machine learning terms, this means training on one set of examples, then testing on an unseen set of examples [Quinlan, 1986]. In human-in-the-loop knowledge acquisition systems, this means that the developers of a system should try the system out on other people. Otherwise, we could encounter the resource conflation problem: i.e. the results could confuse the skill of the developer with the intrinsic value of the tool.
Measurements should be specified enough such that another researcher can reproduce them. Also, it is useful to have an active refutable hypothesis. A good experimenter defines a observation which, if seen would refute some active hypothesis.
Another useful principle is the straw man: i.e. some variant of the studied technique that appears to be obviously inferior. Straw men allow us to be surprised since, sometimes, straw men do not burn; i.e. the apparently stupider approach may sometimes perform as well as an apparently more sophisticated approach (e.g. see the Corbridge study below).
Experimental instrumentation must be calibrated using baseline values and gold standards. It is useful to compare measurements with some baseline value. For example, if we measure (e.g.) 43 in an experiment, that tells us less than if we can measure 43, then contrast that with the known baseline value of (e.g.) 21. Also, beware of ceiling and floor effects; i.e. experiments in which all the measurements are stuck around some highest or lowest figure. Ceiling and floor effects do not allow us to distinguish variables in an experiment. For example, suppose all students score 100 percent in a university entrance exam. That test would be a waste of time since it cannot rank candidates. Straw men are good for identifying floor effects: if all the measures are clustered around the measures for the straw man, then the measure should be changed. Lastly, as well as a baseline, it is useful to be able to compare the results to some have some objective gold standard.
Sample sizes (N) should be carefully controlled. Small sample sizes are hard to analyse. However, as random sample size get larger, they approach a bell shape (the normal distribution) which is a well understood distribution. In practice, N greater than 20 is acceptable and N greater than 30 is encouraged. On the other hand, there may be no benefit with making N very large (Cohen argues that sample sizes of N greater than 50 can be pointless [Cohen, 1995], p116). Spurious correlations can occur in large sample sizes which may require further experimentation or statistical analysis to confirm or deny [Courtney & Gustafson, 1983]. In general, when dealing with large sample sizes, it is best to restrict the conclusions to an analysis of the active hypothesis that prompted the experiment.
The above basic requirements do not tell us what numbers to collect. This issue has been addressed in the literature. [Buchanan & Shortliffe, 1984a, Gaschnig et al., 1983] note that the success criteria should reflect end-user concerns and not internal criteria. For example, in the PIGE farm-management expert systems, the evaluation was not (e.g.) number of productions fired per second. Rather, it reflected the concerns of the population of farmers who might wish to buy the package. We used the following evaluation criteria: increased profitability per square meter per day [Menzies, 1997a].
Cohen remarks that:
Programs are not experiments, but rather the laboratory in which experiments are conducted [Cohen, 1995], p xiii.
We should not ask experts to evaluate a program merely by watching it run. One side-effect of evaluations studies is the observation that, often, experts disagree ([Gaines & Shaw, 1989, Shaw, 1988, Gaschnig et al., 1983, Yu et al., 1979]). The halo effect prevents a developer for looking at a program and assessing its value. Cohen likens the halo effect to a parent gushing over the achievements of their children and comments that...
What we need is not opinions or impressions, but relatively objective measures of performance. [Cohen, 1995], p74.
In the KBS literature, there are two prominent examples of so-called evaluations that are better characterised as program watching. The PSM community have the Sisyphus studies [Linster, 1992, Schreiber & Birmingham, 1996] just as the older expert systems community had the Oak Ridge spill study [Barstow et al., 1983, Johnson & Jordan, 1983]. In both studies, a group of international researchers agreed to develop systems for some common problem. The Sisyphus studies had a better criteria for success than Oak Ridge (though in the case of Sisyphus-II, it is not clear if all the participants meet that criteria: see below). With few exceptions (e.g. [Zdrahal & Motta, 1996], see below), reports by Sisyphus or Oak Ridge participants comprise reports of a single run of the system. Experimentation requires more than one run. Data is collected for each run and something is slightly different for each trial. Both these studies were useful in unifying and focusing the work of a large number of researchers. As such, they were a tremendous success (and the Sisyphus experiments are continuing). However, as we shall see below, these studies do not qualify as comparative empirical evaluation studies.
The opposite of the halo effect is when the recommendations of the expert system are rejected merely because some judge knows that the recommendations come from a computer program. [Gaschnig et al., 1983] hence recommends blinding studies. In such blinding studies, the evaluating agent is not told recommendations come from the expert systems and which come from other sources.
After performing one evaluation, your work does not stop there. A good experimenter critically reviews their results (if they don't, someone else will) and look for ways to improve them. For example, the MYCIN evaluation study [Yu et al., 1979] took five years and two earlier versions to define adequately. Faults with the prior versions were used to design the next version [Buchanan & Shortliffe, 1984a].
This self-critique stage is very important. There are numerous examples in the literature where evaluation stopped too early. For example, the first trials with the XCON system (October to December 1979) comprised a panel of twelve experts. Ten orders for computers were configured by XCON. These configurations were assessed and the system deemed proficient. Note that this evaluation process had no well-define success criteria. In terms of the above discussion, it suffered from program watching and (possibly) the halo effect. Nevertheless, despite the results of this evaluation study, one year later, XCON was a poor configuration tool. The earlier evaluation was incomplete since it only studied a tiny fraction of the set of possible orders [Gaschnig et al., 1983] (p270-271).
We should routinely expect to have to perform multiple evaluations since not everything can be measured in one experiment. An ideal experiment simultaneously scores highly on three dimensions: specificity: tight experiment controls; face validity: a correspondence of the experimental situation to the real situation; and meaningfulness: theoretical depth; i.e. generality and rigor. Sanderson [Sanderson et al., 1989] comments that the experience of cognitive engineering and ergonomics is that:
It seems to be impossible to do all three at the same time. By maximizing any two, there always seems to be a compromise in the third... Individual studies might maximise different pairs of dimensions, but taken together the studies would offer converging evidence on an issue.
Elsewhere, I have discussed the design of languages that support evaluation as an on-going process through the life cycle of an expert systems [Menzies, 1995, Menzies & Compton, 1997].
We illustrate some of the above points with an example taken from the PSM literature. Corbridge et.al. studied the efficacy of problem solving methods on KA [Corbridge et al., 1995]. In this study, subjects had a fixed two-hour time period to extract a list of disorders and knowledge fragments from a transcript of a doctor talking to a patient. These lists were compared to a gold standard: a list generated using unlimited time by Corbridge et.al. The results are shown in Table 1.
Table 1: Analysis via different models
In a statistical analysis of this study, there was no detected statistical difference between the "A" groups. That is, models of problem solving methods invented the night before assist KA just as well as models developed over more than a decade. Further, the "B" group were statistically better than the "A" groups. That is, using no PSM was better than using a PSM at all!!
The Corbridge et.al. study is an example of a good experiment. The experiment contains a straw man, a gold standard, and performed multiple trials with a controlled variation between each trial. Further, all the materials associated with the experiment are offered in the appendix to that paper; i.e. it is reproducible. One complaint with the study is that the time period involved (2 hours) may not reflect how industrial practioners really use tools like PSMs. In terms of comments of Sanderson, the Corbridge study was not optimised for face validity. However, since a single experiment cannot optimise for face validity and specificity and meaningfulness, this is not a fatal flaw with the Corbridge study. The best we can usually do is design multiple experiments that optimise different pairs of the above three goals.
This section reviews the list-of-claims made by the PSM literature.
This section argues that the knowledge-levelview taken by PSM research precludes arguments of computational tractability.
Expressibility vs tractability trade offs are discussed extensively in the knowledge representation (KR) literature (e.g. [Levesque & Brachman, 1985]). Solutions to a class of problems (the NP-hard problems) are known to have an exponential upper-bound on their runtimes; i.e. may be intractable. Much of the KR literature is concerned with finding restrictive cases in which a representation can be shown to tractable; i.e. worst-case runtimes are polynomial. This style of analysis requires a detailed knowledge of the syntactic structure of a knowledge base (e.g. [Tambe et al., 1990, Tambe & Rosenbloom, 1994, Brachman & Levesque, 1984]). In the usual case, PSM research separates itself from symbol-level implementation detail (exceptions: [Benjamins, 1993, Fensel, 1995]). This has the advantage that many implementations could handle this functionality such as rules, frames, a statistical package, or even a human operator to operationalise the functionality However, without a commitment to symbol-level detail, a KR-style analysis of the computational tractability of a KB is impossible.
My reading of the current PSM literature is that experimental evaluations of PSMs are rare. Hence, it is hard to make a definitive evaluation of the success of PSM-based approaches. For example, three impressive PSM-based developments are SHELLEY: a PSM-based knowledge engineering workbench [Wielinga et al., 1992]; VT: an elevator configuration system [Marcus et al., 1987, Marcus & McDermott, 1989]; and Sisyphus-II: attempts to emulate VT [Schreiber & Birmingham, 1996]. These are discussed below.
An example of using the SHELLEY workbench is given in [Wielinga et al., 1992]. In that example a knowledge engineer is shown mapping a transcript of an expert interview into a library of PSMs. If a user of SHELLEY decides that they are using some PSM, then the knowledge acquisition process can be directed towards collecting lists of the terminology required for that PSM. This report of SHELLEY includes no measurements which explore the efficacy of SHELLEY.
VT was built using a knowledge acquisition tool called SALT [Marcus et al., 1987, Marcus & McDermott, 1989]. SALT was based on a propose-and-revise PSM. SALT's interface restricted itself to only collecting information relevant to that PSM. SALT automatically generated the majority of the VT rules (2130/3062=70 percent). The VT results are an impressive demonstration that, in one application, the SALT implementation technology can scale up to very large systems. However, the VT report is an experience report rather than an evaluation report of the adequacy of the system (such an evaluation report would describe data collected from numerous runs with slight variations between each trial).
While PSMs are extensively studied, their utility in working systems is rarely experimentally evaluated in the literature. For example, only one Sisyphus-II offering reports multiple runs with their implementation [Zdrahal & Motta, 1996]. Five variants on elevator speed and elevator capacity were explored. In 13 of the reported 25 runs, their system could not configure the elevator Their results are shown in Table 2.
Table: The P&R local greedy search method for configuring elevators fails in 13 out of 25 legal ranges of speed and capacity. From [Zdrahal & Motta, 1996].
Zdrahal and Motta argue that the failures of their elevator configuration system were fundamental to the propose and revise PSM in the Sisyphus-II specification [Zdrahal & Motta, 1996]. Standard propose and revise is a local greedy search; i.e. constraint violations are fixed as they occur. Such a hill-climbing algorithm may ignore solutions which are initially unpromising, but lead later on to better solutions. That is, the above errors where not a function of the Zdrahal and Motta implementation. Rather, they should also have been seen in the other Sisyphus-II offerings if they had followed the problem specification and if they had run their program over the range of legal inputs. The fact these errors were not reported elsewhere strongly suggests that the other Sisyphus-II offerings were not extensively tested. That is, it cannot be argued that the Sisyphus-II successfully achieve the task of elevator configuration.
In summary, PSM research generally lacks experimental evaluations (exceptions: the Corbridge study and the work of Motta and Zdrahal). Hence, the claim that PSMs successfully achieve some task is still an exploratory claim, not an evaluation claim.
The Corbridge study (mentioned above) suggests that it is not necessarily so that PSMs simplify initial acquisition.
Do PSMs clarify or confuse design and implementation issues? Evaluations in this regard are rare so this is an open issue. Two studies of the effects of PSMs on implementation are given below. Note that they offer contradictory results: more empirical evaluation is required.
Clancey reports that after a PSM analysis of 176 MYCIN rules, he could generate a new knowledge base where 80 percent of the rules had only a single condition. Further, the problem solving strategies removed all uncontrolled backtracking [Clancey, 1992]. However, this result has not been reported elsewhere and it can hardly be called an evaluation study (no repeated runs with some slight change between each run).
Motta and Zdrahal discuss the various Sisyphus-II implementations using their special knowledge of constraint satisfaction algorithms [Zdrahal & Motta, 1994]. I find their analysis more insightful into the construction process than the less-detailed, high-level PSM approach. This low-level view of a problem can find errors that experienced PSM practioners cannot. For example, Motta and Zdrahal argue that one declarative translation of the procedures in the Sisyphus-II specification blurred the distinction between hard constraints (which must not be violated) and soft constraints (which can be optionally violated) [Motta & Zdrahal, 1995].
Elsewhere [Menzies, 1996a], I have argued that PSMs can obscure important similarities. Significant similarities exist between seemingly different PSMs. If we actively explore those similarities, one basic abductive inference procedure becomes apparent: the extraction of a consistent subset of a theory that is relevant to some task. Abduction over and-or graphs can be shown to implement many of the PSMs; i.e. prediction, classification, explanation, tutoring, qualitative reasoning, planning, monitoring, set-covering diagnosis, consistency-based diagnosis, validation, and verification [Menzies, 1996a].
This section argues that the literature has yet to evaluate the testability of PSMs. Claims that PSMs improve KBS testing are common, e.g [Shadbolt & O'Hara, 1997, van Harmelen & ten Teije, 1997, van Harmelen & Aben, 1996, Fensel & Schoenegge, 1997]. However, none of this work has yet to devise an experimental evaluation of their claims that PSMs = better testing.
A well-developed area of testing research is the knowledge base verification and validation (V and V) community. Nearly all V and V work focuses on an analysis of the dependency networks between literals in a rule-base; e.g. [Preece, 1992] (exceptions: [Fensel et al., 1996, van Harmelen & ten Teije, 1997, van Harmelen & Aben, 1996, Menzies & Compton, 1997, Menzies, 1996b, Waugh et al., 1997, Zlatereva & Preece, 1994]). As such, it is usually a symbol-level analysis. One of the premises of knowledge level modeling is that intelligence can be analysed using knowledge content rather than knowledge form; i.e. it is irrelevant if it is expressed in rules or frames or C code or whatever. Hence, for the most part, PSMs cannot utilise the symbol-level V and V techniques. Note that this rejection of symbol-level analysis was seen above when PSM tractability was discussed.
In my own research into KBS testing I encountered numerous issues which are just not addressed in the PSM literature. Firstly, in order to properly validate a theory, some outside source of knowledge must be mentioned. Generally, this quality assessment knowledge or social context knowledge must reflect how the knowledge base will be perceived when it is deployed. Secondly, in my view [Menzies & Compton, 1997], a real world test engine for a knowledge base has to handle inconsistent theories being developed in poorly measured domains. Routinely, such a test engine has to make assumptions and mutually exclusive assumptions must be kept in separate worlds. Once they worlds are generated, a preference criteria must be applied to heuristically select the best world. Using the criteria of return the world(s) which contain the most known outputs, we can fault published theories of neuroendocrinology using the data published to support them (a result first obtained by Feldman and Compton [Feldman et al., 1989], then repeated and generalised by myself and Compton [Menzies & Compton, 1997]). This test engine has been experimentally evaluated in numerous studies in which various aspects of the theory being analysed were varied (e.g. theory size and connectivity [Menzies, 1996a], effects of conjunctions in the theory [Menzies et al., 1997] and different interpretations of time [Waugh et al., 1997]).
Maintenance is different to validation and verification. A good maintenance strategy permits knowledge modification but blocks changes which make changes harder in the future. That is, changes to section I of KB do not also break sections J, K, L,... Three significant explorations of the maintenance problem are ripple down rules [Compton & Jansen, 1990, Preston et al., 1993]; the RIME editor [Bachant & McDermott, 1984, de Brug et al., 1986, Soloway et al., 1987]; and KA scripts [Gil & Tallis, 1997a]. Of these, only KA scripts comes from the PSM community. Ripple down rules (discussed below) abandons the idea of knowledge level altogether. RIME was not based on PSM-principles:
This section argues that the KA scripts results represent an interesting exploration of PSMs, but not an evaluation of the maintainability of PSMs. A comparative analysis of do PSMs provide better maintenance than alternative approaches? is done below (see claim 5).
In the case where numerous changes have to be made to a PSM, if the user does not complete all those changes, then the PSM may be broken. Gil and Tallis [Gil & Tallis, 1997a] use a scripting language to control the modification of a PSM to prevent broken knowledge. These KA scripts are controlled by the EXPECT TRANSACTION MANAGER (ETM) which is triggered when EXPECT's partial evaluation strategy detects a fault (errors are detected if a method cannot fire because the types of the input parameters to the methods are not available). In one study of maintenance times by four subjects (S1..S4) and two change tasks for EXPECT KBS, maintenance was easier with ETM. For example, ETM performed some changes automatically. The Gill & Tallis results are shown in Table 3.
Table: Change times for ETM with four subjects: S1...S4. From [Gil & Tallis, 1997b]
These results cannot be read as an evaluation results demonstrating that PSMs simplify maintenance. While some attempt was made to perform repeated trials whilst varying some factor, the results do not satisfy several Fenton's software measurement criteria:
Also, the results conflate three effects:
Reuse is the holy grail of software and knowledge engineering. This section argues that the reusability of PSMs has not been adequately evaluated.
My reading of the PSM literature is that PSMs change more than they are reused. Between the various camps of PSM researchers, there is little agreement on the details of the PSMs. The list of primitives within the PSMs (e.g. select, classify, etc) from KADS [Wielinga et al., 1992] and the SPARK/ BURN/ FIREFIGHTER project [Marques et al., 1992] are significantly different. Also, the number and nature of the problem solving methods is not fixed. Often when a domain is analysed using PSM, a new method is induced [Linster & Musen, 1992].
When we look at published problem solving methods, we see many differences. For example, [Menzies, 1998] describes eight different supposedly reusable models of diagnosis (four from the PSM community, four from elsewhere). While some of the these views on diagnosis share some common features, they reflect fundamentally divergent different views on how to perform diagnosis. I therefore believe that, at least in the case of diagnosis, a consensus view on diagnosis has not stabilised with time and that such a view may not do so in the foreseeable future. More generally, since PSMs have not stabilised over time, their extensive reuse is hence unlikely. My reading of the current literature is that my no-reuse argument cannot be faulted due to drawbacks with the PSM reuse evaluations studies.
Two major studies in PSM-based reuse are the SPARK/ BURN/ FIREFIGHTER (hereafter, SBF) experiment [Marques et al., 1992] and the MeKA study [Runkel, 1995]. In the SBF toolkit, SPARK builds a domain-specific KA tool that is tailored to the business information supplied by the user. BURN conducts a structured interview with the expert. This interview maps the business information offered by the user into a library of inference sub-routines (called mechanisms). The mapping process is guided by PSM meta-knowledge. At choice points in the mapping, SBF can ask the user questions questions which select different PSMs. Once this mapping has been made, a rule base can be generate which solves the business problem. This is given to the FIREFIGHTER environment which assists the user in executing and debugging the operationalised program. Marques et.al. report significantly reduced development times for expert systems using the 13 mechanisms in the SBF toolkit. In the nine applications studied by Marques et.al., development times changed from one to 17 days (using SBF) to 63 to 250 days (without using SBF).
To the best of my knowledge, this study represents the high-water mark in reported productivity increases in software or knowledge engineering. Nevertheless, the study has its drawbacks:
In the MeKA study, Runkel describes eight applications using mechanisms for knowledge acquisition, or MeKA. Each MeKA divided a PSM into data structure knowledge and control knowledge. MeKAs contain four modules: (i) an acquire/ module which gathers information such as a formula; (ii) a verify module that checks it; (iii) a generalise module which tries to apply the new knowledge to more general expressions, e.g. is the formula applicable to other parameters?; (iv) a dialogue module which handles the screen design for the other modules. All the MeKAs had to be built for the first application (0 percent reuse), but MeKA reuse in subsequent applications rose as high as 88 percent. The Runkel results are shown in Table 4.
Table: Reuse in the MeKA system. From [Runkel, 1995].
The MeKA study is a better experiment than SBF in that the MeKA work has more chance of being reproducible. However, it terms of evaluating the reusability of PSMs, the MeKA study has some drawbacks. Runkel does not comment on who built the applications. If was himself, then once again we may have the resource conflation problem. Also, unlike the SBF study, Runkel does not record the time taken to build each application. That is, if Runkel's goal related to productivity improvements, his measurements could not address that question.
Wielinga et.al. argue that one of the advantages of KADS (a technique which uses PSMs) is that its superior ability to explain the inner workings of an expert system [Wielinga et al., 1992]. Clancey's Heuristic Classification paper [Clancey, 1985] is an impressive PSM-based reverse engineering of numerous expert systems in terms of his heuristic classification technique. The reader is left with a strong impression that heuristic classification explains the inner-workings of the surveyed expert systems. This section repeats the arguments of [Menzies & Compton, 1994] to argue that this strong impression may not be true.
From an empirical evaluation perspective, it is still an open question if PSM-based approaches produce better explanations. Current thinking in the explanation field (e.g. [Wick & Thompson, 1992, Leake, 1991, Leake, 1993, Paris, 1989]) is that good explanations cannot be generated merely via an abstract trace of the system's traversal over a task description (e.g. a PSM) or the print the rules that fired approach used in early expert systems such as MYCIN [Buchanan & Shortliffe, 1984b]). In the current view, explanation is a problem solving task in its own right. Explanations are user-specific:
The audience of an explanation can significantly affect the purpose and therefore the content of an explanation [Wick & Thompson, 1992]
Explanation is an inference procedure that determines what is to be presented to the user. Leake [Leake, 1991] and Paris [Paris, 1989] discuss explanation algorithms where explanation presentation is constrained to those explanations which contain certain significant structures. Paris's significant structures are determined at design time while Leake assigns significance at runtime. For example, when the goal of the explanation is to minimise undesirable effects, the runtime significant structures are any pre-conditions to anomalous situations. From a range of possible inferences, some subset is selected that meets some understandability criteria for different users and different goals. That is, a model that is good for explanatory purposes contains some degree of indeterminacy (can generate more than one behaviour). Also, Leake argues convincingly that a cache of prior explanations and an active user model are essential components of a good explanation module [Leake, 1993].
User-profiles, indeterminate models, and case libraries are not issues addressed in current PSMs approaches. Therefore, in their current form, PSMs may not be a good generalised explanation tool.
Consider the statement software technology X lets me do task Y. This is hardly an evaluation statement since there may be many software technologies that allow us to implement Y. A better statement is comparative: software technology X lets me do task Y better than software technology Z. In order to compare an approach, we need to identify an alternative approach. This section records certain alternatives to PSMs which have demonstrated competency: problem-space traversal systems, standard software engineering, ripple down rules, and human-computer interaction. At the very least, these systems are straw men. PSMs should at least be able to out-perform the following, apparently less sophisticated, techniques.
Significant levels of reuse are already reported in the standard software engineering literature. Stark reports code reuse levels of 70-80 percent using FORTRAN and some object-oriented design principles [Stark, 1993]. Frakes and Fox found maximum median values for reuse in requirements, design, and code reuse at 15, 70, and 40 percent respectively [Frakes & Fox, 1995]. Frakes and Fox found no significant correlation between reuse and technology options such as the use of CASE tools; the presence of code repositories; or language level (assembler has a lower language level than object-oriented languages such as Smalltalk); The factors that were positively correlated to reuse were all organisational factors such as practioner education in reused; unified software process; or industry type (telecommunications always was one of the highest reusers, possibly due to the standard hardware configurations in that field).
These reports of Stark, Frakes and Fox suffer from inexact measures of reuse. For example, the Frakes and Fox study never looked at source code: it's data was based on a questionnaire sent and returned by post. Nevertheless, this work does show that some levels of significant reuse may be achievable without technology options such as PSMs. The empirical evaluation goal of PSM researchers should be some test that PSMs produce higher levels of reuse that (e.g.) standard software engineering.
One of the largest studies in knowledge maintenance is the RIME's KB editor [de Brug et al., 1986, Soloway et al., 1987]. RIME acquired parts of the meta-knowledge for the XCON computer configuration system [Bachant & McDermott, 1984]. RIME is a problem-space traversal system. It assumes that the KB comprised operator selection knowledge which controlled the exploration of a set of problem spaces. After asking a few questions, RIME could auto-generate complex executable rules. RIME has not been evaluated in an empirical experiment (but see [Soloway et al., 1987]). Nevertheless, RIME is a landmark system. Other PSM-based maintenance research has yet to make an empirical case that their techniques are superior to RIME.
Another problems-space traversal system was Yost's Sisyphus-II contribution [Yost, 1994]. The rest of the Sisyphus-II contribution were all PSM approaches. I can see no evidence of productivity benefits of PSM over Yost's system in the Sisyphus-II results. Indeed, Yost's "old-fashioned" problem-space traversal system was developed in times comparable to SALT and faster than many of the other PSM approaches.
These comments on comparative evaluations and Sisyphus-II could be criticised as follows. The sample size was too small and too inaccurately measured to yield meaningful results (most Sisyphus-II groups were less-than-rigorous in documenting their development times except for Runkel et.al. [Runkel & Birmingham, 1994] and Yost [Yost, 1994]). I return below to the issue of comparative analysis of maintenance techniques (see ripple down rules). For the moment, all we need to say is that the comparative advantage of PSMs for maintenance over none-PSM approaches is an open issue in the literature.
Compton takes a weak situated cognition [Menzies, 1997b] line, which he calls justification in context, His argument is that patching in the context of error is a more realistic KA approach than assuming that a human analyst will behave in a perfectly rational way to create some initial correct design [Compton & Jansen, 1990].
RDR implements this patching process. The RDR representation is optimised for fault localisation in KBS without PSMs [Compton & Jansen, 1990, Compton et al., 1993]. RDR knowledge is organised into a patch tree. If a rule is found to be faulty, some patch logic is added on a unless link beneath the rule. The patch is itself a rule and so may be patched recursively. Whenever a new patch (rule) is added to an RDR system, the case which prompted the patch is included in the rule. These cornerstone cases are used below when fixing an RDR system. At runtime, the final conclusion is the conclusion of the last satisfied rule. If that conclusion is faulty, then the fault is localised to the last satisfied rule. Once a fault is localised, an expert can then ask the system for a list of possible patches. The system replies with a difference list which is calculated as follows. As the current case navigates down the RDR tree, if it finds a some satisfied rule, it then checks their unless patches. The different between the current case and the cornerstone case of the last satisfied rule is the difference list. In terms of empirical evaluation, RDR is exceptional in that RDR builds evaluation into the life cycle of the whole system. At anytime, the current RDR tree can correctly classify 100 percent of the cases seen to date.
RDR trees are a very low-level representation. RDR rules cannot assert facts that other RDR rules can use. In no way can a RDR tree be called a model in a PSM sense. Further, the RDR formalism makes no commitment to tree structures that are optimal. An RDR tree can contain repeated tests, redundant knowledge, and its sub-trees can overlap each other semantically. Despite these apparent drawbacks, RDR has produced large working expert systems in routine daily use. In practice the RDR trees are only twice as big as the optimum tree [Gaines & Compton, 1992] and runtimes have never been an issue. It may be somewhat misguided to attempt to optimise an RDR tree to (e.g.) remove the redundancies or separate the overlaps. The important feature of an RDR tree is that is it optimised for maintenance. Alternative representations may run faster, but incurs the penalty of more complicated maintenance.
In practice, RDR appears to work very well. For example, the PIERS system at St. Vincent's Hospital, Sydney, modeled 20 percent of human biochemistry sufficiently well to make diagnoses that are 95 percent accurate [Preston et al., 1993]. RDR has succeeded in domains where previous attempts, based on much higher-level constructs, never made it out of the prototype stage [Patil et al., 1981]. Further, while large expert systems are notoriously hard to maintain [de Brug et al., 1986], the no-model approach of RDR has never encountered maintenance problems. System development blends seamlessly with system maintenance since the only activity that the RDR interface permits is patching faulty rules in the context of the last error. For a 2000-rule RDR system, maintenance was very simple (a total of a few minutes each day).
The core of the competency of problem-space traversal systems and ripple down rules is some knowledge base. However, it may be possible to build a system that supports (e.g.) diagnosis without such a knowledge base. For example, [Vicente et al., 1995] discusses diagnosis, and fault detection using 'ecological interface design' (EID). An EID contains visual representations at five levels of an abstraction hierarchy:
Interestingly, none of this abstraction hierarchy may exist in a knowledge base of an EID system. Rather, the above five principles are used by an interface designer when re-arranging and augmenting the display on the screen. No inference engine accesses this hierarchy at runtime in the conventional knowledge representation sense.
[Vicente et al., 1995] suggest that EID-based interfaces lead to better performance on diagnosis tasks when subjects are simply asked to monitor the physical While it was not the intention of the authors of [Vicente et al., 1995] to do so, this work offers a challenge to the standard KBS view of model-based diagnosis and repair. Rather than build sophisticated KBS systems, perhaps we should be looking at better interface design? At the very least, it seems to me that the KBS community should attempt a comparative evaluation of KBS-style diagnosis and fault detection vs EID-based diagnosis and fault detection.
Give me a fruitful error any time, full of seeds, bursting with its own corrections. You can keep your sterile truths for yourself. Vilfredo Pareto
PSM research is still exploratory; i.e. it lets us define questions for knowledge engineering (the list-of-claims). However, PSM research is not evaluatory; i.e. the questions it asks have yet to be answered using empirical evaluation techniques. Evaluation is very important. Before we can sell PSMs to the wider knowledge engineering community, we should be able to demonstrate that PSMs are valuable. Such demonstrations are lacking in the current literature. We should work towards performing such evaluations in the future.
This article has analysed the drawbacks with current PSM evaluation studies. This analysis can be used to avoid certain traps in future PSM evaluations such as:
This critique has only focused on PSMs. A similar critique (too much exploration, not enough evaluation) cannot yet be applied to the ontologies research (e.g. [Gruber, 1993]). PSMs research is at least 14 years old [Chandrasekaran, 1983] while ontologies are a much newer concept which are being explored. However, I would hope that within the next five years, ontological researchers move away from exploratory research towards evaluation research (e.g. along the lines proposed in [Menzies et. al. , 1997]).