Published on 18 September 2026
EMDR and substance use disorders: how solid is the signal on craving?
The essentials
A systematic review with meta-analysis published on 17 September 2025 in Frontiers in Psychiatry pools 14 studies, 327 patients treated with EMDR and 322 controls. Craving falls with a moderate effect size, g = 0.55 [0.40, 0.70], for a reported heterogeneity of I² = 35%, an estimate carried by 22 effect sizes from 9 of the 14 studies. Post-traumatic stress symptoms (g = 0.69), depressive symptoms (g = 0.64) and anxiety symptoms (g = 0.72) move in the same direction, but each of these three results rests on only four to five effect sizes, drawn from three to five largely overlapping studies. Addiction severity itself does not move: g = 0.14 [-0.20, 0.48], not significant. These figures rest on a body of evidence whose fragility the authors themselves describe. Of the eleven randomized trials assessed with RoB 2.0, seven are rated at high risk of bias, two at some concerns, and only two at low risk; the single randomized crossover trial is also rated high risk, and the two non-randomized studies are rated at serious risk. Egger’s test is significant for craving (p = 0.024), precisely on the outcome that carries the clinical interest of the work. Comparators are heterogeneous: usual care, a sham procedure, recall only, no treatment, or cognitive behavioral therapy alone, depending on the trial. Comparator type was tested as a moderator, with no difference found between active and passive controls, but this comparison operates on whole studies rather than on randomly allocated patients. No quantitative synthesis of extended follow-up could be conducted, for lack of a sufficient number of studies reporting it. What this work documents is a convergent signal on weak data. The cautious reading is that of a plausible adjunct in the dependent patient carrying an active trauma history, not a validation of EMDR in addictions.
The context
The overlap between substance use disorder and psychological trauma is a commonplace of clinical practice. In a patient with alcohol dependence, the question of whether to treat the addiction first, the trauma first, or both together, arises in almost any reasonably long-term care relationship, and often without a clear answer. The historically cautious position was to stabilize substance use before opening trauma work, on the grounds that reliving traumatic memories might trigger relapse. This position never rested on solid trials, only on clinical experience and a reasonable concern.
EMDR occupies a particular place in this landscape. It is a structured, widely disseminated psychotherapy whose role in post-traumatic stress disorder is well established. Its extension to addictive behavior, however, rests on a theoretical wager: if craving is partly a conditioned response to charged memories and emotional states, then reprocessing those memories might dampen its intensity. The idea is appealing, which is exactly why it deserves to be examined with rigor.
The work analyzed here sits inside this question. It does not ask whether EMDR treats addiction; it asks on which dimensions of the clinical picture EMDR moves something when offered to patients with a substance use disorder. The distinction is not rhetorical. A treatment that reduces craving and emotional intensity without changing the severity of the disorder does not occupy the same place in a care strategy as a disease-modifying treatment, and is not prescribed to a patient in the same terms.
Method note: what a pooled g does, and does not, tell you
The first issue concerns the comparators. The included trials do not pit EMDR against the same thing: depending on the study, the control group receives usual care, a sham procedure, simple recall, no treatment, or cognitive behavioral therapy alone. No waitlist condition appears among the included studies, contrary to what the eligibility criteria might suggest. These conditions do not measure the same object. An effect obtained against no treatment folds in everything that simply being cared for provides: clinical attention, expectation of benefit, time spent. An effect obtained as an addition to a properly conducted cognitive behavioral therapy measures something else, a genuine add-on effect over an active treatment, which is a far heavier requirement. The authors tested the question, and credit is due for that: comparator type, active versus passive, does not moderate the effect on craving, beta = 0.008 [-0.299, 0.315], p = 0.958. This null result does not amount to equivalence, though. It operates on nine whole studies rather than on randomly allocated patients, its power is very low, and only one of the fourteen studies compares EMDR added to an addiction-focused psychotherapy against that psychotherapy alone. The g = 0.55 therefore remains an average across different comparison situations.
The second issue concerns the nature of the effect sizes themselves. They are reported as Hedges’ g, calculated on the difference in change scores between the treated and control groups, following the Cochrane Handbook’s recommendations, with a conservative convention when the standard deviation of change was missing, the correlation between baseline and endpoint measures then being set to zero. Two consequences follow. The first is reassuring: the estimate is indeed a between-group comparison rather than a raw within-group change, so that the passage of time, regression to the mean and the specific effect of ongoing withdrawal weigh on both arms and largely cancel out. The second calls for caution: several estimates were reconstructed from incomplete data, which widens confidence intervals rather than narrowing them, and the choice to start from change scores rather than post-treatment means, which the authors themselves claim as an improvement over earlier meta-analyses, makes the values difficult to compare term for term with those already published.
The study at a glance
| Population | Adults with a substance use disorder: alcohol, other drugs, nicotine. 327 participants in the EMDR groups, 322 in the control groups. Four of the fourteen studies included participants exposed to trauma or carrying a diagnosis of post-traumatic stress disorder. No studies in children or adolescents. |
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| Intervention | EMDR in three forms: addiction-focused in nine studies, trauma-focused in four, mixed in one. 1 to 12 sessions, 50 to 90 minutes per session, once or twice a week. |
| Comparator | Heterogeneous across trials: usual care, sham procedure, recall only, no treatment, cognitive behavioral therapy alone. No waitlist condition among the included studies. The active or passive nature of the comparator was tested as a moderator of the craving effect, with no difference found. |
| Outcomes | Craving, addiction severity, post-traumatic stress symptoms, depressive symptoms, anxiety symptoms. Effect sizes as Hedges’ g, calculated on the difference in change scores between groups. |
| Design | Systematic review with random-effects meta-analysis, restricted maximum likelihood estimation. 14 studies included: eleven randomized trials, one randomized crossover trial, two quasi-experimental studies. 22 effect sizes for craving. PROSPERO registration CRD420251070837, conduct declared compliant with PRISMA with a completed checklist provided as supplementary material, seven bibliographic databases searched plus one thesis database. Risk of bias assessed with RoB 2.0 and ROBINS-I. Meta-regression and subgroup analyses. |
Quality control
| Registration and conduct of the review | Solid Protocol registered on PROSPERO under number CRD420251070837, PRISMA framework claimed with a completed PRISMA 2020 checklist provided as supplementary material, seven bibliographic databases searched, supplemented by a thesis and dissertation database for grey literature. The registration date does not appear in the publication: the prospective nature of the registration cannot be established from this document, even though the limitations section, which flags protocol-specified outcomes that could not be analyzed for lack of data, points in that direction. |
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| Risk-of-bias assessment | Solid Tools matched to each study design: RoB 2.0 for randomized trials, its crossover variant for the relevant trial, ROBINS-I for non-randomized studies. Domain-by-domain tables are published as supplementary material. The assessment is done seriously, and it is precisely what reveals the weakness of the body of evidence. |
| Statistical apparatus | Solid Random-effects model, confidence intervals, I², tau-squared and H-squared heterogeneity indices, meta-regression, subgroup analyses, Egger’s test, Kendall’s test, fail-safe N, influence analyses via standardized residuals, DFFITS and Cook’s distance. |
| Primary study quality | Weakness Seven of the eleven randomized trials assessed are at high risk of bias, two at some concerns, two at low risk. The crossover trial is at high risk. The two non-randomized studies are rated at serious risk. The domains at issue concern randomization, missing data and selection of the reported result. Only the outcome-measurement domain is judged low risk across the eleven randomized trials. |
| Publication bias | Caution Egger’s test significant for craving (p = 0.024) and for post-traumatic stress (p = 0.029), Kendall’s test not significant in either case. The fail-safe N needed to nullify the result is high for craving (654), much more modest for the other domains (44 for post-traumatic stress, 15 for depression, 17 for anxiety), which partially reassures without lifting the observed asymmetry. |
| Time horizon | Not synthesized Pooled effects are end-of-treatment effects. Too few studies report follow-up for a quantitative synthesis to have been conducted, and relapse and treatment adherence, both specified in the protocol, could not be analyzed for lack of data. The durability of the benefit is therefore neither established nor excluded. |
The results
Pooled effect size on craving, g = 0.55 [0.40, 0.70], I² = 35%, from 22 effect sizes drawn from 9 of the 14 included studies. A moderate effect with contained heterogeneity, but drawn from a body of evidence in which seven of eleven randomized trials are at high risk of bias, and accompanied by a significant Egger’s test on this very outcome.
| Craving | g = 0.55 [0.40, 0.70], I² = 35%, 22 effect sizes, 9 studies. PEB read: A moderate, significant effect, with modest heterogeneity for such a disparate body of evidence. This is the result that carries the whole work, and it is also the one on which the publication-bias signal weighs most. One nuance matters: several studies contribute three or four effect sizes drawn from the same sample, which introduces a dependency between estimates that the model used does not account for, and artificially tightens the interval. |
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| Post-traumatic stress symptoms | g = 0.69 [0.36, 1.02], I² = 20%, 5 effect sizes, 4 studies. PEB read: The domain where EMDR is otherwise best established. An effect in this register among addicted patients is coherent; it is not a discovery and does not on its own validate the extension to addictive behavior. The estimate is above all fragile: its highest value, g = 2.01 [0.62, 3.40], comes from a pilot trial of twelve patients, while the largest trial in the set, the only one to use a clinician-administered scale, gives the lowest value, g = 0.45 [0.05, 0.84]. One of the five effect sizes moreover measures dissociation rather than post-traumatic stress severity. |
| Depressive and anxiety symptoms | g = 0.64 [0.25, 1.03] and g = 0.72 [0.35, 1.10]. PEB read: Effects of similar magnitude, each resting on four effect sizes, drawn from four studies for depression and three for anxiety. These are largely the same studies as for post-traumatic stress, and these dimensions correlate strongly with one another: these are not independent results confirming each other, but very likely several measurements of the same emotional improvement, in the fraction of the corpus selected for trauma comorbidity. |
| Addiction severity | g = 0.14 [-0.20, 0.48], not significant, I² = 51%. PEB read: No difference demonstrated. This does not prove the absence of any effect: the outcome rests on four effect sizes from only three studies, the corresponding power is low and heterogeneity is moderate. But as it stands, nothing warrants saying that EMDR changes the severity of the disorder. |
| Moderator, population | Alcohol greater than smokers, beta = 0.387 [0.117, 0.657], p = 0.005. PEB read: A comparison between studies, not between randomized patients. A meta-regression of this kind generates a hypothesis; it does not establish one: alcohol trials and tobacco trials also differ in their populations, intensity of care and methodological quality. The authors themselves offer a simple explanation, that the smokers included had no diagnosis of nicotine dependence and therefore started from a lower level of craving. The other-substances group, meanwhile, does not differ from smokers, beta = -0.178 [-0.955, 0.600], p = 0.655. |
An important point: the dissociation between craving, which moves, and addiction severity, which does not. Two interpretations remain open, and the available data do not allow a choice between them. Either EMDR genuinely acts on emotional load and on the urge to use without this translating, at this point, into a change in consumption behavior. Or craving scales, more subjective, more sensitive to the expectation of benefit and often collected unblinded, capture an improvement that severity measures, more anchored in observable behavior, do not confirm. The second hypothesis is all the harder to dismiss given that seven of eleven trials are at high risk of bias, with, notably, problems of missing data and selective outcome reporting. In a psychotherapy trial, blinding the patient is structurally impossible, and it is precisely the self-reported outcomes that suffer most from this. It should be added that the two sets of studies only partly overlap: craving is documented by nine studies, severity by three, and nothing guarantees that the same patients were followed on both fronts.
Critical appraisal
| Primary study quality | Major weakness. A meta-analysis does not correct the bias of its sources, it tightens their confidence interval. Pooling seven high-risk trials produces a more precise estimate, not a more accurate one. One element does count in its favor: on craving, the estimate restricted to randomized trials is higher than that of the crossover and quasi-experimental designs, g = 0.67 [0.46, 0.88] against g = 0.38 [0.20, 0.55]. The gradient therefore does not point toward an effect manufactured by the weakest designs. It remains that the randomized trials themselves are mostly at high risk of bias, which limits the reach of this comparison. |
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| Comparator heterogeneity | Strong caution. Usual care, sham procedure, recall only, no treatment and cognitive behavioral therapy alone do not ask the same question. The analysis exists and finds nothing: whether the comparator is active or passive does not moderate the effect on craving (beta = 0.008 [-0.299, 0.315], p = 0.958). But a null moderation test on nine studies does not establish equivalence, and only one study in the corpus compares EMDR added to an addiction-focused psychotherapy against that psychotherapy alone. The difference between better than nothing and better than what I am already doing is therefore not settled. |
| Publication bias | Caution. A significant asymmetry on Egger’s test for craving, in a field where trials are small and often run by teams committed to the method, points toward an overestimation of the published effect. The negative Kendall’s test and the high fail-safe N temper the conclusion without cancelling it. For post-traumatic stress, the asymmetry is also significant, this time with a much lower fail-safe N. |
| Addiction severity unchanged | Inconclusive. Absence of demonstration, which is not a demonstration of absence: four effect sizes, three studies, moderate heterogeneity, hence low power. It remains that the only outcome describing consumption behavior itself is also the only one that does not move, and this asymmetry must weigh in the interpretation. |
| Long-term follow-up | No synthesis. In addiction medicine, a benefit without extended follow-up says nothing about what matters most. No quantitative synthesis of follow-up could be conducted, too few studies reporting it, and relapse and treatment adherence could not be analyzed for lack of data. The few observations cited diverge: one trial reports a maintained benefit at one month and less frequent relapse at six months; another observes the complete disappearance of the craving gain within one month. This is not silence, it is insufficient and discordant data, which authorizes no promise of durability. |
| Independence and transparency | Satisfactory. Public funding: Korea Institute of Oriental Medicine (KSN2313022) and the Korea Health Technology R&D Project through the Korea Health Industry Development Institute, Ministry of Health and Welfare, Republic of Korea (RS-2023-KH138802). The authors declare no commercial or financial relationship constituting a conflict of interest. Use of generative artificial intelligence for language editing is declared, which is transparent and does not bear on the analyses. The first author has also published an earlier meta-analysis favorable to EMDR in depression, cited in this work’s bibliography: allegiance bias, a constant whenever a team evaluates a method that forms its own research line, deserves to be kept in mind, though nothing declared here documents it. |
| Internal consistency of the count | Internal inconsistencies. The count was reconstructed from the publication and its supplementary material, and it shows some inconsistencies. The text attributes the 22 effect sizes on craving to 14 studies, while the corresponding figure shows only 9. One of the fourteen included studies, dated 2012, contributes to none of the five reported analyses, carries no reference number in the descriptive table, and its matching bibliographic entry is listed under a different first author. Finally, the flow-diagram counts do not add up: 704 records minus 621 duplicates gives 83, not the 76 reported, and 76 minus 47 exclusions gives 29, not the 28 retained for full-text reading. These discrepancies do not change the estimates; they weigh on the confidence placed in the care taken over the report. Conversely, the sum of participants study by study matches exactly the announced 327 and 322 participants. |
In practice
EMDR’s place in the treatment of post-traumatic stress disorder is well established and is not in question here. Its status in substance use disorders is of a different nature: it remains exploratory, and this work does not move it into another category.
In everyday practice, the relevant situation is narrow and identifiable: a patient followed for a dependence, whose history includes an active trauma, in whom reliving episodes, hypervigilance or avoidance visibly sustain substance use, and whose reference addiction care is already in place. This is, in fact, very precisely the profile of the few studies that carry the results on emotional symptoms. In this patient, referring toward EMDR work is defensible, provided what is expected of it is clearly named. One can hope for an improvement in the post-traumatic, depressive and anxious register, with a possible reduction in craving intensity. There is no basis for promising a reduction in the severity of the addictive disorder, and none for promising a benefit that holds over time.
The consequence fits in one sentence: EMDR substitutes for nothing. Not for pharmacological treatment of the dependence when indicated, not for addiction follow-up, not for the psychosocial interventions whose effect is better documented. Positioning it as an adjunct is consistent with the available data. Positioning it as an alternative is not, and this slippage is the main risk carried by a quick reading of this meta-analysis.
Level of evidence
PEB assessment: confidence is high regarding the conduct of the review itself. The question was registered on a public registry, the search was broad, risk of bias was assessed with tools suited to each design, the statistical apparatus is thorough, including its exploration of publication bias and its testing of the moderators most useful to the clinician. The authors acknowledge the weakness of their corpus and the insufficiency of follow-up data, and do not harden their conclusion. This is an honest meta-analysis of a mediocre literature, whose report nonetheless contains several counting inconsistencies.
Confidence is low, however, regarding the effect sizes themselves. A g of 0.55 drawn from a set in which seven of eleven randomized trials are at high risk of bias, with a significant publication asymmetry on this very outcome, comparators that do not overlap, and several dependent estimates drawn from the same sample, does not read as an established effect. It reads as an estimate whose confidence interval describes the precision of the pooling, not the real uncertainty about the size of the phenomenon. Three situations must be distinguished, and rarely are. On durability and relapse, there is no synthesis: a few trials report follow-up, their results diverge, and the number was too small to pool. On the comparison to an active treatment, the analysis exists and finds nothing, but it operates on whole studies and its power is too low to conclude equivalence. On addiction severity, the analysis exists, it is negative, and it rests on three studies. Absence of synthesis, an inconclusive analysis, and a negative result are not reported in the same terms.
The colleague test
What an experienced colleague would say if shown this study in two minutes, between two consultations.
“So EMDR lowers craving but not addiction severity, on trials most of which are at high risk of bias, against controls ranging from usual care to a sham procedure, and without a follow-up we could pool. That’s not nothing, but it doesn’t tell me whether it beats what I’m already doing. I’ll think of it for my patients with an active trauma, which I was doing anyway.”
Translation for practice: the work reinforces an existing clinical intuition and gives it a numerical backing, without licensing a change in care strategy or a move of EMDR from adjunct status to that of a treatment for dependence.
What you can do with this
- In a dependent patient with an active trauma, a referral to EMDR remains defensible alongside addiction care already in place, never in its place.
- Frame the goal with the patient in terms the data support: an expected reduction in reliving episodes, anxiety and depressive load, a possible easing of craving, no promise on consumption itself.
- Do not present this effect as durable: follow-up could not be synthesized, and the few available data point both ways, up to the complete disappearance of the craving gain within one month in one trial.
- If an addiction-focused cognitive behavioral therapy is already underway and working, this work provides no argument for replacing it with EMDR: only one study in the corpus tests EMDR added to such a therapy.
- If you want to track an effect, measure craving with a simple scale before and after, keeping in mind that a self-reported outcome in an unblindable treatment is the most permeable to the expectation of benefit.
- In case discussions or teaching, cite this work for what it is: a serious lead on weak data, not a validation of EMDR in addictions.
- The course of action is set out in the NICE decision tree for depression in adults.
Does this meta-analysis validate EMDR as a treatment for addictions?
No. It documents an effect on craving and on emotional dimensions, and no demonstrated difference on the severity of the addictive disorder. On a corpus of this quality, with a publication-bias signal on the outcome that carries the result, the defensible reading is that of a plausible adjunct, not that of a validated treatment.
What does a g of 0.55 mean for a patient?
It is conventionally a moderate effect. But the clinical translation of an effect size depends on the scale used and on the comparison situation, and here the comparators range from no treatment to cognitive behavioral therapy. The moderation test does not distinguish active from passive controls, but it operates on nine studies and is not enough to consider the question settled. Without knowing precisely what the effect was obtained against, converting it into an expected individual benefit makes no sense.
Why does craving decrease when addiction severity does not move?
Two explanations remain open. Either the effect genuinely acts on emotional load and urge without changing, at this point, consumption behavior. Or craving scales, which are subjective and collected without possible blinding, are more sensitive to the expectation of benefit than severity measures are. A more mundane reason adds to this: craving is documented by nine studies, severity by only three. The available data do not allow this to be settled.
Is the effect really better for alcohol than for tobacco?
A meta-regression reports a difference favoring alcohol, and the subgroup analysis points the same way, g = 0.75 [0.50, 1.00] against g = 0.38 [0.24, 0.53]. This comparison operates on studies, not on randomly allocated patients, and the authors themselves offer a common-sense explanation: the smokers included had no diagnosis of nicotine dependence and started from a lower craving level. It is a hypothesis to test, not a result to build an indication on.
How many sessions should be planned?
The included protocols range from one to twelve sessions, of 50 to 90 minutes, once or twice a week. The total number of sessions was tested as a continuous moderator of the craving effect, and the coefficient is null, beta = 0.003 [-0.085, 0.092], p = 0.940. The analysis exists, then, and shows no dose-effect relationship, but it rests on nine studies, which does not allow concluding that no such relationship exists.
Should substance use be stabilized before starting trauma work?
This work provides no solid answer to this question, which would require a direct comparison of care sequences. The authors note, moreover, that the treatment phase in which EMDR was delivered is rarely documented, which prevented any analysis of this factor. They note in their discussion that improvements in the post-traumatic register were observed even before the end of withdrawal, which argues for early integration, but this is the authors’ own reading, not a result. No adverse events and no return to substance use are reported in this meta-analysis, and an absence of reported data on tolerability is not proof of safety.
Annotated bibliography
Seok JW, Kim K, Kim JU. Therapeutic effects of eye movement desensitization and reprocessing for substance use disorders: a meta-analysis of addiction-related and emotional symptoms. Frontiers in Psychiatry, 17 September 2025; 16: article 1660046. DOI 10.3389/fpsyt.2025.1660046. PMID 41040945. PMCID PMC12484161. Funding: Korea Institute of Oriental Medicine (KSN2313022) and the Korea Health Technology R&D Project through the Korea Health Industry Development Institute, Ministry of Health and Welfare, Republic of Korea (RS-2023-KH138802). Conflicts of interest: the authors declare no commercial or financial relationship constituting a conflict of interest; declared use of generative artificial intelligence for language editing. Source study. Systematic review with random-effects meta-analysis, 14 studies, 327 patients treated and 322 controls, risk of bias assessed with RoB 2.0 and ROBINS-I. Its own contribution is not being the first pooled estimate of EMDR’s effect on craving, which already existed, but covering five symptomatic domains within a single work and basing effect sizes on the difference in change scores between groups rather than on end-of-treatment means. Limitations: low quality of primary studies, publication asymmetry on craving, multiple effect sizes drawn from the same sample, absence of a synthesis of extended follow-up.
Prior work. Two earlier meta-analyses cover the same field and are cited by the source study: Logsdon E, Cornelius-White JH, Kanamori Y, Journal of EMDR Practice and Research, 2023; 17: 21-32, presented by the authors as the first meta-analysis devoted to EMDR in substance use disorders; and Martínez-Fernández DE et al., Brain Sciences, 2024; 14: 1110, DOI 10.3390/brainsci14111110, which already reported a significant reduction in craving. Both references are reproduced as they appear in the source study’s bibliography and have not been independently verified.
Review protocol. PROSPERO registration, number CRD420251070837. Allows the pre-specified outcomes to be checked against those actually reported, a useful control given the risk of selective outcome reporting identified in several included trials. The registration date is not stated in the publication.
No other reference is cited in this analysis: contextual work will be added after direct verification of each source. An unverified reference does not appear in our pages.
What was consulted. Verification carried out on the published version of the source study (Frontiers in Psychiatry, 17 September 2025, volume 16, article 1660046, DOI 10.3389/fpsyt.2025.1660046, PMID 41040945) and on its two supplementary material files: the first contains figures S1 to S3, study-by-study risk-of-bias assessment and subgroup analyses by study design and by population; the second contains the completed PRISMA 2020 checklist. All numerical values in this analysis were taken from these documents. Two reservations: the right-hand columns of the descriptive study table, detailing each trial’s intervention protocol and measurement tools, were truncated in the copy consulted and could not be read; the authors’ affiliations did not appear in this copy. The two earlier meta-analyses mentioned in the bibliography are cited from the source study’s reference list and have not been independently verified.
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Verified on August 12, 2026 against the full text of the publication and its supplementary material where available. This analysis underwent an independent double reading. The English version was checked for conformity on September 18, 2026, against the figures of the French version and against the source. How we verify what we publish
This analysis is intended for healthcare professionals. It does not constitute a prescribing recommendation and does not replace individual clinical judgment.
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