Journal of Experimental Psychology: Human Learning and...

Journal of Experimental Psychology:Human Learning and Memory

VOL. 6, No. 5 SEPTEMBER 1980

Evidence Against a Semantic-Episodic Distinction

John R. Anderson Brian H. RossCarnegie-Mellon University Yale University

The possible empirical bases for the semantic-episodic distinction are ex-amined. Two kinds of results are particularly relevant. The first concernswhether the same functional laws can be demonstrated for semantic as forepisodic memory. Failure to demonstrate such generalities argues for thedistinction, whereas success at demonstrating generalities argues against theneed for such a distinction. The second kind of diagnostic result concernswhether one can demonstrate transfer between semantic and episodic memory.Failure to find transfer argues for a separation, whereas evidence for transferargues against any real separation between the memories. A review of theliterature relevant to these two criteria yields considerable evidence againstthe semantic-episodic distinction. Three experiments are reported thatprovide new evidence against the distinction. The experiments test whetherlearning episodic material interferes with the retrieval of semantic information.The dependent measure was the time to respond true or false to a categoriza-tion statement (e.g., "A spaniel is a dog."). Before participating in that task,subjects learned sentences that provided information about the item and cate-gory. The results indicated that the time to make the semantic judgment wasaffected by the item-category relation in the prior study sentences. Generally,the study effects, as well as some other findings, were correctly predicted bythe ACT theory, which makes no semantic-episodic distinction. However,contrary to the ACT theory, it was found that learning additional informationabout a concept does not interfere with making positive semantic memoryjudgments and possibly facilitates.

Tulving (1972) proposed a distinction be- memory for specific events and is temporallytween semantic and episodic memory, dated. Semantic memory is essential forEpisodic memory is an autobiographical language use and contains organized knowl-

edge about symbols and concepts detachedfrom autobiographical reference. Tulving

This research was supported by National Science suggested that these two memories may beFoundation Grants BNS76-00959 and BNS78-17463. governed by different principles and pro-

Both authors contributed equally to this article; d seyeral other possible differences be-the order of authors was determined by a com toss. r , • i j- i_ j f cWe thank Bill Jones and Ed Smith for their comments tween them, including the mode of referenceon this manuscript. We also thank Barbara Adams for (autobiographical VS. cognitive) and re-taking responsibility for the programming, execution, trieval characteristics. Though in his 1972and analysis of Experiment 3. article he stated that this distinction is not

E^^?S5.S2SJ2II^1£- John R. necessarily a functional one, it has oftenAnderson, Department of Psychology, Carnegie- been taken to be such (Atkinson, Herrmann,Mellon University, Pittsburgh, Pa. 15213. & Wescourt, 1974; Kintsch, 1975; Lockhart,

Copyright 1980 by the American Psychological Association, Inc. 0096-1515/80/0605-0441S00.75

441

442 JOHN R. ANDERSON AND BRIAN H. ROSS

Craik, & Jacoby, 1976; Shoben, Wescourt,& Smith, 1978; Tulving, 1976; Watkins &Tulving, 1975) and has gained considerableacceptance. The semantic-episodic dis-tinction has not been accepted as implyinga functional difference by many associativeand neoassociative models of memory (seeAnderson & Bower, 1973). Such theoriesare inclined against accepting this distinc-tion because of their empiricist leanings,their emphasis on the continuity of knowl-edge, their rejection of the synthetic-ana-lytic distinction, and their belief that allknowledge derives from experience. Noneof these factors compel one to reject thedistinction, but they do predispose one. Ourpurpose in this article is not to questionthe utility of the semantic-episodic dis-tinction as a conceptual heuristic, butrather to question whether there is reallyany functional difference between thememory that stores semantic knowledgeand the memory that stores episodic knowl-edge.

In this article, we will try to accomplish anumber of objectives relevant to evaluat-ing the semantic-episodic distinction. Wereview the state of the literature with respectto the issue of whether there is a functionaldistinction between semantic and episodicmemory. We argue that the state of theliterature does not support a functionaldistinction between semantic and episodicmemory. The two types of memory appearto obey the same laws and to be so highlyinterdependent that they are best consideredone memory system. We present a series ofthree experiments from a fact recognitionparadigm that demonstrates the stronginterdependence of semantic and episodicmemory. In addition to addressing thesemantic-episodic distinction directly, weconsider how well a particular memorytheory called ACT (Anderson, 1976) faresin accounting for the results of our experi-ments. This theory assumes that all informa-tion is stored in a single memory and soexpects a high degree of interdependencebetween facts supposedly in "semanticmemory" and facts supposedly in "episodicmemory." This theory is interesting be-cause it not only predicts a high degree ofinterdependence, it predicts the nature of

the interdependence. As such it will serveto bring out other interesting aspects of thedata. The reader should keep in mind, how-ever, that the semantic-episodic issue andACT provide somewhat independent per-spectives on the data. For instance, it mightwell turn out that there is no functionaldistinction between semantic and episodicmemory and that the ACT theory of memoryis wrong, too.

The ACT Theory

Before considering the relevant literature,it is useful to review the ACT theory (Ander-son, 1976). Long-term memory in ACT isrepresented by a network of propositionsinterconnecting concepts. The relations be-tween concepts are encoded in the preposi-tional structure connecting the conceptnodes. All information, semantic andepisodic, is stored together. This does notmean that there are no differences amongthe memory traces. The various possibilitiesthat Tulving (1972) suggested, such as auto-biographical tags and differing richness ofconnections, are represented. However,the ACT theory does not require a strictcorrelation of trace characteristics as en-visioned by Tulving. So, for example, aparticular trace may be temporally tagged asare episodic memories but be richly con-nected as are semantic memories. In thismodel, there is no functional distinctionbetween semantic and episodic informationin terms of storage, retention, or retrieval.It is basically all one big memory.

One extensive application of the ACTtheory has been in understanding how sub-jects recognize facts like A spaniel is a dog.To verify a particular proposition, the nodesrepresenting the concepts in the propositionare activated and a search is started fromall nodes. The search process consists ofthe activation spreading from the nodesdown all links until there is an intersection.At that time, the intersection is evaluated todetermine whether it matches the proposi-tion to be verified. Quillian (1968), Collinsand Quillian (1972a), and Collins and Loftus(1975) have proposed similar search mech-anisms. The spread of activation from anode is assumed to be a limited-capacity

EPISODIC EFFECTS ON SEMANTIC KNOWLEDGE 443

parallel process (see Townsend, 1974), sothat the more links connected to a node, theslower the search along each link. In ad-dition, links may vary in strength, withstronger links being traversed more quickly.The time to verify a proposition, then, de-pends on how strongly the concepts areconnected relative to the other connectionsattached to each concept.

Deciding that a particular proposition wasnot studied or is unknown may be accom-plished in several ways. One proposal(Anderson, 1976, chap. 8; King & Ander-son, 1976) is that subjects decide that aproposition has not been studied after wait-ing for a period of time in which no inter-section of activation occurs. The reasoningbehind this strategy is that if no correctintersection has been found after one wouldnormally have been expected, no such inter-section probably exists. It is possible forspurious intersections to occur that willslow the rejection process, since the subjectwill have to evaluate the spurious path ofintersection and then reinstitute the waitingprocess. We do not mean to imply that thiswaiting process is the only means by whichsubjects reject propositions, only that itis an important process. Alternate rejectionprocesses have been proposed for networkmodels (Anderson & Reder, 1974; Collins& Quillian, 1972b; Holyoak & Glass, 1975).

Evaluation of the Semantic-EpisodicDistinction

Some objections to the semantic-epi-sodic distinction have been made on logicalgrounds. In particular, Schank (1975) arguesthat the distinction is a false one, since allconceptual knowledge must be obtainedthrough experience. He believes insteadthat most of memory is an experientiallybased conceptual memory. Ortony (1975)pointed out some flaws in Schank's argu-ments, such as the conceptual confusionbetween knowledge of experience andknowledge from experience. Even thoughboth semantic and episodic information maybe obtained from experience, as Schankclaims, only episodic memory is hypothe-sized to contain knowledge of experience.We think Ortony convincingly refutes

Schank's arguments against a semantic-episodic distinction, but he is much lesspersuasive when providing evidence infavor of the distinction.

There are two kinds of empirical resultsthat are particularly diagnostic in evaluatingthe semantic-episodic distinction. One iswhether similar memory effects are ob-tained in experiments on episodic memoryas in experiments on semantic memory.Similar effects would be evidence that thetwo types of knowledge obeyed similarfunctional laws and would be evidenceagainst a functional distinction. Differenteffects would be evidence for the distinc-tion. The second result that would be diag-nostic is whether one could obtain transfer(positive or negative) of learning betweenepisodic and semantic knowledge. Thiswould be evidence against the separationbetween the two memories. We will reviewthe relevant evidence under these twoheadings.

Note that it might be possible that thetwo systems will display similar functionallaws but no transfer. This might indicatetwo physically separate memory systemsoperating according to the same principles.It is also possible that there might be dif-ferent functional laws but many transfereffects. This would indicate two structurallyinterconnected systems operating accordingto different principles. Of course, the clear-est results would be to find both the samelaws and transfer or neither.

Similar Memory Effects

Interference

Tulving (1972) suggested that semanticmemory might be impervious to the kindsof interference effects that have beendemonstrated over and over again in epi-sodic memory. Episodic traces are remem-bered only through their temporal tags, sothey are very vulnerable to interference.Semantic memories, however, are em-bedded in rich cognitive structures, allowingaccess by many means and hence providingprotection from interference.

Of particular importance to this article isthe class of interference experiments(Anderson, 1974, 1976; Hayes-Roth, 1977;


Thorndyke & Bower, 1974) showing thatthe more episodic facts subjects learn abouta concept, the slower they are to recognizeany of these episodic facts about this con-cept. This result is predicted by the limited-capacity activation process within the ACTtheory. The rate at which a fact is activatedfrom a concept is a function of the strengthof that fact relative to the other facts. Thus,the more facts learned, the slower the acti-vation.

Normally, relative strength and numberof interfering facts will covary, but they canbe decorrelated. When they are decor-related, subjects are as fast to verify a factabout a category with more facts as a factabout a category with fewer, if the two factsare of same relative strength (see Anderson,1976, pp. 285-290, for a demonstration).On the other hand, if one holds a numberof facts constant, subjects are slower toverify the less frequently studied (henceweaker) facts. If one uses production fre-quency norms as a measure of relativeassociative strength, there is ample evi-dence that associative strength affectsverification time in semantic memory(Glass, Holyoak, & O'Dell, 1974; Loftus,1974; Smith, Shoben, & Rips, 1974; Wilkins,1971). There is also evidence that control-ling for relative strength, there is no effectof category size (Freedman & Loftus, 1971)—as ACT would predict. So, when wedefine interference effects in terms of rela-tive strength, we get analogous effects bothfor semantic and episodic memory.

By this reasoning, it should be the case,but it seems not to have been directly tested,that the mean time to verify a semanticmemory fact about a category should be afunction of number of facts in the category.That is, the mean time to verify that one ofthe 12 mo. is a month should be faster thanthe mean time to verify that one of thehundreds of birds is a bird. This result ispredicted because the larger the category,the lower the mean relative strength. Therehave been some studies that have shownweak but positive effects of category size(e.g., Landauer & Meyer, 1972; Wilk-ins, 1971), and studies that have failedto find such effects (Freedman & Loftus,1971). However, these studies have not sys-

tematically sampled members of larger cate-gories to get a mean time. Sampling fromlarger categories has been biased in favorof more frequent members.

Shoben, Wescourt, and Smith (1978)reported a pair of experiments that theyinterpreted as showing that these kinds ofinterference effects are not found in seman-tic memory. They had subjects verifysemantic facts like sparrows have feathersand varied the number of questions theyasked about the concept sparrow. Theyargued that this manipulation was the ana-logue of the episodic manipulation of numberof learned facts. They found no effect ofthis variable. However, their negative con-clusion may be at least partially due to howthey operationalized the analogy. The betteranalogy to number of learned facts in theepisodic experiment would be the totalnumber of semantic facts known aboutsparrow, rather than the number tested inthe experiment. The ACT predictions forthe Shoben et al. task differ from the pre-dictions for experiments in which the num-ber of facts learned about a concept arevaried.

ACT predicts1 that the important variableshould be total number of facts, and onlywith much repeated testing should the num-ber of facts tested become important. Re-peated testing should result in an increase ofstrength for tested propositions, relative tothe ones not tested. Once there is sufficient

1 The following is a summary of the ACT predictionsfor the Shoben et al. (1978) experiment (See Anderson,1976, chap. 8 for details of the ACT analysis of RT): Let5 = the baseline strength of each fact. Let k = the totalnumber of facts known about a concept. Let n = thenumber of facts tested in the experiment, the variable.Letp = the number of timesafact has been tested. Thestrength of the fact will increase with p. The strengthof each of the n facts tested p times is S + p. Thestrength of each of the k - n nontested facts is S. So,the RT to a tested fact will be inversely proportionalto its relative strength.

RT = P) + (k -+P

(k-n)Ss +P

For small values of p relative to 5, RT will be largelydetermined by k. As p gets larger, differences amongconditions will get larger with longer times for highervalues of H.


practice that the experimental strength islarge relative to the preexperimental strength,it will be important how many experiment-ally strengthened propositions there arecompeting. Thus, the ACT prediction isthat there should be an interaction betweenthe number of facts tested about the conceptand the number of times they are tested,although it is unclear how much testingwould be required to get the interaction.The second experiment of Shoben et al.shows some effect in this direction, but itwas not significant.

Relatedness Effects

In the semantic memory literature, therehave been numerous demonstrations of theeffect of semantic relatedness (e.g., Collins& Loftus, 1975; Collins & Qullian, 1972a;Glass et al., 1974; Meyer, 1970; Schaeffer& Wallace, 1970; Smith et al., 1974). Thisfactor refers to the extent to which thesubject and predicate terms are related andhas been measured by direct ratings or pro-duction norms. The general result is thathigh relatedness speeds the confirmation oftrue sentences and slows the disconfirma-tion of false ones. There is no consensuson how to interpret the positive effect fortrue sentences. High relatedness correlateswith production frequency and other vari-ables that might be better thought of asmeasures of associative strength (see Ander-son & Bower, 1973, chap. 12), and in fact,production frequency can be a better pre-dictor of verification time than direct ratingsof semantic relatedness (see Smith et al.,1974). The semantic relatedness effect hasbeen interpreted in terms of associativestrength (Anderson, 1976; Anderson &Bower, 1973; Anderson & Reder, 1974;Glass et al., 1974), which has been shown tohave strong effects in episodic memory (seeAnderson, 1976, chap. 8 for a review).

The relatedness effect with falses hasbeen more problematic for many associativeanalyses. However, such an effect is ex-pected by the spreading activation processin ACT because related falses should resultin more spurious intersections. For in-stance, the reason that a bat is a bird isslower than a bat is a rock is because irrele-

vant intersections of bat and bird (e.g.,through wings, animal) slow down the re-jection process. The subject must considerthese sources of intersection before re-jecting the assertion. King and Anderson(1976) showed analogous effects of spuriousintersections in episodic memory on reject-ing statements about an episodic data base.McCloskey (Note 1) has shown that seman-tic relatedness will also slow down an epi-sodic judgment. In McCloskey's experi-ment, subjects, after studying Fred is arabbi, were slower to reject Fred is a priestthan Fred is a banker.

Shoben et al. (1978) reported a result thatthey interpreted as indicating that episodicmemory does not show a relatedness effect.They had subjects study true, highly relatedfacts like tigers have stripes; true, less re-lated facts like tigers have ears; false, relatedfacts like tigers have fingers; and false, un-related facts like tigers have cars. Subjectswere to commit all such facts, true or false,to memory. In a later recognition test, theywere asked to discriminate such facts fromunstudied, true statements like tigers haveteeth and false statements like tigers havewings. Shoben et al. were concerned withthe studied items. They claimed that if epi-sodic memory were like semantic memory,there would be a positive effect of related-ness on trues and a negative effect of re-latedness on falses.

However, this does not correspond to theACT predictions for studied items. In allstudied cases, subjects have to associatesubject and predicate together in com-mitting the items to memory. Therefore,relatedness should help in establishing thisassociation and retrieving it. Lack of re-latedness should only help in the case inwhich the subject can reject a probe on thebasis of no connection between subject andpredicate as in the case where the subjectis judging the probe tigers have cars for thefirst time. However, in their experiment,a studied probe like tigers have cars wasneither novel nor was the subject supposedto reject it. Seven of the eight comparisonsthat they reported (p < .05, by sign test)support ACT's prediction that subjectsshould be uniformly faster with relatedstudied probes.


Encoding Specificity

The research on encoding specificity isfrequently presented as relevant to thesemantic-episodic distinction (see Flexser& Tulving, 1978; Kintsch, 1974; Postman,1975; Tulving & Thomson, 1973; Watkins& Tulving, 1975). This class of results in-volves demonstrations of the context de-pendency of memory. For instance, a wordthat can be remembered in one context willnot be remembered in another context. Thiscontext dependence is interpreted as show-ing that one does not have access from asemantic trace (the word in general) to anepisodic trace (the specific word). A majorproblem with these findings as evidence forthe semantic-episodic distinction is thatthe results can be interpreted in other waysthat do not require a semantic-episodicdistinction (see Anderson, 1976, chap. 10).For instance, Anderson argued that a wordhas many memory structures (senses,elaborations) associated with it and thatcontext determines which structures can beaccessed. Recall depends on accessing attest the same structures that were accessedat study. Under this explanation, contextdependency arises from retrieval difficultieswithin memory in general, not from a seman-tic-episodic distinction. Consistent withthis other interpretation is the result ofMuter (1978), who demonstrated a similarcontext dependency in memory for thenames of historical figures. His resultsseemed to indicate that such context de-pendency can be found within semanticmemory and does not depend on a "gap"between semantic and episodic memory.

Transfer Between Semantic andEpisodic Memory

There are two directions for transfereffects between semantic and episodicmemory. Demonstrations of a transfer ofsemantic knowledge to episodic memoriesneed not be problematical for the seman-tic-episodic distinction. Tulving (1972)recognized that if episodic traces wereto contain meaningful information, theywould have to be affected by semanticmemory, since it contains the informationessential to comprehension. There have

long been findings that the retrieval ofepisodic information is affected by semanticfactors, such as meaningfulness (see Hall,1966, chap. 10, for a partial review). Theseresults do not argue against Tulving's dis-tinction because they require a dependenceof episodic memory on semantic memoryonly in the creation of the episodic trace.Once established, this trace may not beaffected by semantic memory.

A recent experiment indicates thatsemantic and episodic memory may not beindependent after the initial encoding.Perlmutter, Harsip, and Myers (1976) mea-sured reaction time to recall the response ofa paired associate. They found that thecued recall time was affected by the wordfrequency (negatively) of the stimulus andthe strength of its primary preexperimentalassociate. This finding shows the effect ofsemantic variables (frequency and associ-ative strength) on the speed of retrievingan episodic memory. It is difficult to seewhy such semantic information would beencoded in the episodic trace.

The other transfer possibility involvesthe effect of episodic information on theretrieval of semantic knowledge. Accordingto the proposed distinction, access to in-formation in semantic memory may beaffected by the organization of semanticknowledge, but it should not be influencedby what is stored in episodic memory.(Of course, semantic memory must becapable of being changed in response toexperience; however, it never has beenspelled out how these changes take place.)If learning episodic material facilitates orinterferes with the retrieval of semanticinformation, the distinction is weakened. Ifthe transfer effects are similar to those foundwith solely episodic information (e.g., nega-tive transfer in interference paradigms),there is good evidence against a functionalbasis for the distinction. The experimentsto be reported test this possibility.

A few studies have examined whetherepisodic information facilitates or interfereswith semantic memory. Unfortunately, theresults have been mixed. Slamecka (1966)found that subjects' ability to recall freeassociates to a stimulus was not affectedby learning other experimental associates.


A pilot experiment reported by Collins andQuillian (1972b, pp. 134-136) also failed tofind an effect of episodic information onsemantic memory retrieval time.

A recent study, however, found effectsof episodic memory on semantic retrievaltime. Lewis and Anderson (1976) testedwhether experimentally learned informationwould interfere with preexperimental his-torical knowledge. They had subjects studyartificial facts about famous people andmeasured the time to verify a well-knownfact about a famous person (e.g., "Washing-ton crossed the Delaware.' '), verify artificialfacts studied, or falsify re-paired foils. Thepertinent results are that the time to verifya well-known fact increased with the num-ber of artificial facts learned about the in-dividual, and this was true in both pure testblocks (only real facts are true items) andmixed test blocks (both real and artificialfacts as true items).

The semantic-episodic boundary is notalways clear, however, and historicalknowledge may be considered by some tobe in the gray area. It may not possess therich interconnections posited of semanticknowledge nor be free of temporal dating.Inthe present experiment, this possible objec-tion was eliminated. The semantic-epi-sodic distinction was tested by examiningwhether the transfer effects found withepisodic information apply to the kind ofknowledge that might underlie languageuse. The semantic material was categorical,or set-inclusion, knowledge in which judg-ments are made as to whether an item is amember of a category, such as "A spanielis a dog." The issue is whether studyingepisodic facts about these concepts affectlater semantic verification times. This typeof knowledge was chosen because in addi-tion to its use in comprehension, it has beenthe focus of many experiments (Collins &Quillian, 1969; Holyoak & Glass, 1975;Meyer, 1970; Smith et al., 1974) and has beenimportant in semantic memory theorizing.

Priming

There has been considerable recent re-search on priming effects (e.g., Fischler,1977; Meyer & Schvaneveldt, 1976; Neely,

1977), and it has often been assumed thatthese priming effects are confined to seman-tic memory. Processing of one item isfacilitated if that item is preceded by asemantically related item. Although most ofthe research on priming used connectionssupposedly in semantic memory, there isnow evidence for semantic priming usingepisodic connections. The experiment ofKing and Anderson (1976) can be seen asdisplaying such an effect. The clearestdemonstration of priming with episodicconnections comes from the research ofMcKoon and Ratcliff (1979), which directlycompared priming via episodic and semanticconnections both for lexical decision anditem recognition tasks. In both tasks, equaleffects were obtained from priming bysemantic connections and by episodic con-nections.

Summary of the Literature

This survey of the literature is somewhatmixed, but on the whole it is against a func-tional distinction between semantic andepisodic memory. There are numerousdemonstrations of similar effects in episodicand semantic memory. The experiments ofShoben et al. (1978) claim to show theopposite, but we have argued against someof their conclusions. There are a number ofdemonstrations of transfer between seman-tic and episodic memory that are difficultto reconcile with the distinction. Thereare some failures to find transfer, but, sincethese are null results, they should beweighted less than the positive results. Theencoding specificity effects have been ad-vanced as a demonstration of lack of trans-fer. Though these results are not based onaccepting the null hypothesis, the inter-pretation of encoding specificity is in disputeand similar effects have been obtained en-tirely within semantic memory. The verbal-learning literature in transfer (Kjeldergaard,1968) is full of failures to transfer withinepisodic memory. There seems no reasonto suppose that the semantic-episodicdistinction provides any special barrier totransfer.

Of the two ways to address the seman-tic-episodic distinction, to look for similar


memory effects or to look for transfer fromone memory to the others, we feel that thetransfer results are more persuasive in argu-ing against an episodic distinction. The re-search in this article is directed at showinghow episodic experience affects semanticjudgments. We feel that this is the mostpowerful sort of demonstration givengeneral assumptions that semantic memoryis impervious to influence from episodicmemory.

We were also interested in whether wewould get transfer effects as predicted bythe ACT theory (Anderson, 1976), whichdoes not make a distinction between seman-tic and episodic memory. The ACT theoryprovides a concrete realization of a theorythat makes no distinction. The analysis ofShoben et al. (1978) comes closest to a con-crete theory for these experiments, whichinstantiates the opposite point of view andwe will frequently refer to it. Although theissue is more general than these specifictheories, these theories will serve to bringsome focus to a somewhat vague but stillimportant general issue.

Experiment 1

The general purpose of the first experi-ment was to see whether the time to retrievesemantic information could be affected bythe prior learning of episodic information.The episodic study sentences involved theconcepts that the subject would later haveto verify in semantic probes. These study

sentences varied with respect to their rela-tion to the semantic probes. Following thememorization of these study sentences, sub-jects made categorization judgments of thetest pairs. The dependent measure of in-terest is the reaction time (RT) to theseitem-category pairs. If semantic and epi-sodic memories are functionally separate,learning episodic material should not affectlater retrieval of semantic information. Inaddition to this study manipulation, twoother independent variables, test speedand test block, were orthogonally variedto check some further predictions of ACTrelevant to the semantic-episodic dis-tinction.

The study condition variable is central totesting the semantic-episodic distinction.Examples of the five conditions for trueand false test pairs are shown in Table 1.For a given subject, each test pair wasassigned to one of these five conditions. Inthe control condition, no facts were studiedabout the item or category. The other fourstudy manipulations involved learning infor-mation (adding links) about the item andcategory. In the practice condition, subjectsstudied a sentence that gave informationrelevant to the categorization judgment. Forthe true pairs, subjects studied the exactitem-category information to be testedlater. This manipulation should facilitatethe judgment by strengthening the relevantproposition's links. For false pairs, subjectslearned a sentence in which the item-category subset relation was explicitly

Table 1Examples of Materials Used in Experiment 1

Test pair

True: Spaniel-Dog False: Rose-Insect

Study condition Sentences studied

1. Control2. Practice3. Interference action verb

4. Interference copula verb

5. Spurious connection

A spaniel is a dog.A spaniel retrieves a ball.A plumber pets a dog.A spaniel is not an elephant.A collie is a dog.A spaniel sniffs a dog.

A rose is not an insect.A worker smells a rose.An insect buzzes noisily.A rose is not a drawer.A bee is an insect.An insect flies around a rose.

Note. Each subject saw the sentences for only one study condition for each test pair.


negated. Though this condition gives in-formation that allows the subject to make acorrect categorization judgment, it is notclear that the subject uses such informationin making a false judgment. For instance,none of the falsification processes men-tioned earlier would make use of this in-formation. In fact, by adding links to eachconcept node, it is possible that this manip-ulation might slow down the search pro-cess. Glucksberg and McCloskey (Note 2)reported that explicitly studying that some-thing is not the case will slow subjectsdown in deciding that it is not the case.

For the two interference conditions, sub-jects learned two sentences, one contain-ing the test item and one containing the testcategory. This manipulation should lead toan increase in RT, since the addition of anirrelevant link off each concept node slowsdown the rate of activation. The differencebetween the two interference conditionswas whether the verb was copula (e.g., "is")or an action verb. The primary purpose ofthis manipulation was for design reasons,but it also serves to test a prediction of ACTthat the speed to verify or falsify a proposi-tion does not depend on the verb type.

The final study condition, spurious con-nection, connected the item and category asin the practice condition, but this time by anirrelevant fact. For false test pairs, this con-dition was expected to be especially inter-fering, since it results in an extra intersec-tion that must be evaluated, in addition toadding a link off each node slowing searchtime. For true responses, the prediction ismore complicated. Though here, too, thesearch time for the correct intersection isslowed down and a spurious intersectionmay occur, true responses may also befacilitated by this manipulation. It is pos-sible that additional intersections betweenthe two nodes will lead to more fast guesses(responses made without evaluating theactivated intersection), which happen to becorrect for true test items. For false items,fast guesses of this type are errors. For trueitems, then, the spurious connection con-dition has both interfering and facilitatingeffects, and the relative magnitudes ofthese counteracting influences are notcertain.

In summary, the theory that makes nosemantic-episodic distinction predicts thatthe study manipulation should have animpact on categorization times. At leastsome of the semantic-episodic theoriespredict no effect (e.g., Shoben et al., 1978).Furthermore, some non-semantic-episodictheories such as ACT predict a particularordering on the judgments. For true re-sponses, the ordering, from fastest to slow-est, is practice, control, and interference,with the ranking of spurious connectionuncertain, though slower than practice. Forfalse responses, the ordering is control,interference, and spurious connection,with the exact ranking of the practice con-dition uncertain/though no slower than theinterference and spurious connection con-ditions.

The second variable was test speed. Forboth true and false materials, item-cate-gory pairs were classified as fast or slow,depending on the categorization RT in anearlier experiment (Anderson & Reder,1974). This division was made with theconstraint that the lexical decision RTswere equal in the two groups, so that thespeed difference was presumed to be due tomemory search time. This manipulationallows a test of the ACT explanation forthe results of relatedness on verification oftrue statements, as discussed earlier. TheACT model attributes this result to thegreater strength of the connection betweenthe item and category concepts. The ACTmodel assumes that the rate of spread ofactivation from a node along a particularlink is a function of the strength of thatlink relative to the sum of the strengthsof all links attached to that node. Sincesearch time depends on proportionalstrength, ACT predicts that the strengthen-ing and interfering effects of study will besmaller for the more strongly connectedtest pairs than for the weakly connectedones. We assume that our faster probesare more strongly associated and would re-ceive higher relatedness ratings. So for trueresponses, there should be a Study Con-dition x Test Speed interaction, with largerstudy effects for the slow test pairs.

The test speed manipulation also allowsa test of ACT's explanation for the fact


that relatedness results in slower falsifica-tion times. ACT's explanation for the slowRTs is that strong but irrelevant connectionsbetween the two concepts (e.g., both batsand birds have wings) result in spuriousintersections that must be evaluated. Weassume that slower false items have morespurious intersections. If so, the spuriousconnection condition should not affect theslow pairs much (which already have spuri-ous connections), but it should increase theoccurrences of spurious intersections for thefast pairs. The interference condition shouldalso reduce the difference between the fastand slow pairs. Since adding links to conceptsslows down activation rate, this manipulationwill decrease the probability of spurious in-tersections for the slow items before waitingtime is up. For false responses, then, aStudy Condition x Test Speed interactionis also predicted, but it should be the reverseof the true response case, with a largerstudy effect now expected for the fast pairsthan the slow ones.

The final independent variable was testblock. All test pairs were presented once ineach of four test blocks. ACT and probablyother non-semantic-episodic theories pre-dict definite changes with blocks. For truetest pairs, each categorization judgmentresults in a strengthening of the relevantconnection. As this relevant proposition be-comes stronger, it will come to largelydetermine the RT. The effects of studymanipulation, test speed, and their inter-action will decrease. Also, the RT shouldget faster with blocks due to this strengthen-ing and due to general speedup of encodingand response. Thus, there should be a maineffect of block, and block should interactwith the study condition and the StudyCondition x Test Speed interaction.

Practice should also serve to attenuatethe effects for false test pairs. If a waitingprocess was used, the period of time forwaiting should decrease with practice (asexplained in Anderson, 1976, chap. 8),reducing effects of the other variables. Sofor both true and false test pairs, responsesshould get faster with blocks, and the dif-ferences between study conditions and theirinteractions with test speed should de-crease. This interaction with block is not

predicted by semantic-episodic theorieslike that of Shoben et al.

In summary, the principal purpose of thisexperiment is to test whether there is afunctional basis for the semantic-episodicdistinction. If the study manipulations affectcategorization time, this will be evidenceagainst the distinction. The findings will bemore persuasive if they are the ones pre-dicted by ACT, a model in which there isno distinction between semantic and epi-sodic information. This experiment alsotests some further predictions of the ACTtheory concerning categorization searchprocesses (Study Condition x Test Speedinteraction) and the effects of test repetition(block main effect and interactions). Sucheffects and interaction would be furtherevidence against a semantic-episodicdistinction.

Method

Materials and design. This experiment employedcategorical test pairs and related study sentences.The 40 item-category pairs in the test phase werechosen from the ones used by Anderson and Reder(1974). That study obtained many measures on thestimuli, including item-category verification times(e.g., apple-fruit), item-category falsification times(for re-paired items and categories, e.g., apple-clothing), and lexical decision times for both itemsand categories. Ten pairs were assigned to each offour test conditions, determined by the correct re-sponse (true or false) and the test speed (fast or slow):true fast, true slow, false fast, and false slow. Thirty-nine of the 40 items and categories were paired exactlyas they had been in the Anderson and Reder study.Because of an incompatability between their materialand the constraints of this design, one pair (carrot-bedding) had to be used for which there was no falsifica-tion data available. Because of the lack of relatednessbetween subject and predicate, we assumed that itwould be a fast false. All of the materials are givenin Appendix A.

For the test speed classification, a measure of timefor memory activation was desired. The pairs weredivided such that the item-category verification (trues)or falsification (falses) times for the fast and slowgroups were far apart with nonoverlapping ranges,whereas the lexical decision times were as close aspossible. This presumably should roughly equateencoding and memory access time while distinguishingthe groups on memory activation time. For the trues,the mean verification times for the fasts was 888 msec,and it was 1,063 msec for the slows; the combineditem and category mean lexical decision times were653 msec for the fasts and 668 msec for the slows.For the false test pairs, the mean falsification times


were 927 msec for fasts and 1,103 msec for slows,with mean lexical decision times of 670 and 668 msec.2

In addition to the 40 experimental stimuli shownduring the test phase, 10 buffer pairs were included.

For each of the 40 critical item-category pairs,there were five possible study conditions, which areillustrated in Table 1. Sentences for each of the studyconditions were constructed in the following way: Theitem and category from pairs in the control conditionwere not in any sentences during the study phase.The item and category from pairs in the practicecondition were in study sentences that containedinformation relevant to the categorization judgment,either the exact relation to be tested (for trues) or itsnegation (for falses). The interference conditionsconsisted of two sentences, one with the item andone with the category. The two conditions differedin whether the verbs in the two sentences werecopulas or action verbs. The spurious connectioncondition consisted of presenting the item and cate-gory in the same sentence but the sentence wasirrelevant to the later categorization task. All studysentences were in the present tense and used in-definite articles. It was necessary to present 48study sentences to establish the various studyconditions for the 40 item-category pairs. In ad-dition, there were 12 buffer sentences, made fromthe buffer test pairs, that were shown to all subjects.

Altogether there are 20 experimental conditions (2values of truth x 2 values of speed x 5 study con-ditions). Two of the 10 pairs for each Truth x Speedcombination were randomly assigned to one of the5 study conditions. This random assignment was doneindependently for each subject.

Subjects. Fifty adults, 17-34 years old, from theNew Haven area participated in the experiment ingroups of 1-4. Most were Yale undergraduates. Sixadditional subjects were eliminated because of com-puter failure (1), low accuracy in the study phase (3),or low accuracy in the test phase (2). Subjects werepaid $5 for the experiment which lasted 114-2 hr.

Procedure. Study and test materials were pre-sented, and response times were collected by a PDF11/40 computer with four VT50 terminals, each in aseparate room. The YEPS system (Proudfoot, 1978)was used, allowing multiple subjects to be run inde-pendently at one time.

In the initial study phase, the 60 study sentences(12 buffers followed by 48 critical sentences) were pre-sented 1 at a time on the screen for 15 sec. The sub-ject was told to memorize the sentences by encodingthem as meaningfully as possible, imagining a situationin which someone might have said each sentence.

In the next study part of the experiment, the com-pletion phase, the first few words of each sentence(the sentence subject) were presented, and the subjecttyped in the remaining part. Feedback was given, and,if the response was correct, the beginning of anothersentence was presented 3 sec after the feedback. Ifthe response was incorrect, the full sentence was dis-played and could be studied until the subject pressedthe return key. This procedure was used to allow thesubject as much study time as desired, since mistakesmay have been due to typographical errors as well as

memory failures. The 48 critical sentences were pre-sented for completion in four random orders, precededeach time by a randomized ordering of the 12 buffersentences. This study procedure was self-paced andtook about 70 min (range = 50-110 min).

On completing the study phase, the subjects weregiven instructions on the test phase and began aftera short break. They had not previously been told any-thing about this part of the experiment. Item-cate-gory pairs (e.g., spaniel-dog) were presented on thescreen with two blank spaces between the words. Ifthe item on the left was a member of the category onthe right, the subject was to press the yes button.Otherwise, the subject was to press the no button.The subject sat in front of the terminal keyboard andwas told to respond as quickly as was consistent withbeing accurate. The K key on the keyboard was usedas the yes button and the D key as the no button. Tobe sure that the subject understood, the program haltedafter three practice trials to allow the subject to askquestions about the procedure. Feedback was givenafter each trial for 2 sec, followed 1 sec later by thenext trial. The 40 critical item-category pairs werepresented in four random orders, with each orderpreceded by a random ordering of the 10 buffer pairs.Between each pass there was a minimum 30-sec restperiod that the subject could extend if more rest wasdesired. The whole test phase lasted about 20 min.

Results

The 50 subjects were 97% correct in thefinal pass through the completion phase. Soit seems reasonable to conclude that theyhad learned the study material. The realinterest in the experiment is in the verifica-tion phase. For each subject, RTs for cor-rect responses in each condition (StudyManipulation x Test Speed x Block xTruth) were averaged. To avoid effects ofextremes, times longer than 2 sec (less than1% of data) were set equal to 2 sec. In this

2 We divided material into groups of slow and fastitems rather than high and low similarity because wethought reaction time was a more theoretically neutralbasis for assignment. The contrasting theories of therelatedness effect would prescribe different ratingmeasures as the best way to divide the material.In fact, the groups of items did differ in terms ofsimilarity. Using the ratings of Anderson and Reder(1974), the fast trues had a mean rating of 5.97 and theslow trues had a rating of 5.15 on a scale from 0 to 7,with 7 denoting greatest prototypicality of instance tocategory. This difference was significant, /(79) = 3.51,p < .001, using the variance estimate from the 80 itemsin Anderson and Reder (1974). The slow falses had arating of 1.83, and the fast falses had a rating of 1.21.This was also a significant difference, t(79) = 2.04,p < .05.


Table 2Reaction Time (in msec) in Experiment 1 Collapsed Over Test Blocks

Study condition

Test item

FastSlow

FastSlow

Control

672 (.005)741 (.023)

785 (.013)803 (.050)

Practice

Trues639 (.018)664 (.005)

Falses762 (.013)777 (.048)

Interference

670 (724 (

778 (799 (,

.005)

.026)

.009)

.036)

Spuriousconnection

659 (.003)720 (.023)

776 (.025)813 (.068)

Note. The interference condition means are based on a maximum of 800 observations (800 minus the numberof errors), and all other means are based on a maximum of 400 observations. Error rates are in parentheses.

way long times would have effect on the in Block 1 and 14.1 msec in Block 4. Formean times without any single time having the false responses, the standard errorsan overwhelming effect. The RT means were 25.3 and 20.5 msec. The overall errorand error rates, collapsed over all four rate was .022. For false responses, the errorblocks, are presented in Table 2. The overall rates were positively correlated with RTstandard error for each Study x Test x across conditions (r = .580). For true re-Block cell was 16.7 msec for the true responses, the range of error rates was verysponses and 21.4 msec for the false re- restricted (.000-.040), and there was asponses. small negative correlation (r = -.099). The

The RT means and error rates for Blocks times for the two interference study con-1 and 4 are given in Table 3. The standard ditions have been collapsed in Table 2,errors for the true responses were 21.4 msec Table 3, and in all analyses, because there

Table 3Reaction Time (in msec) for Test Blocks 1 and 4 of Experiment 1

Study condition

Test item Control Practice InterferenceSpurious

connection

TruesBlock 1

FastSlow

Block 4FastSlow

842 (.981 (,

587 (.609 (

,000),040)

,010).010)

733790

565601

(.020)(.010)

(.030)(.000)

768 (,914 (

612 (,615 (

.005)

.040)

.005)

.010)

734912

622625

(.000)(.030)

(.000)(.030)

FalsesBlock 1

FastSlow

Block 4FastSlow

1,035(,1,096(,

643 (,635 (,

,030),120)

,000),030)

875929

681685

(.000)(.080)

(.000)(.050)

916 (947 (

676 (692 (

.005)

.070)

.005)

.015)

918997

685690

(.030)(.150)

(.020)(.030)

Note. The interference condition means are based on a maximum of 200 observations (200 minus the numberof errors), and all other means are based on a maximum of 100 observations. Error rates are in parentheses.


was less than a 3-msec difference overall,and in no block was the difference betweenthe two conditions greater than 1 SE.

Analyses were performed separately fortrue and false pairs. The error terms of allcontrasts to be discussed include only thevariability of the cells involved in the con-trast. Several of the analyses were repeatedafter taking log transformations of themeans. The differences in the outcomes ofthe untransformed and transformed dataanalyses were small, and only the analysesof the untransformed data are reported. Therandomization of materials for each subjectallows the generalization for most contrastsover both subjects and items without theapproximate measures advocated by Clark(1973). For the analysis of the test speedeffects, however, the use of Fmln test wasnecessary because the test pairs were nestedwithin the test speed levels.

The first issue examined is whether thetest speed classification had the expectedeffect. Over the four blocks, for the trueresponses, RTs were about 50 msec fasterto the test pairs in the fast group, Fmln(l,25) = 10.39, p< .01. Though this was asmaller difference than found with the samepairs in the Anderson and Reder (1974)study, an inspection of Table 3 shows thatthe difference was considerably larger in thefirst block (130 msec) than in the fourthblock (16 msec). This decrease in the dif-ference between fast and slow is predictedby ACT in that extra practice should serveto equalize the strength of connection. Forfalse responses, the two test speed levels didnot show a significant difference in RT,^min(l> 23) < 1, although the difference is inthe expected direction. The large error ratesfor the slow false items in Block 1 suggestthe possibility of a speed-accuracy trade-off. An analysis of the error rates after anarcsine transformation showed that sig-nificantly more errors were made to the slowitems, Fmln(l, 23) = 5.59, p < .05. Thismight have also been partially due to morefast guesses in the slow condition, as sug-gested in the introduction. Without the ex-pected main effect in RT, the predictedStudy Condition x Test Speed interactionbecomes impossible to test.

The next result concerns the main effect of

blocks. Overall, there was a significant blockeffect, with subjects speeding up consid-erably both for true responses, F(3, 147) =127.20, p < .001, MSe = .033, and for falseresponses, F(3, 147) =115.78, p < .001,MSe = -058.

The most important results concern theeffects of study manipulation. For trues,the conditions ordered themselves: practice(651 msec), spurious connection (689 msec),interference (697 msec), and control (707msec). The practice condition mean wasfaster than the mean of the other three con-ditions, F(l, 147) = 47.08, p < .001, but thedifferences among the other three conditionswere not significant, F(2,147) = 1.76. Thus,the predicted advantage for the practicecondition was obtained, but the predicteddeficit for the interference condition relativeto the control failed to materialize. Theeffects of the study conditions did decreasewith practice as indicated by a significantBlock x Study interaction, F(9, 441) =6.16, p < .001, and as can be confirmed inTable 3. Although it was considerably re-duced, there was still a significant advantagefor the practice material in Block 4, F(l,147) = 6.21,p < .02. For true responses, thecontrol condition in Block 1 was slower thanboth the practice condition, F(l, 147) =33.85, p < .001, and the interference con-ditions, F(l, 147) = 12.54, p < .001, but byBlock 4 there was no significant differencefor either contrast, F(l, 147) < 1; F(l, 147) =1.22, p > .25. This change over blocks washighly significant for both the practice-control contrast, F(l, 147) = 22.21,p < .001,and the interference-control contrast, F(l,147)= 12.20, p<. 001.

For the false items, the study conditionsordered themselves: practice (770 msec),interference (789 msec), control (794 msec),and spurious connection (795 msec). Thepractice condition mean was again fasterthan the mean of the other three, F(l, 147) =6.79, p < .01, but the other conditions didnot differ, F(2, 147) < 1. There was a highlysignificant, F(9,441) = 8.77, p < .001, inter-action between block and study conditionas indicated by Table 3. Particularly note-worthy is the change in the relationshipbetween the control and the interferenceconditions. In Block 1 the control condition


was significantly slower, F(l, 147) = 27.84,p < .001, whereas in Block 4 it was sig-nificantly faster, F(l, 147) = 4.82, p < .05.Thus, the predicted relationship betweencontrol and interference was obtained in thefinal block. It was also predicted that thespurious connection condition would beworse than the interference condition. Eventhough the reaction time difference was inthe right direction, it was clearly not sig-nificant. On the other hand, the error ratefor spurious connections was .047 comparedwith .023 for the interference condition,F(l, 49) = 6.76, p < .05, MSe = .016. Thus,a speed-accuracy trade-off may have de-creased the RT difference. This accuracydifference might be due to more fast guessesin the spurious connection condition, asmentioned in the introduction.

It is clear that a major unexpected com-plication is the slowness of the controlcondition. It may be that subjects are hurtby a general unfamiliarity with the items inthis condition. Consistent with this inter-pretation is the fact that subjects are 370msec faster in Block 4 than in Block 1 forthe control condition but only 224 msec forthe other study conditions.

A final question of interest is how thisdifference in study condition interacted withtest speed and how this interaction changedwith blocks. Let us consider as our measureof the study effect the difference betweenthe two study conditions predicted to bemost extreme: practice and interference fortrues and practice and spurious connectionfor falses. We report a series of contrastsinvolving these conditions. The expectationwas that the study manipulation would belarger with the less strongly connected items,but that this difference would decreasewith repetition. For Block 1 trues the studycondition effect was larger for the slowpairs, F(l, 49) = 4.45, p < .05, M5e = .022.For Block 4, the difference was small,F(l, 49) = l.lO.p > .25, MSe = .013. Therewas a definite change in the Study Con-dition x Test Speed interaction from Block1 to Block4,F( 1,49) = 6.51,p < .Q5,MSe =.014. For false test pairs, since there wasno significant RT difference between fastand slow pairs, the predictions are not clear.There was no overall interaction, F(l, 49) =

1.06, p > .25, MSe = .022. There was nointeraction in Block 1 or Block 4, nor wasthere any change in the interaction withblocks (all Fs < 1).

Discussion

The experiment found a number of in-stances of transfer between semantic andepisodic memory, indicating that semanticand episodic memory are not distinct: (a)Episodic practice facilitated the making ofsemantic judgments, (b) Although the pre-dicted interference effects often did notmaterialize, there were two examples ofinterference for false judgments. In Block 4the interference condition was slower thanthe control. Overall, the spurious con-nection condition produced higher errorrates, (c) Practice at decision making re-duced prior differences among material andreduced the effects of the study manipula-tion. Note that this contradicts the resultsof Shoben et al., which have been used toargue for the semantic-episodic distinc-tion. These effects were predicted by theACT theory. There was, however, oneeffect predicted by the ACT theory thatwas not obtained—that for trues the inter-ference condition should be significantlyworse than the control. Inspection of Table2 will confirm that if anything, the effect isin the opposite direction. Even though thisoutcome is damning for the ACT theory, itis less clear that it provides much supportfor the episodic-semantic distinction.ACT is only one species of the theoriesthat make no episodic-semantic distinc-tion. Clearly, no such theory is committedto the claim that every episodic manipula-tion will have a semantic effect, and cer-tainly many species would not predict aninterference effect in this circumstance.

The three positive instances of transferlisted earlier argue against a semantic-episodic distinction. This is not to say thatno semantic-episodic theory could predictthese results. However, many including theone articulated by Shoben et al. for this taskwould not.

We were suspicious that the poor per-formance in the control condition may havebeen due to the lack of familiarity of the


items in this condition. The material in theother conditions had been seen five timesduring the study phase. This may havefacilitated the lexical encoding and accessof the words making up these items. Evi-dence consistent with this familiarizationexplanation is that after the first test block,the first time the control items were seen,the control condition sped up more rapidlythan those in the other conditions.

Experiment 2

The second experiment was an attempt toget further evidence about the study con-dition manipulations. We wanted to elimi-nate the potential explanation that the controlcondition was slow simply because of lackof familiarity with the lexical items. We hadthe subjects rate the control categoriesbefore the verification phase of the experi-ment to practice encoding these terms.Lewis and Anderson (1976), who had foundthat subjects learn control material slowerthan interference material in a similar de-sign, had used a prior rating task for theitems that formed the control material.

Another result we wanted to investigatefurther was why subjects got faster and thedifferences among conditions disappearedwith practice. Practice eliminated botheffects due to episodic factors (the studymanipulation) and effects due to semanticfactors (the test speed manipulation). Onechange in the design of Experiment 2 was torun the experiment for six blocks to tracefurther the change in reaction time. A re-lated manipulation was to introduce newtest pairs in the third and fifth blocks. Thiswould enable us to determine if the speedupand decrease in size of effects were due tospecific practice with the items or to moregeneral experimental practice.

Yet another manipulation occurred in thefifth block. Half of the items and categoriesused in negative probes were recombinedto yield true probes. Similarly, half of thetrue probes were switched to be false. Thismanipulation was to get at the issue ofwhether subjects' speedup depended onsomething as simple as remembering theresponse of an item. If it did, subjectsshould suffer interference and perform

worse on these switched probes than onnew probes. In contrast, the ACT analysisof the speedup, which attributes it to thestrengthening of the relevant semantic in-formation, would not necessarily predictthat subjects would perform worse on theswitched probes than on new probes.

Because of the extra test variations tostudy the speedup effect, the variation offast versus slow test items was eliminatedto make it easier to assign materials to con-ditions. Also, two of the study conditionswere deleted—the spurious connectioncondition for the trues and the practice con-dition for the falses. These were the twoconditions for which the ACT predictionswere uncertain. Finally, only one inter-ference manipulation was used, since thetwo types of interference conditions had notdiffered in the previous experiment.

Method

Materials and design. The test materials wereagain taken from Anderson and Reder (1974). Thestimuli were 36 item—category pairs. All of the cate-gories and many of the items had been used in Experi-ment 1. The item-category pairs were grouped intotriplets, constructed so as to maximize the relatednessof categories within a triplet, as judged by the authors.The item-category pairs for true and false responsesare given in Appendix B. Twelve buffer pairs,grouped into four triplets, were also included.

The study sentences were constructed from thetest pairs in the following way, as illustrated in Table 4:For test pairs assigned to either control condition,the items and categories were not included in anysentence shown during the study phase. For testpairs assigned to the true practice condition, thesentences studied included the relevant categorizationinformation in the form "An instance of a Categoryis an Item."3 For the other three study conditions,the manipulations were made over the three test pairsin each triplet. For test pairs in the true interferencecondition, each item appeared in two sentences, oncewith each category in the triplet other than its owncategory. Each category appeared in two sentences,once with each other item in the triplet. This involvedhaving the subject study six interfering sentences forthe three pairs in a triplet. All of these sentencesused transitive verb constructions. For test pairs

3 The practice sentences had been worded "An itemis a category" in Experiment 1. This format waschanged in Experiment 2 to check the uninterestingpossibility that the facilitation in the practice conditionmight be due to a surface match between the testprobe and the sentence studied. In Experiment 2, itemand category order at test is different from the orderat study.


Table 4Example of Materials for Experiment 2

Study condition Sentences studied

True test pair: python-snakeAn instance of a snake is a python.

The python ate a fish.The dog barked at a python.The snake waited for a trout.The collie attacked the snake.

PracticeControlInterference

False test pair: python-dogControlInterference

Spuriousconnection

An instance of a dog is a collie.The trout swam away from a dog.An instance of a snake is a python.The python ate a fish.The dog barked at a python.The python attacked a dog.

Note. For each test pair, subjects studied sentencesfrom one condition. The interference condition studysentences presented also include part of the manipula-tion for other test pairs in the same triplet.

assigned to the false interference condition, thesubject also studied two sentences about the item andtwo sentences about the category. The item sentencesused the other two categories from the triplet, andthe category sentences used the other two items. Oneof the other categories for the item would be the cate-gory that contained the item, and similarly one of theitems for the category would be in that category. Inthese cases the subject was presented with a sentencein the same form as in the true practice condition.This allowed a design such that the subset relationsentences gave no clue as to how the item and cate-gory would later be tested. The other sentences inthe false interference condition involved transitiveverbs connecting item and category. The final studycondition was the false spurious connection. Item-category test pairs assigned to this condition werepresented together in two sentences, one with the itemas the sentence subject and one with the category asthe sentence subject. Two sets of triplets were as-signed to each study manipulation, yielding 42 studysentences (6 for true practice, 12 for true interference,12 for the false interference, and 12 for the falsespurious connection). Fourteen buffer sentences con-structed from the buffer test pairs were included. Allsentences involving transitive verbs were in the pasttense.

The test condition manipulation involved the testblock in which the item-category pair was first tobe presented (Block 1, 3, or 5) and whether the itemsand categories recombined to change the truth of theprobe. Two triplets were assigned to each study con-dition. Within each study condition, one of the tripletswas assigned to the switched test condition and one tothe nonswitched condition. The three test pairs withineach triplet were then assigned to a test condition

determining the block in which it would be introduced.These assignments were randomly made for eachsubject. The number of test condition manipulationsvaried with block: On Blocks 1 and 2 there was one,on Blocks 3 and 4 there were two (whether the itemswere introduced on Blocks 1 or 3), and on Blocks 5and 6 there were four (whether the items had beenintroduced in Blocks I, 3, or 5 or were switched.) In theswitched case one or both terms had been introducedin a prior block.

For the pleasantness ratings, all words (96) to beused in any categorization judgment were included.Two sets of 48 words were constructed with an itemand its true category assigned to different sets. Halfof the subjects were shown each word set first.

Subjects. The subjects were 42 adults, 18-30 yrold, from the Yale University community. Most wereundergraduates. In addition, data from 9 other subjectswere not included, due to computer problems (6), lowstudy accuracy (1), or low test accuracy (2). Eachsubject was given course credit or was paid $5 forparticipating.

Procedure. The computer setup was as in Experi-ment 1.

The procedure had a few changes from the firstexperiment. In the completion phase, there were onlythree passes through the 56 study sentences, and sub-jects had to type only the last word of the sentence,which was always an item or category to be used inthe categorization judgments. These changes wereintroduced to compensate for time increases createdby other aspects of the design. Following the studyphase, subjects rated the 96 words composing the testpairs as to their pleasantness, on a scale of 1 to 9.Though the subjects were not told this beforehand,they were then shown the same words again and wereasked to give each word the same rating as they hadthe first time. These 192 rating responses took about15 min. In the test phase there were two differencesfrom Experiment 1. Since new items were introducedin Blocks 3 and 5, the test block length changed. ForBlocks 1-6, the numbers of trials, including warm-upitems, were 18, 18, 33, 33, 48, and 48, respectively.Subjects had been told when new items would bepresented and were reminded immediately beforeBlocks 3 and 5. Before Block 5, subjects were warnedthat half of the item-category pairings would beswitched.

Results

Subjects were 98% correct in the finalpass through the completion phase. Foreach subject, RTs for correct responses ineach condition in the verification phase(Study Manipulation x Test Condition xBlock x Truth) were averaged. To avoideffects of extremes, times longer than 2.5sec (less than 1% of data) were set equal to2.5 sec. Figures 1 and 2 present a largeportion of the data. Blocks 1 and 2, Blocks3 and 4, and Blocks 5 and 6 were collapsed,


and the data are not presented from theswitched-truth conditions. Each curve inthese figures presents a different test con-dition, with the curves beginning at theblock the test conditions were introduced.The standard errors of the times in thesefigures were 20.1 msec for tubes in Blocks 1and 2, 16.0 msec for trues in Blocks 3 and4, 23.3 msec for trues in Blocks 5 and 6,26.3 msec for falses in Blocks 1 and 2, 21.2msec for falses in Blocks 3 and 4, and 31.3msec for falses in Blocks 5 and 6. Standarderrors were calculated from the Subject xCondition interaction for each block. Thesestandard errors from each block werepooled to get the standard errors reportedfor pairs of blocks. These overall standarderrors were used in forming the statisticaltests. It is important to realize in inter-preting these figures that times becomemore variable in Blocks 5 and 6 becausethey are only half as many observations percondition. The other half of the pairingswere switched.

To simplify the data presentation in thesefigures, we have omitted error rates. Ingeneral, errors were low (.022 for Blocks 1and 2 true, .019 for Blocks 3 and 4 true,.019 for Blocks 5 and 6 true, .067 for Blocks1 and 2 false, .032 for Blocks 3 and 4 false,.024 for Blocks 5 and 6 false) and somewhatunrelated to reaction times for trues (r =

1100

900-

700-

O Controlx Interference• Practice

1 a 2 3 8 4Block

Figure I. Mean reaction times for true judgments inExperiment 2. (Separate functions are plotted for itemsintroduced first in Block 1, for items introduced firstin Block 3, and for items introduced first in Block 5.)

tooo

:900

800

D Controlx Interference• Spurious Connection

3 8 4Block

5 a 6

Figure 2. Mean reaction times for false judgments inExperiment 2. (Separate functions are plotted for itemsintroduced first in Block 1, for items introduced firstin Block 3, and for items introduced first in Block 5.)

.26), and positively correlated with reactiontimes for falses (r = .74). In no case is therea claim based on reaction time that would becompromised by consideration of errorrates.

Let us consider the data in the true con-dition (Figure 1) first. Collapsing the datain Figure 1 over everything but study con-dition resulted in a 767-msec mean in thepractice condition, 781 msec in the controlcondition, and 787 msec in the interferencecondition. With an 8.4-msec SE for thesepooled data, there was a marginally signif-icant difference between the practice con-dition and the mean of the interference andcontrol conditions. Thus, it does appear thatthe practice condition was facilitating rela-tive to the control, but there is no significantevidence that the interference conditionshurt. As Figure 1 illustrates, there was asignificant interaction, F(4, 1230) = 2.38,p < .05, between the three pairs of blocksand the three study manipulations. For thefirst pair of blocks, the difference betweenthe mean of the control and interference


(869 msec.) was significantly, /(164) = 3.01,p < .01, slower than the practice (795 msec).In contrast, there was virtually no dif-ference between the mean of the control andinterference conditions (766 msec) and thepractice condition (761 msec) on later trials.Thus, the overall effect of study, which wassignificant, reflected what happened onthe first trials. It should be noted that Ex-periment 1 found the study manipulationstill significant for trues on later blocks,although that study manipulation was re-duced.

There appears to be some tendency forthe control condition to speed up relative tothe interference condition. Looking at thefirst two blocks when material was firstintroduced, the control material had a mean845 msec and the interference material had amean 832 msec. Looking at the third, fourth,fifth, and sixth blocks, after the materialhas been introduced, the control had a mean716 msec and the mean of the interferencecondition was 739 msec. This interactionwas marginally significant, ?(1230) = 1.52,p < .15. To the extent that this interactionis real, it suggests that we did not entirelysucceed in our efforts to familiarize subjectswith the material in the control condition.

Collapsing the false data in Figure 2 overeverything but study condition, the meanswere 884 msec in the control condition, 926msec in the interference condition, and954 msec in the spurious connection con-dition. With an SE of 11.0 msec, the dif-ferences among all three conditions weresignificant. The ?s for differences among theadjacent pairs were 2.70 and 1.80 (one-tailedtests were used for these planned compari-sons). ACT's predictions of the interferencecondition slower than the control and thespurious connection condition slowest wereconfirmed.

This pattern of the data held up for everyblock. In Blocks 1 and 2, control was 980msec, interference was 1,008 msec, andspurious connection was 1.083 msec (ts of.75 and 2.02). In Blocks 3 and 4 control was859 msec, interference was 900 msec, andspurious connection was 939 msec (ts of1.93 and 1.84). In Blocks 5 and 6 controlwas 868 msec, interference was 917 msec,and spurious connection was 920 msec (ts

of 1.92 and .12). The individual differenceswere not always significant, but they werealways in the right direction. A test ofwhether there was an interaction betweenblocks and study was not significant, F(4,1230) < 1. This contrasts with the true data,which indicated that the study manipulationhad no effect after the first two blocks.

It appears that there was no significantinteraction between specific practice andstudy condition in the false data. The meansfor the first two tests on any test probe,averaged over block, were control, 959msec; interference, 989 msec; and spuriousconnection, 1,027 msec. The means for thethird, fourth, fifth, and sixth blocks were 808msec, 864 msec, and 880 msec. The inter-action between blocks and study condition,as reflected in these numbers, was not sig-nificant, F(2, 1230) < 1. The false data con-trast with Experiment 1, which showed asignificant change in the false study effectswith practice. However, this trend in Ex-periment 1 depended on contrasts involvingthe control or practice condition. In thisexperiment efforts were taken to avoid theinitial lack of familiarity in the control con-dition, and there was no practice conditionfor the false materials. Although clearly notsignificant, the control material did speedup slightly more (151 msec) than the inter-ference (125 msec) or the spurious con-nection (147 msec). This is consistent withthe weak indication in the true data that thecontrol material was not quite equal infamiliarity.

Figures 1 and 2 clearly indicate that thespeedup in reaction time is at least partiallydue to specific practice and not generalspeedup. Table 5 presents the analysis forthe data on Blocks 5 and 6, dividing thedata according to whether the test item wasswitched, and if unswitched whether it wasintroduced on Blocks 1, 3, or 5. Subjectswere 37 msec faster on material that theyhad been practicing since the beginning ofthe experiment than on items introduced inBlock 3, f(656) = 2.32, p < .05, and 110msec faster on these items than on itemsintroduced in Block 5, t(656) = 6.92, p <.001). The switched data were not classifiedaccording to the block of introduction. Be-cause these data came from items and cate-


Table 5Mean Reaction Times (in msec) in Experiment 2 for Blocks 5 and 6

TrueFalse

M

1

6% (.008)837 (.012)766 (.010)

Introduced on Trial

3

740 (.000)866 (.016)803 (.008)

5

822 (.048)1,003 (.044)

913 (.045)

Switched onTrial 5

883 (.039)966 (.071)925 (.050)

Note. Error rates are in parentheses.

gories that were introduced on differentblocks, such a classification would not bemeaningful. The critical question is howthese switched items fare relative to itemsintroduced in Block 5. The new items intro-duced as trues on Block 5 were dealt withfaster than the true items switched fromfalses on Block 5, f(1312) = 3.67, p < .001.In contrast, the new falses on Block 5 weredealt with slower than the falses switchedfrom trues on Block 5, f(1312) = 1.83, p <.05. The explanation of this interaction isthat the switched trues came from originallyfalse items in which there were two in-terfering study conditions, whereas theswitched falses came from originally trueitems in which there was a practice con-dition. Thus, comparing new trues withswitched trues also compares the effectsof practice with the effects of interference.The opposite is the case in comparing newfalses with switched falses. The only way tocompare the switched items with new itemsis to look at an average over trues and falses.These averages represent an equal fre-quency of interference versus practice studymanipulations for both the new items andthe switched items. As can be seen, averageperformance was similar in the two con-ditions. The lack of an effect of switchingcontradicts the hypothesis that subjects'speedup was due to simple storage of aresponse. If so, the switched truth conditionshould have resulted in response inter-ference and poorer performance. Thus thesubjects' speedup in the nonswitched con-dition appears to depend on some speedupin the actual judgment process, consistentwith ACT's expectation that practice wouldfacilitate retrieval of the relevant informa-tion.

Discussion

Like Experiment 1, Experiment 2 foundmany examples of transfer from episodicto semantic memory: (a) There was an effectof episodic practice on a semantic judgmentfor the trues (a replication of Experiment 1).(b) There was a significant interferenceeffect for falses. There was some indicationof this in Block 4 of Experiment 1. (c) Therewas a significant deficit due to spuriousintersections (a replication), (d) Practice atmaking semantic judgments produced aspeedup (replication), which was not due togeneral facilitation of the task or to simpleretrieval of a response, (e) The effects of thestudy manipulation decreased with practicefor the trues (a replication). These resultsare all consistent with the ACT theory.However, again, there are predictions fromthe ACT theory that failed to be confirmed.The serious failure of ACT's prediction wasthe lack of a difference between the controland interference conditions for the trues.

Experiment 3

Experiment 1 found no significant differ-ence between control and interference forthe trues and only a weak indication ofinterference on later blocks for falses. InExperiment 2 we had tried to equate forlexical familiarity for a prior rating task.Here we found no significant difference forthe trues and a significant interfering effectfor the falses. It might be argued that Experi-ment 2 had not completely equated forlexical familiarity. Subjects rated all words,control and experimental, but they had extrastudy exposures for the experimental words.The weak tendency for control to speed uprelative to the experimental conditions is


Table 6Reaction Times for Experiment 3

True False

Condition Fast Slow Fast Slow

ControlInterference

850 (.041)846 (.018)

914 (.026)878 (.020)

934 (.037)964 (.057)

969 (.059)995 (.082)

Note. Error rates are in parentheses.

consistent with this interpretation. The thirdexperiment tried to better equate prior ex-posure in the control and interference con-ditions. To increase the experimental powerwith which we could examine this issue,control and interference were the only studyconditions used. We also increased thenumber of blocks to 10 to augment experi-mental power and to get a better estimateof the effect of practice. Because the designconstraints permitted it, we also reintro-duced the distinction from Experiment 1of fast versus slow items.

Method

Materials and design. The same 40 test pairs wereused as in Experiment 1 (see Appendix A). For eachsubject and each predicate of these pairs, one sen-tence was created with that term as subject and an-other sentence was created with that term involvedin the predicate. These study sentences were createdso that they used two words from the test set—one insubject position and one in predicate. So, in all, 80study sentences were created. In addition there were8 practice test pairs from which 16 study sentenceswere created. The items were randomly divided inhalf to form control and interference material for eachsubject under the constraint that there were an equalnumber of slow and fast pairs in the interferenceand control conditions. So there were 10 pairs in eachof the following four conditions: control-fast, inter-ference-fast, control-slow, and interference-slow.Along with the practice items, a subject had to study48 sentences.

Procedure. The computer setup and general pro-cedure were basically the same as in the previoustwo experiments. The study phase involved study ofthe material and four attempts at completion. Sinceeach word in the interference pairs appeared in twosentences in each pass through the study material,we had the subject rate each item from the controlphase twice in each pass. One rating asked the subjectto assign a pleasantness value to the word, and theother rating involved word frequency. The scale forboth ratings was 1 to 7. The test phase involved 10passes through the 40 pairs. In this experiment thetest pairs were presented in the simple form "item

category." Each test pass was preceded by the 8practice pairs. There was a short rest after each studypass.

Subjects. The subjects were 39 adults from theCarnegie-Mellon University community. Most wereundergraduates. In addition, data from 10 other sub-jects was not included: 2 for computer failures; 7because of failing to achieve the learning criterionof 90% correct; and 1 because his reaction timesaveraged greater than 2 sec. Each subject participatedto earn credit for an introductory psychology courseor for $6. The experiment lasted less than 2 hr.

Results

Subjects were 97% correct in the finalpass through the completion phase. Toavoid effects of extreme times, RTs greaterthan 2.5 sec (less than 2% of the data)were set to 2.5 sec. Errors (4.3% of the data)were excluded in calculated mean RTs. The10 blocks were collapsed into groups as fol-lows: Group 1 was Block 1; Group 2 wasthe average of Blocks 2 and 3; Group 3 wasthe average of Blocks 4-6; and group 4 wasthe average of Blocks 7-10. This was doneto give greater emphasis to first trials andbecause reaction times changed moreslowly during later trials. The mean reactiontimes for the four groups were 1,152 msec,940 msec, 824 msec, and 757 msec.

An analysis of variance was performedusing the conditions defined by the factorialcombination of groups of blocks, speed,truth, and study manipulations. Separateanalyses were performed on reaction timesand accuracy using the subjects' mean RTor mean percentage of error in each celldefined by the factorial design. There werehighly significant effects of all main vari-ables except study condition. Table 6 pre-sents a breakdown of the data accordingto speed, truth, and study manipulation.The standard error of the reaction times was


9.1 msec, and for the percentage of errorit was .0056.

As is clear from Table 6, there was ahighly significant interaction (p < .001) be-tween study condition and truth for bothRTs and error rates. Subjects performedbetter in the interference condition for thetrues but worse for the falses. For re-action times, the difference for trues wassignificant ?(38) = 2.20; p < .05, as was theopposite difference for falses, f(38) = 3.02,p < .005. Similarly, for percentage of error,the difference for trues was significant,f(38) = 2.59, p < .01, as was the oppositedifference for falses, f(38) = 3.84, p < .001.

In contrast to Experiment 1, this experi-ment did obtain a significant effect of thespeed variable on reaction times for bothtrues, f(38) = 5.44, p<.001, and falses,f(38) = 3.08, p < .005. As for accuracy,there was no significant effect of speed fortrues, ?(38) = 1.16, but there was for falsesf(38) = 4.20, p < .001, and there was a sig-nificant interaction between trues and falseswith respect to the effects of speed on ac-curacy, F(l, 38) = 13.27, p < .001. As pre-dicted by ACT, the effect of this speedvariable decreases with practice. (This is incontradiction to the conclusions of Shobenet al., 1978). The Block x Speed interac-tions were highly significant for reaction time,F(3, 114) = 17.42, and significant for per-centage correct, F(3, 114) = 3.67. The meandifference between fast and slow in Block1 was 121 msec, whereas for Blocks 7-10it was 10 msec. Unlike previous experi-ments there was no significant interactionbetween practice and the study manipula-tions for reaction time, F(3, 114) = .54, forthe Block x Study interaction, and, F(3,114) = .58, for the Block x Study x Truthinteraction. However, there was significantBlock x Study x Truth interaction foraccuracy, F(3, 114) = 5.32, p < .005, suchthat the initial accuracy differences dis-appeared with practice.

Discussion

Like the past experiments, this experi-ment has produced numerous demonstra-tions of transfer of episodic experiences tosemantic memory retrieval: (a) The inter-

ference study manipulation proved to have afacilitating effect on the judgment of truesemantic statements. Previous experimentshad failed to get significant results, (b) Theinterference study manipulation proved tohave an interfering effect on the judgment offalse semantic memory statements (a repli-cation), (c) Practice in the experimentserved to reduce differences between fastand slow semantic statements (a replica-tion). Indeed, in this experiment unlike theprior two, there was no major instance ofan episodic manipulation that failed to havesome impact on semantic memory judg-ments. The ACT theory predicted all ofthese effects except the first. ACT predictsthat the interference manipulation shouldinterfere. This prediction failed in the pre-vious two experiments, but there was rea-son to attribute the failure to lack of recentpractice at lexical encoding. It is clear thatthis explanation cannot apply in the currentexperiment. Moreover, rather than no effectof the interference manipulation, it provedto be facilitating—both in terms of reactiontime and error rates.

General Discussion

Before commenting on the general im-plications of these experiments, it is worthcommenting on the small size of the effectson which these conclusions are based.These conclusions are based on reactiontime differences between conditions of aslittle as 20 msec and error rate differencesas small as 1.5%. Particularly with respectto reaction times where the means are aslarge as 1 sec, these seem like very smalldifferences. However, in some cases thesecomparisons are based on as many as 4,000observations. The fact that these episodicmanipulations are weak should not be sur-prising because we were trying to manipu-late strongly encoded semantic memories.Thus, the only reason why this researchwas successful was because it was designedto be able to clearly detect such small dif-ferences.

It is also worth reviewing what we thinkare the empirical conclusions from theseexperiments: (a) Committing to episodicmemory a true semantic fact facilitates its


later semantic retrieval, (b) Committing toepisodic memory irrelevant informationabout concepts does not interfere with andcan facilitate later recognition of semanticfacts about these concepts, (c) Committingto episodic memory irrelevant informationabout concepts interferes with later rejec-tion of false semantic facts about theseconcepts, (d) Committing to episodicmemory facts that introduce spurious con-nections between two concepts makes itharder (than in c) to reject a false semanticfact connecting these concepts, (e) Practiceat making semantic judgments leads to aspeedup that is not due to general taskfacilitation or to simple retrieval of a storedresponse. It is true that all of these resultsdid not appear significant in all experiments,but there were certain methodological dif-ficulties with the first experiment, and it isto be expected statistically that certain realdifferences will prove insignificant on oc-casion. However, we feel that the weightof the three experiments strongly supportsthese conclusions.

It is clear that these results offer littlesupport for the semantic-episodic distinc-tion. The experiments provided abundantexamples of transfer from episodic memoryto semantic memory. Many of these transfereffects are in accord with principles es-tablished for episodic memory (practiceeffects, interference effects for falses) andfor semantic memory (effects of spuriousconnections on falses). To be sure, somesemantic-episodic model could be con-cocted to account for these results, butthe character of that model is not immedi-ately obvious. Certainly, the model ofShoben et al., the most directly applicableto this situation, is contradicted by many ofthese results. In line with arguments madeby Anderson (1976, 1978), it is not possibleto produce empirical data that will rejectall possible semantic-episodic models. Inabsence of this possibility, we have to con-tent ourselves with the observation thatthese results are inconsistent with the spiritand semantic-episodic models (i.e., thatthere should not be transfer between the twomemories and that these memories shouldobey different laws) and are inconsistentwith the known semantic-episodic models.

On the other hand, although these resultsare clearly in keeping with the spirit ofmodels that make no semantic-episodicdistinctions, there is one result that is inserious contradiction to the predictions ofthe ACT theory that we had in mind. Thisis the failure to find an interfering effectfor trues. It should be noted that this resultis contrary to the findings of Lewis andAnderson (1976), who found that episodicinformation interfered with retrieval of bio-graphical facts. There are, of course, manypossible differences between these experi-ments and those of Lewis and Anderson,but we prefer to attribute the differentresults to the difference between semanticand biographical memories. There is noreason why a subject would rehearse a bio-graphical fact about an individual whilestudying a fantasy fact about that individual.For instance, there is no reason to rehearsethat Washington crossed the Delawarewhile studying that Washington was a liberalsenator. On the other hand, it seems reason-able that a subject while studying a sentenceabout a cobra might rehearse the fact that acobra is a snake. Consistent with this issome unpublished data from our laboratoryshowing that learning additional, sup-posedly interfering, information about con-cepts facilitates making semantic consis-tency judgments involving the concepts.

It certainly would not be hard to proposea version of a nonsemantic-episodic modelthat would predict that the implicit rehearsalof semantic information would be suf-ficiently facilitating to overcome any inter-fering effect of the study manipulation. Infact, ACT is such a model under certainassumptions about the beneficial effect ofthe episodic rehearsal relative to the detri-mental effect of the interference. For in-stance, if we assume that the strengtheningof semantic information due to rehearsalwhile studying interfering information isequal to the strengthening of the interferinginformation, then the following analysisapplies: Let a be the strength of the oldsemantic fact, S be the strength of the otherfacts about the concepts, and ^ be theamount by which the old semantic and newepisodic information is strengthened. Re-action time to the old semantic fact will be


a function of the ratio of the strength ofall facts to its strength. Thus verificationtime will vary with (S + a + 2s)/(a + s) =2 + (S - a)l(a + s) which is a negativefunction of s, the amount of episodic study.In this view the better control to assess aninterfering effect is the practice conditionthat involved semantic practice and no inter-ference. There was a significant deficit ofthe interference condition relative to thepractice condition.

Even though the beneficial effect of inter-fering material on trues can be explained inthe ACT framework, it clearly was not pre-dicted. Whether the ACT post hoc explana-tion is correct or not can only be determinedby further research. If the ACT post hocexplanation is correct, the failure of pre-diction points to a weakness in the theory'sability to analyze the semantic processingof a sentence as it is encoded.

Other Issues

Although this experiment was not spe-cifically designed to compare semanticmemory models, it does have implicationsfor a current controversy. To account forthe data from various semantic memoryexperiments, network models (Collins &Loftus, 1975; Glass & Holyoak, 1975) andset-theoretic models (Meyer, 1970; Smithet al., 1974) have been proposed. One mayask how these models could account for theresults of the present experiment. SinceACT is the spreading activation networktheory, network models may obviouslyexplain the results. As another example,the Collins and Loftus model would needan additional structural assumption, thatepisodic information is stored with semanticinformation, but no new processing assump-tions.

The necessary modifications for the set-theoretic models are less obvious. Considerthe most complete model of this type, thefeature comparison model (Rips, Shoben,& Smith, 1973; Smith et al., 1974). In thismodel, decisions are made by comparingthe feature overlap between the test itemand category. To account for the presentresults, study manipulations would have toaffect at least one of the following: acces-

sibility of features, decision thresholds, orthe relative importance of features. Further,one of the strongest points of the featurecomparison model is the ease with which itaccounts for relatedness effects on negativejudgments. The apparent effect of spuriousintersections argues against the feature ex-planation. Although an extension could pre-sumably be worked out, since these networkand feature models may well be isomorphic(Hollan, 1975), it will probably require moreinvolved modifications than the networkmodel.

We would like to conclude with somegeneral comments about the nature of thesemantic-episodic distinction and its moti-vation. Memory distinctions can be of twogeneral kinds, functional or content. Thoughthis classification is not absolute and maybetter be regarded as a continuum, thepurposes and consequences of these twokinds of distinctions are different. A func-tional distinction implies that the memoriesbeing distinguished have different structuralproperties or, perhaps equivalently, thatthey show differential properties in basicmemory phenomena and operations such asdecay, interference, or retrieval. The short-term memory versus long-term memory dis-tinction is believed by many to be an ex-ample of this kind of distinction. Short-termmemory is generally acknowledged to showfaster decay, be more vulnerable to certaintypes of interference, and involve differentretrieval processes.

Content distinctions, however, formalizedifferences in the types of information beingprocessed. Though these may lead to thediscovery of functional distinctions, this isnot their sole purpose. The main reason forproposing content distinctions is to gain newinsights. This goal may be accomplished intwo ways. Simply by conceptually partition-ing the information, the classification maylead to new ways of looking at the issues.A detailed consideration of a particularsubdomain may suggest possibilities thatwould not have occurred otherwise. In thiscase, then, one uses the distinction in thehope of generating new ideas about theproblem.

One may also use content distinctions totry to discover general principles or mecha-


nisms. For example, the observed dif-ferences between words and unrelated letterstrings on tasks such as memory span wereinstrumental in developing the widely usednotion of "chunking" (Miller, 1956).4 Whenmanipulations with different kinds of infor-mation lead to different results, there aretwo possible reasons. One possibility is thatthe memory representations of the two in-formation types (or the operations acting onthem) are qualitatively different. A secondpossibility, however, is that the results arejust two manifestations of the same generalmechanism acting on slightly different kindsof information. If the latter is the case, acomparison of the two results may be animportant clue to understanding the under-lying mechanism.

The point of outlining this classification ofdistinctions is to propose that the seman-tic-episodic distinction has been generallyaccepted as a functional distinction, when itshould have been considered as a contentdistinction. The reasons for this acceptancewith little empirical support are unclear.Perhaps the two areas of research initiallyinvolved such different paradigms, mea-sures, and issues, that a functional dis-tinction seemed only reasonable. This per-ceived functional distinction led to people"working in" semantic or episodic memory.In turn, this situation has resulted in gen-erally separate literature with little thoughtgiven to the similarities and relations. Wehope that one outcome of this research willbe that researchers will consider more care-fully the connection between the twomemories. If there are no functional dif-ferences, all of the principles from one re-search tradition should transfer to the other.This would mean both a considerablesimplification in our understanding ofhuman memory and an increase in what weknow about memory.

4 We thank Paul Kline for suggesting this example.

Reference Notes1. McCloskey, M. Search and comparison processes

in fact retrieval and question-answering. Un-published manuscript, Johns Hopkins University,1978.

2. Glucksberg, S., & McCloskey, M. Advantages of

total ignorance: It's harder to remember that youdon't know than to discover that you don't know.Paper presented at the meeting of the PsychonomicSociety, Phoenix, Arizona, November 8-10, 1979.

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Appendix A

Table AlItem-Category Pairs Used in Experiments 1 and 3

Fast

Cobra- SnakeSpaniel -DogJazz- MusicHarvard - CollegeChair- FurniturePolka- DanceFootball -SportGun -WeaponCar-VehicleAunt- Relative

Slow

TruesShirt-ClothingFireman- Profe ssionCotton -ClothFrance- CountryCake-PastryShilling- MoneyArson- CrimeGrape -FruitGeology-ScienceDoll-Toy

Fast

Cat- StateCancer- FuelRobin- VegetableTermite -BirdLondon - ArtworkDiamond -TreeHammer- JewelTrout-DiseaseCruiser-ToolCarrot-Bedding

Slow

FalsesIdaho-CityPepper- BeverageSheet-AnimalOak-FlowerPetroleum- ShipEtching- DwellingRose-InsectEggnog-FishZinc- SpiceTent- Metal

Appendix B

Table BlMaterial Used in Experiment 2

Item

RenoIdahoFrance

PythonTroutCollie

AppleCarrotCake

ArsonChiselGun

TermitePelicanCotton

RoseOakCat

True

CityStateCountry

SnakeFishDog

FruitVegetablePastry

CrimeToolWeapon

InsectBirdCloth

FlowerTreeAnimal

Category

False

CountryCityState

DogSnakeFish

VegetablePastryFruit

WeaponCrimeTool

ClothInsectBird

AnimalFlowerTree

Item

ZincDiamondPepper

CarPropaneDollar

ConcertoWaltzPainting

LawyerHarvardGeology

PoloCruiserDoll

ShirtTentSofa

True

MetalJewelSpice

VehicleFuelMoney

MusicDanceArtwork

Category

False

SpiceMetalJewel

MoneyVehicleFuel

DanceArtworkMusic

Profession ScienceCollege ProfessionScience College

SportShipToy

ClothingDwellingFurniture

ToySportShip

FurnitureClothingDwelling

Received March 3, 1980

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