Published on 19 September 2026
Group EMDR for forced migrants: what can an uncontrolled pre-post series actually show?
European Journal of Psychotraumatology · 2025;16(1):2583875 · Chauliac et al.
DOI 10.1080/20008066.2025.2583875
PMID 41236488
Scientific 62
Editorial 74
The essentials
A Lyon-based team reports on a group EMDR program run at a regional psychotrauma center for 71 adult forced migrants, asylum seekers, refugees and people without residency status, between April 1, 2021 and December 31, 2024. The work is a retrospective pre-post series, with no comparison group. What this design can establish, it establishes well: the program ran to completion in a population usually hard to retain in care, with mean session attendance of 80% and a dropout rate of 15%. What this design cannot establish, it does not establish: the drop in the proportion of patients meeting criteria for complex post-traumatic stress disorder, from 60.9% to 15.2% among the 46 patients with a paired ITQ measurement, and the significant reductions seen on all six primary outcomes, cannot be attributed to the intervention. Spontaneous change, regression to the mean, the effect of the group setting itself, concurrent medication and selection through missing data all remain competing explanations. The most telling figure is, in fact, the one the authors do not foreground: after the program, half of the patients assessed still met criteria for a post-traumatic disorder, simple or complex. The article reads as a feasibility demonstration, and that is the basis on which it deserves to be read.
Context
The question arises in daily practice as soon as a clinician sees an exiled patient with clear post-traumatic symptoms and, in practice, very limited access to structured individual psychotherapy. Waiting lists at specialized centers, the language barrier, administrative instability and unstable housing combine to make the care pathway fragile. The authors frame their work against this imbalance between the volume of need and the actual capacity of services: they note that 43.4 million people had been forcibly displaced across an international border by the end of 2023, a figure drawn from the UNHCR’s Global Trends 2023 report, and that around 11% of the population living in France resides there because of international migration, a figure drawn from INSEE in 2023.
Group format is presented as a response to this imbalance: it treats several patients per therapist slot, and it relies on written worksheets and on bilateral stimulation that patients administer to themselves, which reduces the share of verbal exchange. The authors began to quantify this efficiency argument, and the result is instructive: with two therapists for a 2.5-hour group of six participants on average, the time saved per patient compared with one-hour individual sessions is only 17%, and it shrinks further beyond eight participants, since a third therapist then becomes necessary. The authors themselves call this gain modest and shift the argument to different ground, that of motivation and of normalization of the disorder through the group. This last point is not tested in this work, which compares no modality to another.
The study at a glance
| Question (PICO) | |
|---|---|
| Population | |
| 71 adult forced migrants, asylum seekers, refugees and people without residency status, with a current post-traumatic stress disorder diagnosed clinically by a psychiatrist or psychologist at a prior individual interview. Age 18 to 62 years, mean 34.7 years, 53% women. Recruited at a French regional psychotrauma center, that of Auvergne-Rhône-Alpes at Edouard Herriot Hospital in Lyon, between April 1, 2021 and December 31, 2024. All patients who attended at least one group session and completed at least one self-report questionnaire were included. A third of participants came from two countries, the Democratic Republic of the Congo (18.3%) and Nigeria (15.5%). | |
| Intervention | |
| Group EMDR delivered according to E. Shapiro’s Group Traumatic Episode Protocol (GTEP), modified by the team to better address complex post-traumatic disorder: two sessions of psychoeducation and stabilization, three to four sessions focused on trauma reprocessing, one final integration session. Weekly sessions, with the last one held two to three weeks after the final reprocessing session, for a mean of 54 days between the first and last session. Groups of 4 to 10 participants, 6 on average, 2.5-hour sessions led by a therapist trained in EMDR assisted by one or two additional therapists. Bilateral stimulation is self-administered on a worksheet, in sets of 9, across four to five disturbance points per session. An interpreter was used when needed, otherwise machine translation. | |
| Comparator | |
| None. There is no control group, no waiting list, and no comparison with usual care. Each patient serves as their own reference point, measured before and after the program. | |
| Outcomes measured | |
| Six primary outcomes, all self-reported: post-traumatic stress disorder severity (PCL-5), diagnostic status for simple or complex post-traumatic disorder (ITQ), depression (PHQ-9), psychological distress (K6), quality of life (WHOQOL-BREF), subjective disturbance level (SUD). Measured at the initial interview or the start of the first session, then at the end of the last session, except for SUD, whose baseline measure is taken at the second session. Validated French or English versions, according to participant preference. Paired Wilcoxon test, Hodges-Lehmann estimator for the difference in medians, paired rank-biserial correlation for effect size, Bonferroni correction across six outcomes, giving a significance threshold of 0.0083 and 99% confidence intervals. | |
| Design | |
| Retrospective pilot study, uncontrolled pre-post series, single-center, which corresponds to CEBM level 4 in our assessment. 71 patients included, 48 with paired before-and-after measures for at least one instrument. Analyzed sample sizes vary by instrument: 47 for PHQ-9, 46 for ITQ, 42 for SUD, 34 for PCL-5, 32 for WHOQOL-BREF, 19 for K6. |
Quality control
| Point checked | Judgment |
|---|---|
| Comparison group | Absent |
| FindingThis is the work’s structuring limitation, and the authors state it themselves. Any variation measured between the start and end of the program mixes any effect of the intervention with the change that would have occurred without it. | |
| Data collection | Retrospective |
| FindingData were extracted after the fact from a center’s clinical activity. The analysis plan was therefore not fixed before the results were seen, and the authors acknowledge that this retrospective design prevented any systematic control for confounders, starting with concurrent medication and life events tied to residency procedures. | |
| Measurement instruments | Validated scales |
| FindingPCL-5, ITQ, PHQ-9, K6 and WHOQOL-BREF are recognized tools, used in their validated French or English versions according to participant preference. The question of equivalence remains open for patients fluent in neither language, for whom an interpreter, or even machine translation, was used. | |
| Multiplicity correction | Bonferroni applied |
| FindingThe threshold was lowered to 0.0083 across six primary outcomes, with 99% confidence intervals and an additional correction of effect sizes for within-subject correlation. An unusual precaution for a pilot study. It protects against false positives arising from the number of scales; it corrects nothing about the absence of a control group. | |
| Missing data | Quantified, not imputed |
| FindingThe supplementary material gives the count instrument by instrument. No imputation was performed; the analysis uses available pairs only, which brings the sample down to 19 patients for K6 and 34 for PCL-5, out of the 71 included. The authors compared patients whose measures were used with those whose measures were not, finding no significant difference on PCL-5, PHQ-9, ITQ or SUD, before or after. This sits at odds with the intention-to-treat label the statistics section claims. | |
| Follow-up after the program | Not reported |
| FindingNo follow-up measure is reported, which the authors explain by the mobility of this population, often relocated after a decision on their status. Whether the observed changes persisted beyond the end of the program is therefore an open question, not one the study answered negatively. | |
| Funding and conflicts of interest | Partial disclosure |
| FindingThe authors declare no potential conflict of interest. The published document, however, carries no funding statement. The work comes from a French public academic hospital center, with INSERM, CNRS and Université Claude Bernard Lyon 1 affiliations. | |
Results
| Result | Reported value |
|---|---|
| Session attendance | 80% on average, median 85.7%, standard deviation 25.2. |
| ReadingA feasibility indicator, interpretable as reported. This is the mean proportion of sessions attended per patient, calculated across the 71 included patients. The high standard deviation shows the mean covers widely uneven trajectories. | |
| Dropout during the program | 15% of the 71 participants. |
| ReadingDefined as not returning after a missed session. A low figure given this population’s constraints. It also shapes how the symptom measures should be read: patients who left the program do not contribute to the final measurements. | |
| Diagnostic status (ITQ) | Complex disorder 60.9% before (28 of 46), 15.2% after (7 of 46). |
| ReadingA large-magnitude change, but measured with no external reference and only in the 46 patients with a paired ITQ measurement. The full table tempers this impression: the proportion meeting criteria for simple post-traumatic disorder rises from 28.3% to 34.8%, and the proportion meeting no criteria rises from 10.9% to 50.0%. In other words, part of the drop in complex disorder is a reclassification toward the simple form, and half of the patients assessed still met criteria for a post-traumatic disorder after the program, against 89.1% before. | |
| Post-traumatic stress severity (PCL-5) | Mean 49.68 before, 37.85 after, n = 34, p = 0.0001, rank-biserial correlation 0.77 (99% CI 0.46 to 0.91). |
| ReadingMedians of 52 to 37. The drop of nearly 12 points exceeds the threshold usually used for a clinically meaningful change on this instrument, which the authors note, drawing on the scale’s validation work. This reading holds within a given patient; it says nothing about the share attributable to the program. | |
| Depression (PHQ-9) | Mean 16.55 before, 11.70 after, n = 47, p less than 0.0001, rank-biserial correlation 0.72 (99% CI 0.43 to 0.88). |
| ReadingMedians of 17 to 12, that is, a shift from moderately severe to mild-to-moderate depression on the usual PHQ-9 reading scale. The concurrent reduction in depressive symptoms is consistent with the change in post-traumatic disorder; it does not independently confirm it. | |
| Subjective disturbance (SUD) | Median 9 before, 6 after, n = 42, p less than 0.0001, rank-biserial correlation 0.96 (99% CI 0.91 to 0.99). |
| ReadingThe largest effect size in the table, and also the most fragile measure. The baseline value is not collected before the program but at the second session, that is, after psychoeducation and part of stabilization, and it is a discomfort rating requested by the therapist within the EMDR protocol itself. | |
| Psychological distress (K6) | Mean 14.95 before, 9.63 after, n = 19, p = 0.0054, rank-biserial correlation 0.73 (99% CI 0.25 to 0.92). |
| ReadingA significant result at the corrected threshold, but resting on only 19 pairs, a quarter of the included cohort. The 99% confidence interval on the effect size, 0.25 to 0.92, reflects this imprecision. | |
| Quality of life (WHOQOL-BREF) | Mean 11.59 before, 12.93 after, n = 32, p = 0.0022, rank-biserial correlation -0.68 (99% CI -0.88 to -0.25). |
| ReadingThe one outcome the authors single out in their summary sentence, excluding WHOQOL from their mention of large effect sizes, even though their own table marks it as reaching the corrected threshold. The absolute gain is 1.3 points; the clinical significance of such a change is not discussed. | |
| Diagnostic worsening | Three participants moved from simple to complex disorder. |
| ReadingThese three patients saw their PCL-5 score rise, and their attendance was incomplete. The authors propose that partial exposure to desensitization sessions may have reactivated traumatic memories without sufficient stabilization or reprocessing. A plausible hypothesis, not testable on three cases, but one worth knowing for any team deploying this format. | |
Critical appraisal
| Domain | Judgment |
|---|---|
| Causal attribution | Impossible by design |
| FindingFive competing explanations remain open for the observed changes: spontaneous symptom change, regression to the mean in patients included at a moment of peak severity, the effect of the group setting itself and of regular contact with a team, concurrent medication received by some participants during the intervention period, and the departure from the program of the patients doing worst. None is ruled out by the design, and the authors explicitly acknowledge that the retrospective design prevented them from controlling for the last two. | |
| Patient selection | Single specialized center |
| FindingPatients were referred to a regional psychotrauma center and selected for a group format, which presupposes a minimum of stability and engagement. The population analyzed is therefore not equivalent to the full range of exiled people seen in frontline care. The authors instead claim good representativeness, on the grounds that they included every eligible patient referred to the center: the argument holds for the center’s active caseload, not beyond it. | |
| Outcome measurement | Self-report questionnaires |
| FindingAll six outcomes rest on patient self-report, in a setting where the patient knows the expected direction of change and has formed a relationship with the team. This expectation bias works in the direction of improvement, and it is counterbalanced by no independent assessment. The authors acknowledge this and note that no clinician-administered instrument, such as the CAPS-5, was used. | |
| Missing data and loss to follow-up | Compared, no significant difference |
| FindingThe best-handled point in the work. The supplementary material compares patients whose measures were used with those whose measures were not, on PCL-5, PHQ-9, ITQ and SUD, before and after, finding no significant difference. The caveat is statistical power: with sample sizes of this order, the absence of a significant difference does not establish the absence of a difference, and the comparison says nothing about the profile of the 15% of patients who left the program. | |
| Statistical analysis | Multiplicity corrected |
| FindingNonparametric tests suited to modest sample sizes, Bonferroni correction across six outcomes, 99% intervals, effect-size correction for within-subject correlation. This care is unusual for a pilot study. One caveat, though: the analysis is presented as intention-to-treat, while it in fact covers only complete pairs, 19 to 47 patients depending on the instrument, out of the 71 included. The label and the method do not match. | |
| Authors’ caution | Title and abstract more assertive |
| FindingThe discussion and the limitations section are honest: no causal inference, no control group, no follow-up, a call for randomized trials. The title, however, announces the protocol’s effectiveness, and the abstract concludes that the results suggest it is both effective and applicable, then that the study provides evidence supporting its use. The body of the text is measured; the packaging is less so, and it is the packaging that circulates. | |
| Transferability | Direct |
| FindingThe work describes a real program run in a French center, with recruitment, language and precarity constraints comparable to those found in comparable services elsewhere. Findings of this kind travel across settings that share these constraints, which is what gives this series its practical value, independent of the question of efficacy. | |
Level of evidence
Confidence is high on one point, and one only: a group EMDR program could be run to completion, in a French center, with 71 exiled people, with mean attendance of 80% and dropout of 15%. This organizational finding depends on neither a comparator nor a causal inference, and it stands as a result in its own right. Confidence is low on everything touching the program’s effect. CEBM level 4 corresponds exactly to what an uncontrolled pre-post series produces: a description, not an effect estimate. The large effect sizes are not therapeutic effect sizes; they are amplitudes of within-patient change on self-report questionnaires, in a setting where several nonspecific mechanisms push in the same direction. The work’s statistical rigor, multiplicity correction included, does not raise this level of evidence by one notch: it makes the descriptive result more reliable, not more causal. One further data point the authors cite themselves should be added: the Antuña-Camblor and Hernández meta-analysis, restricted to randomized trials, finds only weak and non-significant effects of EMDR on post-traumatic symptoms in adult refugees. A positive pre-post series carries no weight against this finding; if anything, it underscores the open question.
The colleague test
What an experienced colleague would say if shown this study in two minutes, between two consultations.
What interests me here is not the drop in the complex-disorder figure, because without a control group I don’t know what it’s worth, and because looking at the table I can see that part of it is patients simply shifting to the simple form. Half of them still meet criteria at the end, that puts things in perspective. What interests me is that 80% of sessions were attended and only 15% dropped out, in a population I usually struggle to keep in care. That tells me a group format that doesn’t depend much on language holds up under real conditions, and that’s already an argument for organizing a service. I also noticed the therapist time saved was only 17%, so the budget argument, forget it. For efficacy, I’m waiting for a controlled trial, and I wouldn’t tell my residents anything different.
Translation for practice: this publication supports an organizational decision, not an individual therapeutic one. It gives arguments for offering this format in a service that has a trained therapist; it gives none for telling a patient that the group will reduce their symptoms.
What you can do with this
- Keep the two indicators that hold up: mean attendance of 80% and dropout of 15% among exiled people in precarious circumstances. These are figures to set against the assumption that this population cannot be retained in a structured program.
- Separate, in a team meeting or in front of an oversight body, the feasibility argument, which is documented here, from the efficacy argument, which is not. Conflating the two exposes you to contradiction at the first methodological objection.
- Do not present the group format as a resource saving. The therapist time gain the authors measured is 17%, and it shrinks once the group exceeds eight participants. The argument to make is one of access and of the collective setting, not of cost.
- Know how to answer a patient who has heard of this format: it exists, it is offered in specialized centers, it requires a trained therapist, and its own specific benefit is not yet established by a comparative study.
- Consider how psychotrauma care for displaced people is organized in your own setting. In France, as of September 2026, exiled patients with psychotrauma are served through outreach structures not specific to this population, mobile psychiatry-and-precarity teams and health-access clinics, coordinated regionally through psychotrauma centers under the national trauma resource network created in 2019. This is one national example of what a suitable outreach structure can look like; comparable arrangements exist in other countries under different names. Legal oversight of who may practice EMDR, and under what professional title, also varies by jurisdiction: in France it covers only the protected title of psychotherapist, with EMDR practice itself governed only by a voluntary EMDR Europe practitioner accreditation rather than a state certification. Check the regulatory framework and referral pathways in your own jurisdiction before assuming this model transfers directly.
- Watch what the study does not track: what happens to patients after the program ends, and to those who leave it early. These are the two points on which any team deploying this format should organize its own data collection. Add to that watching for worsening in patients with incomplete attendance, reported here in three participants.
- Do not extend these results to individual care, or to other traumatized populations. The work concerns a group format in a specific migration context.
Frequently asked questions
Does this study show that group EMDR works for forced migrants?
No. It shows that a group EMDR program could be delivered to 71 exiled people with a low dropout rate. The absence of a comparison group makes it impossible to attribute the measured symptom changes to the program, and the authors themselves write that no causal inference is possible. The question of efficacy remains open, and they call for controlled trials.
The drop in complex PTSD from 60.9% to 15.2% still looks impressive.
The magnitude is real, the interpretation is not, and reading it in isolation is misleading. These percentages cover 46 patients, that is, 28 then 7 people. Over the same period, the proportion meeting criteria for simple post-traumatic disorder rises from 28.3% to 34.8%: some patients did not recover, they moved category. Overall, half of the patients assessed still met criteria for a post-traumatic disorder after the program. Add to this regression to the mean, the natural course of the disorder, the effect of the group setting, medication received by some participants, and the fact that patients who left the program are absent from the final measurement. None of these mechanisms is ruled out here.
Is the group format really less dependent on language?
This is the authors’ working hypothesis, based on the use of written worksheets and self-administered bilateral stimulation. It is not tested: questionnaires were administered in French or English according to participant preference, with an interpreter or machine translation when needed, and the study reports no result stratified by language. It also does not compare this format with individual care using an interpreter. The argument remains plausible and untested.
Does the group format actually save time?
Not much. The authors did the calculation: two therapists for a 2.5-hour group of six participants on average represent a 17% time gain compared with one-hour individual sessions, and this gain shrinks further once a third therapist becomes necessary beyond eight participants. They themselves call this result modest and shift the group’s rationale toward motivation and normalization of the disorder, which is not measured here.
Are all the announced outcomes reported?
Yes, the six primary outcomes appear in the results table with their sample sizes, medians, means, confidence intervals, p-values and effect sizes. What is missing is follow-up: no measure is reported after the end of the program, and this gap should be read as missing information, not as a negative result. It is also worth noting the small sample sizes for some outcomes, 19 patients for psychological distress, 32 for quality of life.
Is this the first French study on this format?
That is not what the authors claim. They present their work as the first formal evaluation of this particular adaptation of the GTEP protocol, a narrower and more defensible claim. The same team had already published a preliminary field study on GTEP delivered to migrants in 2023, on a smaller sample. What is certain, and sufficient to justify the attention this work deserves, is the scarcity of French-language data on how psychotrauma care for exiled people is organized.
Annotated bibliography
Source study. Chauliac N, Vignaud P, Butet C, Gautheron M, Salome G, Salles L, Galia P, Prieto N. Applicability and effectiveness of group EMDR therapy for forced migrants. European Journal of Psychotraumatology 2025;16(1):2583875. DOI 10.1080/20008066.2025.2583875. PMID 41236488. Open-access article, received August 5, 2025, revised October 28, 2025, accepted October 29, 2025, published online November 14, 2025. Conflicts of interest: the authors declare that no potential conflict of interest was reported. Funding: the published document carries no funding statement. The document provides a description of a real-world program: sample sizes, protocol course, attendance, dropout, and pre-post changes across six primary outcomes, with supplementary material detailing missing data and comparing analyzed patients with those not analyzed. Its limitation is built into its design, a retrospective series with no comparator, which the authors acknowledge explicitly in their discussion, less clearly in their title and abstract.
Prior work by the same team. Vignaud P, Chauliac N, Contamin E, Richer S, Vuillermoz C, Brunelin J, Prieto N. Relevance and feasibility of group traumatic episode protocol delivered to migrants: a pilot field study. International Journal of Environmental Research and Public Health 2023;20(7). DOI 10.3390/ijerph20075419. PMID 37048033. Cited by the authors as an earlier stage of the same program, on a smaller sample. It was not consulted at source for this analysis, and nothing beyond its existence is drawn from it here.
Methodological counterpoint, cited by the authors themselves. Antuña-Camblor C, Hernández VT. EMDR interventions in refugees and asylum seekers: a systematic review and meta-analysis. Clinical Psychology and Psychotherapy 2025;32(1):e70039. DOI 10.1002/cpp.70039. PMID 39876798. Restricted to randomized trials, this meta-analysis finds, according to the source study’s discussion, only weak and statistically non-significant effects of EMDR on post-traumatic symptoms in adult refugees. The meta-analysis by Macgowan MJ, Naseh M, Rafieifar M, Research on Social Work Practice 2022;32(8):863-877, DOI 10.1177/10497315221082223, is more favorable but finds, again according to the authors, larger effects for individual EMDR than for group EMDR. Both references are reported as they appear in the source publication; they were not consulted at source for this analysis.
Reference framework invoked. The protocol adaptation is justified by reference to the International Society for Traumatic Stress Studies’ phase-based psychotherapy guidelines, cited through Cloitre M et al., Journal of Traumatic Stress 2011;24(6):615-627 (PMID 22147449), Forbes D, Bisson JI, Monson CM, Berliner L, Effective Treatments for PTSD, third edition, Guilford Publications, 2020, and Mahoney A, Karatzias T, Hutton P, Journal of Affective Disorders 2019;243:305-321 (PMID 30261446). These three references appear in the source publication’s bibliography and were not consulted at source for this analysis.
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Verified on September 1, 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 19, 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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