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This commentary assesses the degree to which the reinstatement model is homologous to the human experience of relapse.
A review of the literature suggests that the relationship is less clear than is often assumed, largely due to a lack of prospective data on the precipitants and process of relapse (especially relapse to heroin or cocaine abuse). However, reinstatement does not need to resemble relapse to have immediate clinical value; predictive validity as a medication screen would be sufficient. Whether the model has predictive validity is unknown, because, to date, very few clinical trials have tested medications that are effective in the reinstatement model, and even fewer have used designs comparable to those of reinstatement experiments. A clinical trial comparable to a reinstatement experiment would enroll participants who are already abstinent, and its main outcome measure would be propensity to undergo a specific type of relapse (e.g., relapse induced by stress or cues).
Until clinical and preclinical work are more comparable, criticisms of the reinstatement model’s presumed shortcomings are premature.
The reinstatement model has generated a body of preclinical data that grows increasingly substantial and impressive (Shaham et al. 2003). Yet opinions remain divided about its relation to clinical realities (Marlatt 1996; Bergman and Katz 1998). In this commentary, we address the issues of whether reinstatement resembles relapse, whether it can be useful without resembling relapse, and why neither of those questions can yet be answered satisfactorily. We have drawn on clinical literature and on our own experiences working with substance abusers.
In most published discussions of the reinstatement model, attention is drawn to the fact that the most widely studied precipitants of reinstatement in rats (drug priming, drug-associated cues, and stress) are provocatively similar to the precipitants of relapse in humans. This is typically taken as a point of commonality between the reinstatement model and the real-life experiences of recovered addicts. It is tempting to agree without further consideration; the assertion that priming, cues, and stress precipitate relapse is intuitively appealing and seems to accord with clinical experience. But how strong is the evidence that most relapses are precipitated by any of those three factors?
No definitive answer can be found in the clinical literature. Relapse is usually described retrospectively, with weeks or months intervening between the event and its recollection. This leaves ample time for the introduction of recall bias and the formation of post hoc explanations for the reporter’s behavior. As an only slightly tangential illustration of the problem, consider the intuitively plausible prediction that abused children are at increased risk for later addiction. The prediction is confirmed when adult addicts are asked retrospectively about their childhoods—but not when abused and nonabused children are followed prospectively for incidence of addiction (Widom et al. 1999). This paradox may reflect a human tendency to ascribe one’s behavior to something that seems, in hindsight, to make sense. In the case of relapse, the constructs that make sense to investigators (such as “stress-induced relapse”) may be the same constructs that make sense to addicts as they try to piece together reasons for having relapsed.
The problems inherent in recall of relapses are surmountable by appropriate design and methodology. In studies of tobacco smokers, a technique called Ecological Momentary Assessment (EMA) has been used to enable outpatients to report their activities and moods before a lapse or relapse,1 prospectively and in real time, using handheld data-collection devices (Shiffman et al. 1996). When EMA data are compared with retrospective reports gathered 12 weeks later from the same patients, large discrepancies emerge in reported triggers, activities, and moods during lapses (Shiffman et al. 1997). These discrepancies cannot be reliably correlated with patient characteristics, episode characteristics, or degree of confidence in recall accuracy (Shiffman et al. 1997). Reassuringly, EMA data in smokers tend to confirm that lapses and relapses are associated with smoking-associated cues and with negative mood (Shiffman et al. 1996), supporting assertions often made in support of the reinstatement model (if negative mood can be considered roughly homologous to stress). Similar, though less direct, findings were reported in an EMA study of alcoholics: negative mood predicted urge to drink, which, in turn, predicted drinking (Litt et al. 2000).
Will the same be true for heroin and cocaine? In the absence of real-time data, we are forced to rely on a small body of prospective studies whose time frames were not sensitive to episodes of acute stress. The general finding has been that prospective measures of stress predict lapse or relapse only when aggregated over time frames of 3 to 12 months, not (for example) week by week (Hall et al. 1991; McMahon 2001; Wasserman et al. 1998). Clearer evidence for acute-stress-induced (or cue-induced) relapse seems likely to emerge with real-time monitoring, but the issue has yet to be resolved empirically.
The questions raised in Sect. 1 concern the model’s face and construct validity, and although these questions are important, they may not be the first priority from a clinical point of view. More urgent is the question of predictive validity—whether the model can screen treatment medications. As scientists, of course, we are also interested in models with sufficient construct validity to help elucidate the pathophysiology of relapse. But as clinicians, we want treatments that work, and we do not immediately insist upon the relative luxury of knowing why they work.
Sarter and Bruno (2002) have argued that this approach is too myopic—that if a model has predictive validity without construct validity, it will find some of the right medications “for the wrong reasons” and miss other medications with novel mechanisms of action. The example cited was buspirone, an anxiolytic whose clinical efficacy was not predicted in traditional animal models of anxiety. In response, we would point out that anxiety disorders have long been pharmacologically treatable, while addiction relapse is not. Because no medication is available for relapse prevention, the field would be significantly advanced by a model that finds even one.
At what point, then, should a model of relapse be decreed inadequate? Reasonable guidance is available in an earlier review by Sarter et al. (1992) on animal models of amnesia as behavioral screens for cognitive enhancers. The review showed that the models were amassing an “overwhelming number” of false positives—medications that appeared promising when screened, but which failed clinical trials. An accumulation of false positives is a clear sign that a model needs refinement or abandonment, at least in its role as a screen for medications. From the point of view of treatment providers, this is the ground on which the reinstatement model will stand or fall.
The reinstatement model has generated a large body of data on pharmacological interventions that prevent reinstatement; some of these data are summarized in Table 1. How do they compare with homologous data from clinical trials?
Currently, almost no such comparisons are possible. A clinical trial homologous to the reinstatement model would enroll former users who are currently abstinent (we leave aside, for now, the question of how abstinence is achieved) and would assess propensity to lapse or relapse. Clinical trials answering to the above description are startlingly rare, and the few that do exist have usually tested medications never tested in the reinstatement model. The lack of overlap can be seen by comparing Table 1 and Table 2. (Space limitations preclude a full discussion of the material in the tables, but the main purpose of the tables is illustrative.)
The closest points of overlap between preclinical and clinical work can be found in the alcohol literature. The findings appear, at first, to be mixed. Naltrexone, which blocks reinstatement (Lê et al. 1999; Ciccocioppo et al. 2002), has also been shown to prevent relapse in alcoholics (Streeton and Whelan 2001; Latt et al. 2002)—a finding that seems encouraging, except that the effect size is modest. Fluoxetine, which also blocks reinstatement (Lê et al. 1999), fails to prevent relapse in alcoholics (Kranzler et al. 1995). A reasonable explanation for the negative finding with fluoxetine, and for the modesty of the findings with naltrexone, is that each medication blocks only particular subtypes of reinstatement. As shown in Table 1, fluoxetine blocks reinstatement when the precipitant is footshock stress, but not when the precipitant is a priming dose of alcohol (Lê et al. 1999); naltrexone blocks reinstatement when the precipitant is a priming dose of alcohol (Lê et al. 1999) or an alcohol-associated cue (Ciccocioppo et al. 2002), but not when the precipitant is footshock stress (Lê et al. 1999). In the clinical trials cited here, the hypotheses were not precipitant-specific, and the trials were designed, powered, and analyzed accordingly (with no attempt, for example, to separate subtypes of relapse using EMA).2
In the literature on nicotine, cocaine, and heroin, we found no clinical trials assessing the relapse-prevention efficacy of medications that have been shown to block reinstatement.
If the search criteria are broadened to include clinical trials that did not literally examine relapse prevention, there emerges another modestly encouraging overlap between preclinical and clinical data: baclofen, which blocks priming-induced reinstatement of cocaine seeking in rats (Campbell et al. 1999), has also been shown to decrease cocaine craving and use in outpatients (though this was in an open-label pilot with only ten participants) (Ling et al. 1998). A more ambiguous case is that of buprenorphine, which appears to block priming-induced reinstatement of cocaine seeking in rats (Comer et al. 1993), but may not reduce cocaine use in humans (Compton et al. 1995; Schottenfeld et al. 1997). This apparent false positive may be explicable in terms of buprenorphine-induced motor deficits in the rats (Y. Shaham, personal communication), or it may turn out not to have been false: data from our clinic support the possibility that buprenorphine slightly reduces cocaine use in methadone-maintained polydrug abusers (Montoya et al. 1996), and that this effect is statistically dissociable from its effect on heroin use (I.D. Montoya et al. submitted). The baclofen and buprenorphine findings do not strongly support the predictive validity of the reinstatement model, but neither do they constitute the “overwhelming number” of clear predictive failures for which Sarter et al. (1992) criticized other animal models.
In other clinical trials that did not literally assess relapse prevention, there is possible evidence that the reinstatement model has produced true negatives. For example, bromocriptine reinstates cocaine seeking in rats (Wise et al. 1990), and is not effective against cocaine abuse in clinical trials (Handelsman et al. 1997; Montoya et al. 2002). Similarly, the corticosteroid-synthesis inhibitor metyrapone reinstates heroin seeking in rats (Shaham et al. 1997), and the corticosteroid-synthesis inhibitor ketoconazole is not effective against cocaine or heroin abuse, perhaps even exacerbating them (Kosten et al. 2002). The detection of true negatives could support the specificity of the reinstatement model as a medication screen, but the homology between the preclinical and clinical data is incomplete: the clinical trials comprised patients who had not yet become abstinent, and thus they assessed the real-life homolog of self-administration rather than that of reinstatement. In rats, a drug that has no effect on the former may nonetheless block the latter (Shalev et al. 2002); the same may be true in humans. Therefore, even these negative findings are far from definitive.
If the search criteria are further broadened to include human laboratory studies, there are some additional points of overlap between the reinstatement literature and the human literature, but new complications arise. For example, reinstatement of cocaine seeking in rats is blocked by either ABT-431 (Self et al. 2000) or SCH 39166 (ecopipam) (Khroyan et al. 2000; Ciccocioppo et al. 2001),3 and each of these has been tested in human laboratory studies. However, as shown in Table 3, cross-species comparison is impeded by differing administration schedules. For example, ABT-431 blocks reinstatement more effectively after chronic administration (Self et al. 2000), but the one published human laboratory study used acute administration only, leaving open the possibility that chronic administration would be more effective (Haney et al. 1999). Conversely, for ecopipam, human chronic-administration data are available (Haney 2001), but there are no chronic-administration reinstatement data with which they can be compared.
The tendency among preclinical investigators to screen medications with acute administration may be problematic, because in a clinical situation, those medications would be administered chronically. But there is a broader barrier to interpretation of the findings shown in Table 3, a barrier that would stand even if all the studies had used comparable schedules of administration. The human laboratory studies rely on surrogate endpoints that have sometimes turned out not to predict human behavior in daily life (Teoh et al. 1994; Weiss et al. 1995) or to predict it only weakly (Litt et al. 2000). Humans are aware that what happens in the laboratory is only a simulation of daily life, and that daily life will continue unchanged when the experiment ends. For a laboratory animal, the laboratory is the whole of life; the choices the animal makes within the context of a model are choices about its own survival. In that sense, a good animal model may be less far removed from day-to-day human life than a human psychopharmacological experiment is. None of this should be taken to deny the unique advantages of the latter (such as the experimenter’s ability to give verbal instructions and collect verbal responses). But either approach requires a validity check against the gold standard of prospectively monitored day-to-day human behavior.
As the preceding section shows, there is a remarkable paucity of overlap between the approaches used in reinstatement research and in clinical research on relapse prevention. Clinical and preclinical investigators can each help to narrow the gap.
Preclinical investigators could direct more of their efforts toward medication screening. Much of the research on the reinstatement model involves characterization of the mechanisms of reinstatement, such as the brain regions involved. This work is inherently interesting, but it is unlikely to help validate reinstatement as a model of relapse, because most of it cannot be done in humans. (Of course, it might be useful insofar as it suggests new medications to be tested in the model, and thereafter in the clinic.) Preclinical investigators should also keep an eye toward the ecological validity of their screening. For example, does the medication block reinstatement at a dosage whose interspecies-scaled equivalent is likely to be tolerated in humans? Does it continue to block reinstatement when administered chronically, as it would be administered in clinical practice?
Clinicians, meanwhile, should let the results of such screening guide their future clinical trials—in terms of participant selection, study design, choice of medication, and specificity of outcome measures. Participants should be abstinent former users; studies should center on real-time prospective evaluation of propensity to lapse and relapse. As for the choice of medication, Table 1 shows a large menu of potential medications suggested by preclinical studies. As mentioned earlier, most medications block only subtypes of reinstatement; thus, their specificity needs to be accounted for through a priori decisions about how relapse precipitants will be measured and classified, and studies need to be powered accordingly.
The multifactorial nature of relapse and the specificity of reinstatement-blocking medications suggest that treatment may require polypharmacy. Therefore, clinicians and preclinical investigators should focus on medications without known propensities for adverse interactions with other medications.
From both ends—preclinical and clinical—the homology between drug-seeking behavior in rodents and in humans needs continued elucidation. One obstacle to that elucidation is the point of view wherein terms such as descriptive are used pejoratively. Science begins with good descriptions (Sidman 1960), and for relapse, there is much more describing to be done. The most obvious gap is the absence of real-time data on relapse in heroin and cocaine addicts. Collection of EMA data with handheld electronic devices has its drawbacks, but most of those drawbacks can be overcome (Litt et al. 1998); investigators who are reluctant to issue expensive EMA equipment to illicit-drug abusers should note that this has been done successfully with Ecstasy users (Lukas et al. 2002) and homeless crack cocaine users (Freedman et al. 2002).4 Large-scale longitudinal EMA studies may help resolve issues of face and construct validity in the reinstatement model.
One such issue is that cessation of drug intake in the reinstatement model is the result of an extinction procedure rather than the result of choices made in a multioperant environment (which, for humans, would include entering treatment). This should matter only if the degree of choice involved in initial abstinence alters the precipitants or process of subsequent relapse. Perhaps insight could be gained through prospective assessment of relapse in addicts whose abstinence was initiated under different circumstances, such as self-initiated quitting, psychosocial treatment, depot-naltrexone injection, or involuntary inpatient (or in-prison) detoxification. (To our knowledge, relapse in former prisoners has been assessed only retrospectively, with emphasis on baseline predictors rather than on acute precipitants; Hiller 1996.) If the circumstances of abstinence initiation do make a difference, perhaps the reinstatement model could be refined so that it does not rely on extinction. For example, robust self-administration of drug might be reducible with the introduction of a high-magnitude nondrug reinforcer (as shown in rhesus monkeys by Nader and Woolverton 1991); preference for drug might then be reinstateable by a stressor. Potential relapse-prevention medications could then be screened for their ability to block the effect of the stressor.5
Another issue addressable by good descriptive data is whether humans show “incubation” of the propensity to relapse. In a procedure similar to that used in the reinstatement model, rats withdrawn from cocaine show a progressive increase in cue-induced responding for cocaine (in the absence of actual delivery of cocaine) over the course of 60 days. The clinical implications of this finding seem less dispiriting in light of the observation that responding returns to its initial low levels within 180 days (Y. Shaham, unpublished data). But the clinical occurrence of the phenomenon has yet to be demonstrated at all. One difficulty inherent in trying to demonstrate it is that each outpatient can have only one relapse per period of abstinence, leaving no way to know whether craving would have grown stronger beyond the point when the relapse occurred. It might be possible to study incubation in addicts released from settings in which they have undergone involuntary abstinence; if incubation occurs, latency to relapse should follow an inverted-U-shaped distribution as a function of the length of involuntary abstinence.
Finally, it might also be reassuring to extend the reinstatement/relapse homology to purely behavioral interventions. For example, relapse to heroin use in humans can be delayed or prevented with alternative reinforcers (Gruber et al. 2000). Can alternative reinforcers also block reinstatement? In one study, priming-induced reinstatement of cocaine seeking was not blocked by the presence of sucrose in the cage (Gosnell 2000). But in pilot work with a single rat, food-deprivation-stress-induced reinstatement (and responding during extinction) was blocked by access to toys (Y. Shaham, unpublished data). This line of research may not look especially alluring to most preclinical investigators, but its clinical relevance seems clear.
Most of the questions and issues raised in this commentary could be resolved by increased “crosstalk” between clinical and preclinical researchers. At an institutional level, there are instances of support for bench-to-bedside research. For example, in the US, the National Institute on Drug Abuse has established a funding mechanism called SPIRCAP (Strategic Program for Innovative Research on Cocaine Addiction Pharmacotherapy), and the National Institutes of Health have an intramural initiative called, fittingly, Bench to Bedside. However, recent Bench to Bedside awards do not appear to include any studies of addiction (Gallin et al. 2003). A brief search of the CRISP database of federally funded biomedical research projects (CRISP 2003) revealed no relapse studies of the kind we have suggested here, except for some studies of the natural history of cocaine dependence and predictors of relapse (which do not appear to include EMA) and some clinical trials of bupropion or nicotine replacement for prevention of smoking relapse in postpartum women. Although there is justification for testing those agents for smoking relapse, that justification does not come from the reinstatement model, where neither agent has apparently been tested.
In pointing out the gap between bench and bedside, we intend no criticism of investigators on either side. Translational research faces a daunting barrier in information overload, and as journals and scientific organizations respond to the overload by becoming more specialized, the barrier only grows greater. It is understandable that preclinical investigators are not fully familiar with the patients and settings to which their work is meant to generalize; it is equally understandable that clinical investigators are not fully familiar with the ways in which preclinical work is conceptualized and carried out. But this shared lack of familiarity is now a rate-limiting step in validation of the reinstatement model. Until it is overcome, conclusions about the model’s value to patients, or about its lack thereof, are premature.
We thank David Gorelick, M.D., for helpful comments on the manuscript.
1In this commentary, lapse indicates any use of a drug by an individual who has been abstaining from that drug; relapse indicates a return to compulsive or harmful patterns of use. Operational definitions of these terms vary across studies
2The alcohol literature also includes at least two relapse-prevention trials using acamprosate (Sass et al. 1996; Tempesta et al. 2000), which has been screened (with positive results) in the alcohol-deprivation model (Spanagel et al. 1996; Holter et al. 1997; Heyser et al. 1998). The alcohol-deprivation model differs from the reinstatement model in that there is no operant extinction procedure and alcohol is available again during the postdeprivation session (Lê and Shaham 2002)
3ABT-431 and ecopipam are, respectively, an agonist and an antagonist at D1 receptors. The seeming paradox of their common effectiveness is discussed by Alleweireldt et al. (2002)
4The EMA study by Freedman et al. (2002) focused on the feasibility of issuing and recovering equipment; no data on the process of relapse were reported
5This suggested model is admittedly unsatisfying in several respects. The most obvious is that most animals would continue to self-administer some amount of drug throughout the experiment, thus sacrificing one of the major strengths of the reinstatement model: its ability to separate drug-seeking behavior from the pharmacological effects of the drug. The suggested model would also be unsuitable for assessment of priming-induced reinstatement. Still, this line of research could be useful for determining whether reinstatement in laboratory animals differs depending on the circumstances of cessation