Published online Oct 26, 2026. doi: 10.4252/wjsc.125423
Revised: August 4, 2026
Accepted: October 8, 2026
Published online: October 26, 2026
Processing time: 112 Days and 3.9 Hours
Spinal cord injury (SCI) often causes persistent neurological deficits, and effective treatment options remain limited. Human umbilical cord blood-derived mesen
To systematically evaluate the efficacy and safety of native, unmodified hUCB-MSC transplantation in SCI models, and explore dose-response relationships.
We systematically searched PubMed, EMBASE, and Web of Science from incep
Six studies involving 273 animals were included; 132 animals contributed to the functional-recovery meta-analysis. hUCB-MSC treatment was associated with significantly greater functional recovery [SMD = 2.35, 95% confidence interval (CI): 0.89-3.80, P = 0.009], with substantial heterogeneity (I2 = 81.8%). The certainty of the evidence was rated as low. Subacute administration (> 24 hours) was associated with significantly greater functional recovery (P = 0.033), whereas acute administration did not. No statistically significant increase in mortality risk was detected (relative risk = 1.20, 95%CI: 0.60-2.40). The low-dose subgroup (≤ 1 × 106 cells) showed a statistically significant effect (SMD = 1.40, 95%CI: 1.09-1.70, P < 0.001, I2 = 0%, k = 4), but this finding is hypothesis-generating and requires validation in larger studies.
Preclinical evidence suggests that native hUCB-MSC transplantation may improve functional recovery after SCI, although the overall certainty of the evidence is low. The apparent consistency of effects at low doses is a hypothesis-generating observation requiring further validation.
Core Tip: This systematic review and meta-analysis of six preclinical studies demonstrates that human umbilical cord blood-derived mesenchymal stem cell transplantation significantly improves functional recovery in experimental spinal cord injury, with a large effect size (standardized mean difference = 2.35). The certainty of evidence is low due to substantial heterogeneity and methodological limitations. A hypothesis-generating observation suggests that low doses (≤ 1 × 106 cells) may yield more consistent effects than higher doses, questioning the assumption of a simple linear dose-efficacy relationship. These findings provide an initial quantitative reference for future translational research.
- Citation: Liao LQ, Liang RX, Ren ZX, Wang YY, Wei W, Li YS. Human umbilical cord blood-derived mesenchymal stem cell therapy in experimental spinal cord injury: A systematic review and meta-analysis. World J Stem Cells 2026; 18(10): 125423
- URL: https://www.wjgnet.com/1948-0210/full/v18/i10/125423.htm
- DOI: https://dx.doi.org/10.4252/wjsc.125423
Spinal cord injury (SCI) is a devastating central nervous system (CNS) injury that often causes persistent impairments in motor, sensory, and autonomic function[1,2]. SCI represents a major global health burden, affecting an estimated 20 million individuals worldwide, with approximately 900000 new cases annually[3]. In addition to the primary neuro
Stem cell therapy has emerged as a promising approach for treating a range of diseases[5]. In the context of SCI, transplantation of mesenchymal stem cells (MSCs) may exert therapeutic effects through the secretion of neurotrophic and neuroprotective factors and the establishment of a favorable microenvironment for the neuronal differentiation of endogenous neural stem/progenitor cells[1-4,6]. Additionally, MSCs exhibit strong anti-inflammatory and immunomodulatory properties, promote vascular repair and angiogenesis at the injury site[7,8], and secrete bioactive molecules that facilitate axonal regeneration, relay formation, and remyelination[6]. Thus, MSC transplantation is a promising therapeutic strategy for SCI[6], and MSCs have therefore become one of the most extensively studied cell types for SCI treatment[9].
Currently, MSCs are typically derived from tissues such as bone marrow, umbilical cord, and adipose tissue[6,10,11]. Advances in understanding the mechanisms of stem cell-based therapies for SCI in animal models have provided critical insights into their neuroregenerative and neuroprotective potential[12]. Evidence regarding their therapeutic potential spans preclinical studies, clinical trials, and comparisons involving autologous MSCs, allogeneic MSCs, and various control groups[11,13-17]. Most of the available evidence, however, comes from animal studies, with human clinical data remaining limited[16]. Available findings suggest that MSCs exert neuroregenerative and neuroprotective effects after SCI, although their definitive clinical and functional significance, as well as long-term safety, remain to be established[11,14]. These findings also indicate that MSCs derived from different sources, such as bone marrow, umbilical cord, and adipose tissue, exhibit distinct characteristics and have specific advantages and limitations for SCI therapy[14,16].
Given this context, there is a clear rationale for investigating the therapeutic potential of MSCs from alternative sources. Human umbilical cord blood-derived MSCs (hUCB-MSCs) have multilineage differentiation potential, immunomodulatory properties, high expansion capacity, and superior chondrogenic activity[18]. They offer additional practical advantages, including noninvasive collection and easier accessibility[18]. More importantly, hUCB-MSCs are considered a more primitive cell population than MSCs from bone marrow or adipose tissue, a characteristic associated with lower immunogenicity and tolerance for a greater degree of HLA mismatch in transplantation settings[18,19]. Therefore, hUCB-MSCs may offer distinct therapeutic advantages for SCI.
However, the field of SCI regenerative therapy is rapidly evolving beyond the transplantation of unmodified, native cells. Recent research has increasingly focused on improving therapeutic outcomes through strategies such as using cell-free derivatives, including MSC-derived extracellular vesicles (MSC-EVs)[20,21], combining MSCs with biomaterial scaffolds[22,23], and preconditioning MSCs to enhance their reparative functions[24]. These approaches seek to address key translational challenges, including poor cell survival, uncontrolled differentiation, and inadequate integration at the injury site. In this evolving context, a rigorous quantitative synthesis of the foundational evidence for native hUCB-MSCs is essential. Such a synthesis would provide a more precise estimate of the efficacy and safety profile of hUCB-MSC therapy, help identify the most effective treatment parameters, highlight limitations in the current evidence, and ultimately inform the design of future high-quality preclinical studies and potential clinical trials. To bridge the translational gap, the use of clinically relevant large-animal models that closely reproduce human contusion/compression injuries is essential for predicting therapeutic outcomes[25-27]. Validation in such models may improve the relevance of preclinical findings to human clinical trials. Nevertheless, as the field has rapidly shifted toward complex engineered strategies, such as MSC-EVs, biomaterial-scaffold combinations, and preconditioned cells, the precise efficacy baseline of native hUCB-MSCs has remained undefined. This study provides an initial quantitative reference for native hUCB-MSCs that may serve as a baseline against which future advanced therapies can be evaluated. By defining this baseline, this review aims to support the rational translation of next-generation engineered therapies from the laboratory to clinical application.
This systematic review (SR) followed a prespecified protocol in which all methodological elements, including the search strategy, eligibility criteria, data extraction items, and statistical analysis plan, were developed and finalized before the literature searches were initiated on September 12, 2025. The protocol was submitted for PROSPERO registration in September 2025, and the registration number (CRD420251157232) was assigned in November 2025. No protocol elements were altered after the preliminary results became available. All data extraction and statistical analyses were performed in accordance with the registered protocol. The review was conducted and reported in accordance with the PRISMA 2009 statement[28,29]. The full protocol is available from the PROSPERO registry (https://www.crd.york.ac.uk/prospero/display_record.php?RecordID=1157232). No amendments were made to the registered protocol.
We searched the following databases: PubMed, Web of Science, and EMBASE. No restrictions were placed on publication date; eligible publications were limited to those in English or Chinese, as pre-specified in the registered protocol. Our comprehensive search of PubMed, EMBASE, and Web of Science from inception to September 12, 2025 (Supplementary material) retrieved no eligible studies published after 2018 that met our strict inclusion criteria for native (unmodified) hUCB-MSC transplantation. Although we identified numerous studies published from 2018 to 2025, all of them investigated engineered cellular products (e.g., MSC-EVs, preconditioned MSCs, or biomaterial combinations) rather than transplantation of native hUCB-MSCs alone. Consequently, our synthesis encompasses the complete evidence base for native hUCB-MSC monotherapy in experimental SCI up to 2018. This finding reflects a marked shift in the field’s research focus since 2018 toward engineered cellular products (e.g., MSC-EVs, preconditioned MSCs, and biomaterial-scaffold combinations) rather than native cell transplantation[20-24]. The complete search strategies, including the detailed search strings for all databases, are provided in the Supplementary material.
An updated literature search (PubMed, EMBASE, and Web of Science) was performed on August 31, 2026, before final submission. No additional eligible studies of native, unmodified hUCB-MSC monotherapy in experimental SCI were identified, indicating that the analysis encompasses the complete preclinical evidence base for this specific intervention up to the date of submission.
The eligibility criteria were defined according to the PICOS (Population, Intervention, Comparison, Outcome, Study design) framework. P (Population): Laboratory animals (any species, sex, age, or strain) with an experimentally induced traumatic SCI. I (Intervention): Transplantation of hUCB-MSCs, characterized by standard immunophenotypic markers, without genetic or functional modification. C (Comparator): Any control group without hUCB-MSC therapy (e.g., vehicle, sham, model-only, or active non-cell therapy). O (Outcomes): Quantitative data on: (1) Functional recovery [e.g., Basso, Beattie, and Bresnahan (BBB) locomotor scale, Tarlov scores]; (2) Histopathology (e.g., lesion volume); and (3) Safety (e.g., mortality, adverse events). S (Study design): Controlled animal studies, both randomized and non-randomized.
Inclusion criteria: Studies were included if they: (1) Were controlled animal studies (randomized or non-randomized); (2) Involved laboratory animals with experimentally induced SCI; and (3) Provided sufficient characterization data for hUCB-MSCs. Given the limited reporting quality of preclinical studies published before 2018, we applied an adapted minimum standard derived from the International Society for Cellular Therapy minimal criteria[30], as pre-specified in the registered protocol. Specifically, eligible studies had to report results for at least one positive MSC-associated marker (e.g., CD73, CD90, CD105) and at least one negative hematopoietic marker (e.g., CD34, CD45, HLA-DR) in the main text or Supplementary material. This pragmatic adaptation was necessary because older preclinical studies frequently did not report the full International Society for Cellular Therapy panel. The fourth criterion required at least one quantitative outcome of efficacy or safety as defined above.
Exclusion criteria: Studies were excluded if they: (1) Were not original research (e.g., reviews, editorials) or were only available as conference abstracts with insufficient data; (2) Used non-MSC fractions, MSCs from other sources, or genetically/functionally modified cells; (3) Involved combination therapies for which data on hUCB-MSCs alone could not be isolated, including studies employing biomaterial scaffolds, hydrogels, or other carrier materials in conjunction with hUCB-MSC transplantation; (4) Lacked a relevant control group; (5) Did not meet the minimum cell characterization criteria defined in the inclusion criteria; or (6) The full text could not be obtained despite exhaustive efforts.
Study selection proceeded in three sequential phases to ensure comprehensiveness.
Phase 1: Database search and screening. Records from all databases were merged, and duplicates were removed using the Rayyan web application[31]. One reviewer (Li YS) performed an initial screening of all unique records based on titles and the abstracts available in Rayyan, applying the predefined eligibility criteria. For records for which the abstract was unavailable in Rayyan, the original publication databases (EMBASE, Web of Science, or PubMed/MEDLINE) were consulted to retrieve and assess the abstract. Records were categorized as “include”, “exclude”, or “maybe”. Full-text articles were sought for all records categorized as “include” or “maybe”. Retrieved full texts were then assessed by two independent reviewers (Liao LQ and Liang RX) for eligibility. Disagreements between reviewers were resolved through discussion to reach consensus or, if necessary, by consultation with the third reviewer (Li YS).
Phase 2: Supplementary citation search. To minimize the risk of missing eligible studies, a supplementary search was performed after the initial title/abstract screening by reviewing the studies included in a broader, related SR on umbilical cord blood-based therapies for neurological disorders identified via PubMed.
Phase 3: Integration and deduplication. The lists of studies deemed eligible from phase 1 and phase 2 were combined. Any duplicate studies (i.e., studies identified by both pathways) were removed to produce the final set of included studies.
A standardized, pre-piloted data extraction form was developed in accordance with the study protocol and was used for all included studies. Data extraction covered four main categories: (1) Study characteristics included first author, publication year, journal, country, funding statement, study design, control group type, randomization method, blinding of outcome assessment, ethical approval, conflict of interest statement, and reporting of exclusion criteria and sample size justification; (2) Animal-model details included species, strain, sex, age at injury (weeks), housing conditions, anesthesia/analgesia protocol, total number of animals, injury model, injury level, and injury severity parameters; (3) Intervention details included number of UCB donors, consistency of cell source, cell passage, cell viability (%), cell dose per injection, total cell dose per animal, route of administration, time to first dose (hours post-injury), timing category (acute/subacute/chronic), number of doses, dosing schedule description, use of immunosuppression, and immunosuppression regimen; and (4) Outcome data included functional outcome scale used, scale direction (higher/Lower better), functional score mean, standard deviation, and sample size (n) for treatment and control groups at the latest reported time point; lesion volume mean, standard deviation, and n for treatment and control groups; mortality events and total animals per group; and occurrence of any treatment-related adverse events.
Two reviewers (Liao LQ and Liang RX) independently extracted data using this form. The extracted data were cross-checked. Discrepancies were resolved by consensus or by consulting a third reviewer (Li YS). The extraction process followed a detailed codebook (provided as Supplementary material) to ensure consistency and reproducibility. For outcomes presented only graphically, numerical data were extracted using Engauge Digitizer (v11.3) and Fiji/ImageJ (v1.54p) software[32,33]. For studies with multiple experimental arms, only the hUCB-MSC treatment group and its directly comparable control group (e.g., vehicle-treated or untreated) were extracted for the meta-analysis of functional recovery.
For studies reporting multiple intervention subgroups (e.g., different doses or administration routes) without an overall reported effect, data were pooled to derive a single study-level effect size. The combined mean was calculated as the weighted average of subgroup means, and the combined variance accounted for both within-group variance and between-group variance, following the formula recommended by the Cochrane Handbook for combining groups.
Two reviewers (Liao LQ and Liang RX) independently assessed the methodological quality and risk of bias of each included study using three complementary tools.
Risk-of-bias assessment: The internal validity of each study was assessed using the SR Centre for Laboratory Animal Experimentation’s (SYRCLE’s) risk of bias tool for animal studies[34-36]. This tool evaluates ten domains that cover sequence generation, baseline characteristics, allocation concealment, random housing, blinding of caregivers and investigators, random outcome assessment, blinding of outcome assessors, incomplete outcome data, selective outcome reporting, and other sources of bias. Each domain was judged as “low”, “high”, or “unclear” risk.
Methodological quality assessment: To further evaluate study design quality, we employed the Collaborative Approach to Meta-Analysis and Review of Animal Data from Experimental Studies (CAMARADES) checklist[32,37]. This checklist assesses peer-reviewed publication, statement of potential conflict of interest, statement of control of temperature, randomized allocation, blinded induction of therapy, blinded assessment of outcome, sample size calculation, animal model authentication, exclusion of comorbid animals, and compliance with animal-research policies[35,38]. A score out of the maximum applicable items was calculated for each study.
Reporting quality assessment: Adherence to reporting standards was assessed against the ARRIVE 2.0 guidelines[33,39,40]. We evaluated the reporting of key items essential for interpretation and reproducibility, such as sample size justification, ethical statement, and experimental procedures[32]. Discrepancies in any assessment were resolved by consensus or consultation with a third reviewer. Results are presented in summary tables and traffic light plots[35,38].
The primary outcome of this review was functional recovery after experimental SCI. To ensure consistency across studies that used different scales with potentially opposite interpretations (e.g., BBB locomotor scale, where higher scores indicate better function, vs the Reuter score, where lower scores indicate better function), all outcomes were harmonized to a uniform “higher-is-better” convention prior to meta-analysis[35,38]. Specifically, for the study that employed the Reuter score[19], the data were transformed by multiplying the mean values by -1, thereby inverting the scale direction so that higher values correspond to improved recovery, consistent with the BBB and other scales. The secondary outcome was safety, assessed by extracting data on mortality (events and total animals in treatment and control groups) and reported adverse events across all included studies[35,38].
All analyses were performed using R (v4.6.0) with the “metafor” package. Generative AI tools (DeepSeek, Kimi, and Zhipu Qingyan) were used to assist in drafting the R scripts, and the authors reviewed and verified all outputs, as detailed in the Acknowledgments. Continuous outcomes (functional scores and lesion volumes) were pooled using standardized mean differences (SMDs) with 95% confidence intervals (CIs) to accommodate different measurement scales. A random-effects model was used because we anticipated methodological and clinical heterogeneity among animal studies.
Because preclinical SRs in this field typically include a limited number of eligible studies (often fewer than 10), we employed the DerSimonian-Laird (DL) estimator for between-study variance (τ2), as pre-specified in the registered protocol, with the Hartung-Knapp-Sidik-Jonkman (HKSJ) adjustment as the primary analytic approach. While restricted maximum likelihood (REML) is generally preferred for larger meta-analyses, we selected the DL estimator combined with HKSJ adjustment because: (1) Simulation studies demonstrate superior type I error control with few studies; (2) HKSJ produces more conservative CIs appropriate for anticipated heterogeneity in animal studies; and (3) This approach is recommended for meta-analyses with limited numbers of studies where exact distributional assumptions may not hold[41,42]. Compared with conventional normal-approximation methods, HKSJ can improve CI coverage in meta-analyses with few studies[41].
The point estimate (SMD) was calculated using the inverse-variance weighted average under the random-effects model, with the HKSJ adjustment applied to the standard error for CI and significance test calculations. Had 10 or more studies been available, we would have considered alternative between-study variance estimators and CI methods that are better suited for larger meta-analyses (e.g., REML with Q-profile or bootstrapped CIs), in accordance with established methodological guidance[42].
Heterogeneity was assessed using the I2 statistic and the between-study variance (τ2). Prediction intervals (PIs) were calculated to estimate the potential range of true effects in similar future experiments. Heterogeneity was investigated via subgroup analysis and meta-regression. Sensitivity analyses comprised: (1) Sequentially excluding each study (leave-one-out analysis) to identify influential studies; and (2) Comparing results from random-effects and fixed-effect models to assess the impact of statistical assumptions. Publication bias was assessed visually using funnel plots and statistically using Egger’s regression test, while acknowledging the limited power of these tests given the small number of included studies (< 10).
The study selection process (Figure 1) comprised three phases. Phase 1 (primary database search): Electronic searches of PubMed, EMBASE, and Web of Science (from inception to September 12, 2025) identified 491 records. After removal of 111 duplicates, 380 records were screened by title and abstract, resulting in 50 records (25 categorized as “include” and 25 as “maybe”). For these 50 records, abstracts missing from Rayyan were retrieved from the source databases and reviewed, leading to the exclusion of 6 additional records (conference abstracts or wrong cell type). Full-text articles were sought for the remaining 44 records, of which one could not be retrieved. The 43 obtained full-text articles were independently assessed for eligibility by two reviewers. During full-text assessment, 37 articles were excluded with reasons detailed in Figure 1. Six studies were selected through this pathway.
Phase 2 (supplementary citation search): To reduce the risk of omission, we screened the reference lists of a broader, related SR identified via PubMed. This yielded 17 additional records for full-text assessment, 6 of which were considered eligible. Phase 3 (integration and deduplication): Combining results from both phases revealed that all 6 studies from phase 2 were duplicates of those already identified in phase 1. Consequently, after deduplication, six unique studies (R1-R6)[19,43-47] met all eligibility criteria and were included in the qualitative synthesis of this SR. All six included studies provided functional-recovery data suitable for meta-analysis, encompassing 132 animals. An updated search of all three databases was performed on August 31, 2026 and identified no additional eligible studies (Supplementary material).
The six studies (published 2008-2018) included in the qualitative synthesis involved 273 experimental animals across three species: Rats (3 studies, 210 animals), dogs (2 studies, 20 animals), and rabbits (1 study, 43 animals). The traumatic SCI models included compression (4 studies), contusion (1 study), and transection (1 study). All studies compared hUCB-MSC transplantation with control conditions involving no active treatment (e.g., sham operation, vehicle injection, or injury-only).
Assessment of methodological reporting revealed notable deficiencies: (1) Three studies reported random allocation, but none described the method; (2) Three studies reported blinding of outcome assessment; (3) Although all studies reported ethical approval, conflict of interest statements were absent in three studies; and (4) No study provided a sample size justification.
Intervention protocols varied. Cell doses per injection ranged from 1 × 106 to 2 × 106, although one study did not report the dose; administration routes included intralesional (3 studies) or intravenous injection (3 studies); and timing ranged from acute (≤ 24 hours post-injury) to subacute (> 24 hours). Table 1 summarizes the key characteristics of the included studies. Of note, study R1 did not report sufficient information to calculate the absolute cell dose per animal. The sample sizes listed in Table 1 are the total animal counts per study; the meta-analysis of functional recovery (n = 132) includes only the treatment and control groups from these studies. The BBB locomotor scale was used in four studies (R1, R3, R4, R5), a modified Tarlov scale in one study (R2), and the Reuter score in one study (R6). All six included studies provided quantitative data suitable for meta-analysis of functional recovery.
| Ref. | Study | Species | Injury model | Functional scale | Randomization | Blinding | Sample size1 | Cell dose (per injection) | Cell dose (total) | Route | Timing |
| Yin et al[43] | R1 | Rat | Transection | BBB | Not described | NR | 50 | NS | NS | IL | Acute |
| Lee et al[44]3 | R2 | Dog | Compression | Tarlov | Yes | Yes | 10 | 1 × 106 | 1 × 106 | IL | Subacute |
| Zhang et al[45] | R3 | Rat | Compression | BBB | Yes | NR | 62 | 1 × 106 | 1 × 106 | IV | Subacute |
| Lee et al[46]4 | R4 | Dog | Compression | BBB | NR | NR | 10 | 1-2 × 106 | 1-3 × 106 | IL | Subacute |
| Seo et al[47] | R5 | Rat | Contusion | BBB | Yes | Yes | 98 | 1 × 106 | 1 × 106 | IV | Acute |
| Yang et al[19]5 | R6 | Rabbit | Compression | Reuter2 | Not described | Yes | 43 | 2 × 106 | 6 × 106 | IV | Subacute |
We assessed methodological rigor and reporting quality using three complementary tools: The SYRCLE risk of bias tool, the CAMARADES checklist, and the ARRIVE 2.0 guidelines[40].
SYRCLE risk of bias assessment: Assessment using the SYRCLE risk of bias tool indicated predominantly “unclear” risk of bias across most domains for all six studies (Supplementary Figure 1). Importantly, details of random sequence generation and allocation concealment were lacking in all six studies (100% “unclear”), introducing significant uncertainty regarding internal validity. Blinding of personnel and outcome assessors was poorly reported, with only 3 of 6 studies (50%) rated as “low” risk for outcome assessor blinding. Incomplete outcome data and selective reporting were also predominantly “unclear” because relevant methods were not described. A summary is presented in Supplementary Figure 2.
Assessment using CAMARADES and ARRIVE 2.0: Adherence to reporting standards was assessed against the ARRIVE 2.0 guidelines. Scores from the CAMARADES checklist (mean total score: 5.0 out of 10, or 50.0%) and adherence to ARRIVE 2.0 guidelines (mean: 67.2%) further indicated substantial reporting deficiencies. Key items frequently missing or inadequately described included sample size justification (0% of studies), randomization methods (described in 0%), blinding of intervention (0% described), and temperature control during procedures. In contrast, items such as peer-reviewed publication and ethical approval were reported in all studies.
Overall implications: The collective findings from these assessments indicate that while the included studies address a biologically relevant question, the overall confidence in their methodological rigor is limited due to pervasive inadequate reporting. This high proportion of “unclear” risk judgments, particularly concerning randomization, blinding, and allocation concealment, introduces uncertainty regarding the internal validity of the primary studies and must be considered when interpreting the synthesized evidence.
Primary meta-analysis: A random-effects meta-analysis of six studies (132 animals) using the DL estimator with HKSJ adjustment indicated that hUCB-MSC transplantation was associated with significantly improved functional recovery after experimental SCI, with a large pooled effect size (SMD = 2.35, 95%CI: 0.89-3.80; P = 0.009). As shown in the forest plot (Figure 2), all six individual study estimates favored the hUCB-MSC treatment group, with individual SMDs ranging from 1.31 to 4.47. For study R6, this positive effect estimate follows the pre-specified transformation of the original Reuter score to align with the “higher-is-better” convention.
Heterogeneity assessment: Considerable statistical heterogeneity was observed in the primary analysis (I2 = 81.8%, τ2 = 1.535). The 95%PI was wide (95%PI: -1.15 to 5.85), indicating that the true effect size in a new, similar study could range from possible harm to substantial benefit. This heterogeneity may stem from the methodological and clinical diversity identified above, particularly the timing of intervention and injury model[48,49]. The implications of this heterogeneity for the robustness of the findings were formally assessed through sensitivity analyses (see the sensitivity analyses section).
Subgroup analyses: Pre-specified subgroup analyses revealed that the treatment effect varied considerably across experimental conditions (Figure 3; Supplementary Table 1). Subgroup analysis by intervention timing suggested potentially different effects: Subacute administration (> 24 hours) yielded a statistically significant effect (SMD = 1.98, 95%CI: 0.30-3.66; P = 0.033). In contrast, acute administration (≤ 24 hours) yielded a large point estimate (SMD = 2.88, 95%CI: -17.10 to 22.85) but did not reach statistical significance (P = 0.318) due to extreme heterogeneity (I2 = 94.5%).
Statistically significant pooled estimates were also observed in the canine model (SMD = 1.75, 95%CI: 1.21-2.28; P = 0.015) and in studies using the compression injury model (SMD = 1.98, 95%CI: 0.30-3.66; P = 0.033). In contrast, the rat model showed a large but nonsignificant effect (SMD = 2.32, 95%CI: -2.14 to 6.78; P = 0.155). Beyond limited sample sizes, the exceptionally high within-subgroup heterogeneity (I2 = 91.4%) indicates that species alone did not account for the overall variability. This severe inconsistency among studies utilizing the same animal model underscores the need for protocol standardization in preclinical SCI research. Similarly, for local and systemic administration (local: SMD = 2.73, 95%CI: -1.25 to 6.71, P = 0.098; systemic: SMD = 1.86, 95%CI: -1.24 to 4.95, P = 0.123), the pooled estimates did not reach statistical significance, likely due to limited sample sizes and substantial withinsubgroup heterogeneity (I2 ranging from 71.2% to 81.1%).
The low-dose subgroup (≤ 1 × 106 cells) showed a statistically significant effect with no observed heterogeneity (SMD = 1.40, 95%CI: 1.09-1.70; P < 0.001, I2 = 0%, k = 4). However, this subgroup included only four studies, and with such a small sample size, the I2 estimate has very limited statistical power and should not be interpreted as evidence of true biological homogeneity. The contrast between the observed low heterogeneity in the low-dose group and the marked variability (I2 often > 80%) in higher-dose groups may reflect confounding by factors associated with dose escalation, such as variations in cell viability, injection volume, or local tissue tolerance, rather than a direct dose-response relationship. For clinical translation, these observations support including low-dose arms in future dose-ranging studies, with the goal of identifying a minimal effective dose that ensures consistent and reproducible therapeutic effects. This observation is therefore purely hypothesis-generating and requires validation in larger, pre-specified dose-response studies. Notably, this dose categorization was based on absolute cell counts without normalization for interspecies differences in body weight; therefore, confounding by species cannot be excluded (see Limitations for a detailed discussion). The low-dose cutoff was pre-specified in the registered protocol as a median split of cell doses based on their distribution across the included studies; no formal interaction test was performed, as detailed in the Limitations section.
Meta-regression analyses: Given the small number of included studies (k = 6), we limited the formal meta-regression discussion to three pre-specified variables with clear biological rationale: Cell dose, injury model, and intervention timing. Although cell dose showed a nominally significant association (P = 0.006), none of these pre-specified variables can be regarded as reliable moderators of treatment effect given the limited statistical power and the lack of correction for multiple comparisons [injury model: P = 0.178; timing (categorical): P = 0.577; timing (continuous): P = 0.659]. An additional 15 exploratory variables were examined in supplementary analyses (Supplementary Table 2 and Supplementary Figure 3). However, because 18 univariate models were fitted to only six studies without correction for multiple comparisons, the risk of false-positive findings is substantial. Consequently, only the three pre-specified variables are discussed here; the remaining results should be regarded as purely exploratory and hypothesis-generating.
To assess the robustness of the primary finding, we performed sensitivity analyses. Because all included studies were rated as having “unclear” risk in several key SYRCLE domains, sensitivity analyses stratified by risk of bias were not feasible; this limitation is further discussed in the Limitations section. Leave-one-out analysis indicated that the exclusion of study R1[43] substantially reduced the pooled effect size (SMD = 1.74, 95%CI: 0.64-2.83), representing a 26.0% reduction from the reference estimate. Notably, the exclusion of R1 also markedly reduced heterogeneity (I2 = 43.3%), suggesting that it was a major contributor to the overall study variability. Despite this influence, the recalculated SMD remained statistically significant across all iterations, ranging from 1.74 to 2.61 upon sequential exclusion of any study (see sensitivity analysis plot, Supplementary Figure 4).
Comparison of the primary DL-HKSJ random-effects model and a fixed-effect model yielded a lower but still significant SMD of 2.00 (95%CI: 1.56-2.44), representing a 14.9% reduction from the random-effects estimate of 2.35. This difference, along with the influential nature of study R1, underscores the substantial heterogeneity present and justifies the primary use of a random-effects model. No study exclusion qualitatively changed the conclusion. Collectively, these sensitivity analyses support the persistence of the primary meta-analysis result.
A cumulative meta-analysis, ordered by publication year, was performed to examine the evolution of the evidence base over time. The pooled effect estimate became statistically significant with the inclusion of the fifth study (published in 2011) and remained significant thereafter. The point estimate of the SMD stabilized between 2.1 and 2.5 after the inclusion of the fifth study. The progression of cumulative effect estimates with 95%CIs is shown in Supplementary Figure 5. Heterogeneity (I2) was substantial from the outset and remained high (> 80%) throughout. The reporting of key methodological safeguards (randomization and blinding) did not show a clear trend of improvement over the publication years covered by the included studies.
Publication bias was assessed using both visual and statistical methods. Although the power of these methods is limited when few studies are available, we retained them because publication bias is a major concern in preclinical research[50]. Visual inspection of the funnel plot (Figure 4) showed no obvious asymmetry. Egger’s regression test was nonsignificant (P = 0.311) and did not detect small-study effects. Begg’s rank correlation test also showed no significant asymmetry (P = 0.136). Rosenthal’s fail-safe N was 21, while Orwin’s fail-safe N (using a trivial effect size of 0.1) was 135. Given the small number of studies (k = 6), these analyses have very limited power, and the relatively low Rosenthal’s N further warrants caution regarding unpublished null findings. Collectively, these analyses did not detect publication bias but cannot exclude it. Accordingly, the absence of detected publication bias should not be interpreted as evidence of its absence.
Safety outcomes: For the mortality analysis, we excluded animals from sham-operated control groups (uninjured animals) and included only SCI-induced animals from the treatment and model control groups, resulting in a total of 172 SCI-induced animals from six studies (R1-R6)[19,43-47]. The pooled analysis of mortality data from six studies (n = 172) did not show a statistically significant increase in risk associated with hUCB-MSC treatment (risk ratio = 1.20, 95%CI: 0.60-2.40). The reported deaths were attributed to procedural complications (e.g., postoperative sepsis) rather than directly to hUCB-MSC therapy itself. Although no tumorigenicity or ectopic tissue formation was reported in the included studies, follow-up periods were relatively short (ranging from 4 to 8 weeks post-transplantation). The absence of long-term monitoring (> 6 months) precludes definitive conclusions regarding the oncogenic risk of hUCB-MSC transplantation, particularly given the theoretical concern regarding the proliferative capacity of MSCs. Future preclinical studies should incorporate extended observation periods and systematic histopathological examination of distant organs to comprehensively assess long-term safety. Systematic monitoring and reporting of treatment-related adverse events were notably absent across the included studies. No study comprehensively documented potential complications such as tumor formation, ectopic tissue growth, systemic inflammatory responses, or adverse immunological reactions.
Evidence certainty (GRADE): We assessed the certainty of the evidence for the primary outcome (functional recovery) using a modified GRADE framework. The framework was adapted for preclinical evidence as follows: Certainty was rated separately for each species-level outcome, and imprecision was judged primarily on sample size and the width of the CI. For the overall functional recovery rating, risk of bias was not additionally downgraded because the pervasive “unclear” judgments predominantly reflected inadequate reporting rather than confirmed high risk (Table 2), and the indirectness inherent in translating animal findings to human SCI is addressed in the Limitations section. The initial “high” rating was downgraded two levels to “low” because of serious inconsistency (I2 = 81.8%) and serious imprecision (95%CI width = 2.91). This overall rating is further detailed for key subgroups in the GRADE evidence profile (Table 2). Notably, the certainty for outcomes based on specific species (dogs and rabbits) and for safety was further downgraded to “very low” due to very serious imprecision (e.g., very small sample size, or wide CIs encompassing both benefit and harm).
| Outcome (population) | Study IDs (number of animals) | Effect estimate (95%CI) | I2 | Certainty (GRADE) | Key limitations (reasons for downgrading) |
| Functional recovery | |||||
| Rat (BBB scale) | R1, R3, R5 (102) | SMD 2.32 (-2.14 to 6.78) | 91.4% | Low | Serious inconsistency (I2 > 80%), serious imprecision (wide CI crossing zero) |
| Canine | R2, R4 (16) | SMD 1.75 (1.21-2.28) | 0% | Very low | Very serious imprecision (very small sample size, n = 16); serious risk of bias |
| Rabbit (Reuter) | R6 (14) | SMD 3.79 (2.04-5.54) | N/A | Very low | Very serious imprecision (very small sample size, n = 14); serious indirectness (scale transformation) |
| Safety | |||||
| Mortality (all species) | R1, R2, R3, R4, R5, R6 (172) | RR 1.20 (0.60-2.40) | 30% | Very low | Very serious imprecision (CI includes both appreciable harm and no difference), serious risk of bias (inadequate AE reporting) |
This SR and meta-analysis evaluated the efficacy and safety of hUCB-MSCs for experimental SCI. Our analysis of six included studies found that hUCB-MSC therapy was associated with significantly improved functional recovery compared to controls, with a large pooled effect size (SMD = 2.35, 95%CI: 0.89-3.80; P = 0.009). However, this finding should be interpreted with caution due to substantial heterogeneity (I2 = 81.8%) and low certainty of the evidence according to GRADE assessment.
Our primary meta-analysis of six controlled animal studies, including 132 animals, indicated that hUCB-MSC transplantation was associated with a substantial functional benefit after experimental SCI, with a large pooled effect size (SMD = 2.35, 95%CI: 0.89-3.80; P = 0.009). This finding is consistent with the recognized multimodal mechanisms of MSCs, which mediate repair primarily through immunomodulation, secretion of neurotrophic and angiogenic factors, and mitigation of secondary injury cascades, rather than direct neuronal replacement[51,52]. The magnitude of the observed effect for hUCB-MSCs (SMD = 2.35) is large, exceeding the conventional threshold for a large effect (SMD ≥ 0.8)[53]. However, we caution that this estimate is likely inflated by methodological limitations in the primary studies. All six included studies were rated as having “unclear” risk for random sequence generation and allocation concealment, and blinding of personnel was poorly reported. In preclinical research, such methodological deficiencies are consistently associated with effect-size inflation[50,54,55]. Consequently, the true effect in rigorously conducted, blinded studies may be substantially smaller than our pooled estimate. This is further supported by our leave-one-out sensitivity analysis, in which exclusion of the influential study R1 reduced the pooled SMD by 26% to 1.74. While the direction of effect appears consistent with reports for other MSC sources in preclinical SCI[56,57], direct numerical comparisons are limited by differences in outcome measures and analytical methods. The 95%PI was wide (95%PI: -1.15 to 5.85), indicating that the true effect size in a new similar study could range from possible harm to substantial benefit. Therefore, while the average pooled effect is large, its reliability is limited by this unexplained variance and the pervasive uncertainty regarding performance bias in the underlying evidence base.
The consistent large effect across studies supports the biological plausibility of hUCB-MSC therapy. This effect likely stems from a multipotent paracrine secretome capable of simultaneously modulating key secondary injury processes, including inflammation, excitotoxicity, and apoptosis, while promoting angiogenesis and axonal sparing[58,59]. The pronounced efficacy observed for hUCB-MSCs may be attributable to their unique ontogeny. Cord blood-derived cells are considered a more primitive population with proposed advantages that include high proliferative capacity, strong paracrine activity, and a particularly favorable immunomodulatory profile that may allow for greater histocompatibility mismatch compared to adult tissue-derived MSCs[18,19,60]. Mechanistically, Park et al[61] demonstrated that hUCB-MSCs promote functional recovery partly by enhancing endogenous cell proliferation and oligogenesis, supporting the neurotrophic mechanism of action discussed above.
Importantly, the large effect size (SMD = 2.35) observed for native hUCB-MSCs in this study provides an initial quantitative reference. The field has recently shifted focus toward complex engineered interventions, such as preconditioned cells, MSC-EVs, or biomaterial-scaffold combinations, to address translational challenges like poor cell survival. Establishing a clear efficacy baseline for native cells is essential for evaluating these next-generation strategies. This reference point may serve dual purposes: First, it provides an initial efficacy benchmark against which future engineered therapies can be compared[22-24]. Second, it may inform sample size calculations in future preclinical studies designed to evaluate the superiority of advanced therapies over native cell transplants.
Critically, our pre-specified subgroup analyses revealed that the therapeutic effect may not be uniform. Subacute administration (> 24 hours post-injury) yielded a statistically significant effect (SMD = 1.98, 95%CI: 0.30-3.66; P = 0.033), whereas acute administration (≤ 24 hours) did not reach statistical significance (P = 0.318) due to extreme heterogeneity (I2 = 94.5%). However, this finding should be interpreted cautiously, as meta-regression did not confirm timing as a significant moderator of effect size (P = 0.577), and the discrepancy between subgroup and meta-regression results likely reflects the limited statistical power of both analyses with only six studies. The extreme variability observed in the acute administration group may reflect the volatile and complex inflammatory microenvironment characteristic of early secondary injury cascades[58,59,62]. For clinical translation, although this pattern suggests that subacute administration warrants further study, the optimal timing window remains uncertain.
A recent SR by Nguyen et al[63] on UCB-derived cell therapy for perinatal brain injury similarly concluded that efficacy is limited by low certainty of evidence. This convergence of findings across neurological domains is instructive. It illustrates that “low” certainty should not be misconstrued as evidence of inefficacy, but rather as an indication that the field should adopt more rigorous and standardized preclinical methodologies, such as those outlined in the ARRIVE 2.0 guidelines. The distinct pathophysiology of SCI, particularly the formation of a glial scar and the persistent inflammatory milieu, warrants continued but more rigorous investigation.
It is worth noting that a recent network meta-analysis of animal studies by Lu et al[56] likewise found significant functional improvement with umbilical cord MSC transplantation across dose, route, and timing subgroups, and a 2025 umbrella review by Azimi et al[57] reported a pooled SMD of 2.34 (95%CI: 1.76-2.93) for umbilical cord-derived MSCs, nearly identical to our estimate of 2.35. This convergence of independent estimates supports the overall therapeutic potential of MSC-based therapies for SCI. Additionally, Guo et al[64] reported that hUCB-MSC transplantation promoted functional improvement in a rat SCI model, consistent with our pooled findings.
The substantial statistical heterogeneity quantified in our primary analysis (I2 = 81.8%, τ2 = 1.535) reflects the considerable methodological and clinical diversity inherent in the current body of preclinical SCI research. Our exploratory analyses examined several potential sources of this variation and provide preliminary guidance for protocol optimization and translational planning.
First, as detailed in the synthesis of therapeutic effects section, the three pre-specified meta-regression variables (cell dose, injury model, and intervention timing) did not show reliable associations with treatment effect. Exploratory analyses of 15 additional variables (Supplementary Table 2) are hypothesis-generating only, as the large number of tested moderators (n = 18) relative to the small number of studies (k = 6) introduces a high risk of false-positive results. The association with injury model was not statistically significant (P = 0.178). The considerable heterogeneity observed across injury models underscores the challenge in translating results from highly controlled models with limited clinical relevance (e.g., complete transection) to the complex, dynamic pathophysiology of human contusion/compression injuries, which involve persistent compression, ischemia, and evolving secondary damage[25,26]. Consequently, future advanced preclinical studies should prioritize the use of clinically relevant injury models in large animal species to improve the predictive validity of therapeutic outcomes for human trials[65,66].
Second, among the three pre-specified meta-regression variables, cell dose showed the strongest association with effect size (P = 0.006), though the reliability of this association is limited by the small sample size and the lack of correction for multiple comparisons. As detailed in the synthesis of therapeutic effects section, this model was fitted alongside 15 other exploratory variables without correction for multiple comparisons, so this association may reflect a type I error rather than a true biological moderator. Cell dose should therefore not be regarded as an established determinant of efficacy based on these limited data. Within the studied ranges, several other technical variables, including cell passage number and route of administration, showed no evidence of moderating the treatment effect in exploratory analyses (Supplementary Table 2). These underpowered analyses do not support conclusions about protocol flexibility; instead, they shift attention from the absolute quantity of cells delivered to their functional quality and potency. Emerging consensus indicates that the therapeutic efficacy of MSCs may hinge more critically on their secretory profile, immunomodulatory capacity, and ability to adapt to the host microenvironment than on cell number alone[67].
The considerable heterogeneity we observed is also consistent with a SR by Sharif-Alhoseini et al[68], which highlighted that methodological diversity across injury models, particularly in contusion paradigms, is a well-documented source of outcome variability that can obscure true treatment effects. Our finding that low-dose hUCB-MSCs yielded low observed heterogeneity (I2 = 0%) thus stands out as a tentative observation that may reflect a more consistent signal, though this requires validation in larger studies as discussed in the Limitations section.
Hypothesis-generating consideration: The apparent consistency observed in the low-dose subgroup (I2 = 0%) may reflect the small number of studies (k = 4) and should not be interpreted as evidence of biological homogeneity. Potential dose-related differences in biodistribution or host responses[69] could contribute to this observation, but this hypothesis requires validation in adequately powered prospective studies designed specifically to test dose-response relationships.
The tentative observations regarding low-dose consistency and the limitations of absolute cell counts underscore the need to redefine dosing parameters. Future research should therefore aim to define and standardize critical potency attributes[70] and establish a “functional potency dose” based on quantifiable in vitro attributes (e.g., trophic factor secretion, immunomodulation scores) that correlate with in vivo efficacy, rather than relying solely on cell counts[71].
Despite these identified sources of heterogeneity, a substantial proportion of between-study variance remains unexplained by our meta-regression models. This residual heterogeneity may stem from unmeasured or unreported factors such as donor variability in umbilical cord blood samples (e.g., maternal age, collection volume, processing methods), differences in cell culture conditions (e.g., growth media composition, oxygen tension, passage-related senescence), and variations in surgical expertise and postoperative care protocols across different laboratories. Future studies should systematically report these critical technical variables to permit more precise identification of sources of variability.
Our findings are consistent with the rationale for further investigating these advanced strategies, though rigorous validation in standardized models is required before firm conclusions can be drawn. The association observed in the subacute subgroup (> 24 hours) suggests that hUCB-MSCs may improve functional recovery even after the establishment of the early inflammatory cascade. This finding, combined with the variability observed in acute administration, provides a rationale for testing biomaterial scaffolds[22,23] or EV-loaded hydrogels[22] to standardize cell delivery, retention, and localized action, with the aim of reducing heterogeneity and improving reproducibility in future studies.
Assessment using the SYRCLE risk of bias tool revealed predominantly “unclear” risk judgments across most domains, particularly for random sequence generation, allocation concealment, and blinding of personnel (100% “unclear” for each). This pervasive lack of methodological transparency poses a serious threat to internal validity and severely limits our confidence in the observed effect estimates. These reporting deficits are further quantified by the mean score on the CAMARADES checklist (5.0 out of 10, 50.0%) and variable adherence to ARRIVE 2.0 guidelines (mean: 67.2%)[40]. The 100% “unclear” rating for randomization and blinding is particularly concerning given that these are well-established safeguards against selection and performance bias, with the most frequently missing items being sample size justification, description of randomization method, and blinding of the intervention[32,35,38]. While this pattern may reflect inadequ
These findings underscore an essential requirement for future preclinical studies. To strengthen the evidence base and facilitate reliable translation, researchers must rigorously adhere to reporting guidelines such as ARRIVE 2.0. Using tools such as the SYRCLE checklist or CAMARADES framework during the study design phase is essential to ensure that bias-minimizing measures are not only implemented but also transparently and comprehensively documented in the final publication. Accordingly, we cannot exclude the possibility that the very large observed effect size is inflated by methodological limitations and performance bias in the primary studies (see the interpretation of main findings section for a detailed discussion).
Sensitivity analyses indicate that the positive pooled estimate for functional recovery persisted across study exclusions. Leave-one-out sensitivity analysis identified study R1[43] as an influential study; its exclusion reduced the pooled SMD to 1.74 (a 26.0% reduction). Despite this influence, the treatment effect remained statistically significant across all sensitivity iterations (SMD range: 1.74 to 2.61), indicating that the direction of the pooled effect was stable but potentially influenced by the specific characteristics of early transection model studies. Cumulative meta-analysis, ordered by publication year, indicated that the pooled effect became statistically significant upon inclusion of the fifth study (published in 2011) and remained stable thereafter, suggesting the finding is not dependent on late-emerging data. The relative stability of the point estimate, despite substantial and persistent heterogeneity throughout the evidence accumulation process, suggests a persistent treatment signal, although its magnitude remains uncertain.
Assessment of publication bias, a major concern in preclinical research, did not identify statistically significant small-study effects. Visual inspection of the funnel plot suggested a roughly symmetrical distribution, and Egger’s regression test was nonsignificant (P = 0.311). Orwin’s fail-safe N was 135, whereas Rosenthal’s fail-safe N was 21; given the small number of studies, these values provide limited reassurance against unpublished null findings. However, it is crucial to emphasize that with only six included studies, the statistical power of these publication bias tests is inherently limited; therefore, the absence of detected publication bias should not be interpreted as definitive evidence of its absence. Furthermore, internal biases (e.g., performance bias due to lack of blinding) and publication bias may interact in a non-additive manner, potentially amplifying their overall impact on the observed effect size, a methodological nuance underscored in recent statistical literature[72]. Thus, although traditional metrics did not detect bias, they provide limited reassurance; the true effect size may be more uncertain, a caveat reflected in the “low” GRADE rating.
This uncertainty also motivates investigation of emerging acellular approaches, such as those using well-characterized MSC-EVs[20,21]. EV-based therapies, which encapsulate key therapeutic factors while minimizing risks associated with whole-cell transplantation (e.g., uncontrolled differentiation, microvascular occlusion), may offer a promising approach for achieving more predictable and safer therapeutic outcomes[73]. The effect size reported in this meta-analysis may serve as a useful reference point for evaluating the efficacy of such EV-based products.
Analysis of safety outcomes from the six studies that provided relevant data (n = 172 animals) did not demonstrate a statistically significant increase in mortality risk associated with hUCB-MSC treatment (risk ratio = 1.20, 95%CI: 0.60-2.40). Reported deaths were attributed to procedural complications rather than to cell therapy itself. This finding is broadly consistent with reports of a favorable safety profile for hUCB-MSCs in other preclinical and limited clinical contexts of regenerative medicine; this profile has been linked to their low immunogenicity and immunomodulatory capacity[10,60,74].
However, a critical limitation must be emphasized: Systematic monitoring and reporting of treatment-related adverse events were notably absent across the included studies. None of the studies comprehensively documented potential complications such as tumor formation, ectopic tissue growth, systemic inflammatory responses, or adverse immunological reactions. Consequently, while the available mortality data are reassuring, the existing preclinical evidence provides an incomplete safety profile that cannot characterize the complex immunological and long-term risks in heterogeneous human patient populations with chronic injuries and comorbidities.
Despite these preclinical limitations, limited short-term safety data are emerging from clinical trials of hUCB-MSCs in other neurological disorders. For instance, a phase I trial by Kim et al[75] reported that intracerebroventricular injection of hUCB-MSCs was safe and well tolerated in patients with Alzheimer’s disease dementia. Such clinical data, although from a different disease context, provide indirect translational reassurance but do not establish safety in SCI; they support the continued clinical development of this cell source for CNS indications.
These efficacy and safety findings may inform a cautious translational pathway. The large but heterogeneous effect size observed in this preclinical synthesis, combined with the absence of a statistically significant mortality signal but incomplete adverse-event reporting, does not, by itself, establish readiness for clinical translation but may eventually inform the careful design of early-phase clinical trials. If clinical trials are pursued after further confirmatory preclinical work, key design principles should include: (1) Exploring intervention windows across both acute and subacute phases, as the evidence regarding optimal timing remains inconclusive. While subgroup analysis suggested a significant effect for subacute administration, meta-regression did not identify timing as a significant moderator (P = 0.577), likely due to limited statistical power. Future studies should directly compare different time windows within the same experimental design to clarify this question; (2) Incorporating rigorous protocol-defined safety monitoring for both acute adverse events and long-term outcomes, as emphasized in reviews of early-phase stem cell trials[76]; and (3) Employing dose-escalation designs to formally assess safety and tolerability while exploring potential efficacy signals, an approach successfully implemented in recent phase I/II studies of MSC-based therapies[77]. Initial trials could focus on well-defined patient subgroups with acute SCI to maximize the potential for detecting a biological effect based on the preclinical evidence presented here.
Our review has several limitations that should be considered. First, regarding the scope and evidence base, the focused scope on native hUCB-MSC monotherapy necessarily resulted in a small number of included studies (k = 6 for functional outcomes), which limits the statistical power of subgroup, meta-regression, and publication bias analyses. Although Egger’s test was not significant, the limited number of studies inherently reduces the power to detect publication bias. Additionally, the use of the DL estimator with this small sample may yield less reliable estimates of between-study variance and CIs compared to REML estimation; however, our sensitivity analyses comparing random-effects and fixed-effects models yielded consistent results, supporting the robustness of our findings.
Second, our literature search did not include Chinese-language databases (CNKI, Wanfang, VIP, SinoMed). China is a major contributor to MSC preclinical research, and this omission may have limited the comprehensiveness of our evidence synthesis. Future updates should incorporate these databases to mitigate this limitation. Third, the overall risk of bias was unclear for the majority of domains (86.7%), with all six studies rated as having “unclear” risk for randomization and allocation concealment. This precluded sensitivity analyses stratified by risk of bias and raises the possibility that treatment effects may be overestimated in the included studies. While we employed traditional tools, our assessment of more complex bias dynamics (e.g., the interaction between performance bias and selective reporting) was necessarily qualitative[72]. Moreover, significant heterogeneity was observed among the included studies (I2 = 81.8%, P < 0.001). This heterogeneity may stem from differences in injury models, intervention protocols, and animal species. Specifically, heterogeneity in dosing regimens within some included studies posed a challenge for meta-analysis. Although we employed a statistical method to combine subgroup data, the potential impact of different doses on the overall effect size could not be excluded. In leave-one-out analyses, sequential exclusion of each study, including R2, R4, and R6, which had heterogeneous dosing regimens, did not qualitatively change the results (pooled SMD range: 1.74 to 2.61, all remaining statistically significant).
Finally, regarding dose-response relationships and translational implications, findings from our subgroup and meta-regression analyses should be interpreted as hypothesis-generating rather than definitive. A critical methodological limitation is that our dose subgrouping was based on absolute cell counts (≤ 1 × 106 cells), which does not account for interspecies differences in body weight or surface area. The included studies span three species (rats, dogs, and rabbits) whose body weights differ by an order of magnitude; consequently, the equivalent dose per unit body weight varies considerably across studies. This limits biological comparability across species and creates a potential confound because apparent dose effects may partly reflect species differences. Although exploratory meta-regression identified a nominally significant association with total cell dose (P = 0.006), this must be interpreted with extreme caution given the small number of studies (k = 6), the lack of correction for multiple testing, and the confounding between dose and species. Notably, the low-dose subgroup (≤ 1 × 106 cells) demonstrated a statistically significant effect with no observed heterogeneity (I2 = 0%), whereas higher doses were associated with greater variability. The I2 = 0% observed in the low-dose subgroup (k = 4) should not be interpreted as evidence of true biological homogeneity; with such a small number of studies, the statistical power to detect heterogeneity is extremely limited, and the estimate is highly unstable. Additionally, we did not perform a formal subgroup interaction test (e.g., a Q-test for subgroup differences) to directly compare low-dose vs high-dose effects, because the small number of studies (k = 6) provides insufficient statistical power for such a test to yield reliable results. Without this, concluding that a dose difference exists simply because one subgroup was statistically significant and another was not would be methodologically unsound. This observation is hypothesis-generating only and requires validation in larger, adequately powered studies that employ dose normalization (e.g., per kilogram body weight or body surface area) and are specifically designed to test dose-response relationships. Furthermore, the inherent translational gap between controlled animal models and human SCI limits direct extrapolation of effect sizes to clinical settings[25]. The “low” certainty of the evidence also reflects the indirectness inherent in a preclinical synthesis: Our findings are derived from highly controlled animal models, which inevitably simplify the complexity of human SCI pathophysiology, including comorbidities, age-related differences in regenerative capacity, and the chronic phase of injury where most clinical interventions occur[25]. The translational value of any time window identified in preclinical models, while mechanistically insightful, must be rigorously tested in clinical settings where logistical and safety constraints may alter the feasibility of ultra-early intervention.
Based on our findings, we propose the following recommendations for future preclinical research.
Enhance methodological rigor and transparency: Future studies should adhere rigorously to reporting guidelines such as ARRIVE 2.0[40] and use tools such as the SYRCLE checklist during design and reporting. Detailed descriptions of randomization, blinding, allocation concealment, and sample size calculations are essential to reduce “unclear” risk of bias and enhance reproducibility.
Integrate native cell therapy with engineering innovations: Two strategic pathways are recommended: (1) From cells to enhanced products: Research should transition from solely optimizing native cell transplantation parameters to engineering enhanced therapeutic products. Priorities include developing potency assays for hUCB-MSCs that predict in vivo efficacy in SCI models, moving beyond surface marker characterization; systematically testing preconditioning protocols (e.g., hypoxic, inflammatory cytokine priming) to standardize and amplify the therapeutic secretome of hUCB-MSCs[24]; and designing combinatorial therapies in which hUCB-MSCs or their derivatives are integrated with biomaterial carriers (e.g., hydrogels, nanoparticles) that provide structural support, controlled release, and protection from the hostile microenvironment[22,23]; and (2) Cell-free strategies as a parallel pathway: Given the mechanistic importance of paracrine actions, dedicated research should compare the efficacy and safety profiles of native hUCB-MSCs with those of their derived EVs in standardized models[20,21]. Dose equivalency and mechanism-of-action studies are needed to define the position of EV-based therapies within the translational pipeline[73].
Adopt clinically relevant advanced models: The foundational efficacy of native hUCB-MSCs should be confirmed in large animal models with contusion/compression injuries that more closely mimic human SCI pathophysiology, including, where scientifically and ethically justified, nonhuman primates. Only after a reliable baseline is established should the added biological complexity of engineered therapies be evaluated in these models[27].
Conduct comprehensive safety and dose-finding studies: Dedicated studies with extended follow-up periods are required to rigorously assess long-term safety, including tumorigenicity and systemic effects. Integrated efficacy and safety studies should employ dose-ranging designs to identify the optimal therapeutic window in which maximal efficacy is balanced with an acceptable safety profile.
Facilitate data sharing and comparative analysis: Establishing standardized data repositories for preclinical SCI studies would enable more powerful comparative and individual animal data meta-analyses in the future, helping to resolve residual heterogeneity and identify animal- or injury-specific factors influencing treatment response.
We synthesized preclinical evidence for hUCB-MSC therapy in experimental SCI. The analysis indicates an association between hUCB-MSC transplantation and improved functional recovery (SMD = 2.35, 95%CI: 0.89-3.80; P = 0.009). However, subgroup analysis and meta-regression provided discordant results regarding the optimal delivery window (subgroup P = 0.033; meta-regression P = 0.577), likely reflecting limited statistical power. Consequently, the optimal delivery window remains undetermined. No statistically significant increase in short-term mortality risk was detected in animal models. However, due to serious inconsistency (I2 = 81.8%) and serious imprecision, the overall certainty of the evidence was rated as “low” according to GRADE criteria. Given the limited number of eligible studies (k = 6), these findings should be interpreted as hypothesis-generating and require validation in larger preclinical studies. Future research should directly compare acute and subacute delivery within standardized experimental designs to clarify the optimal timing, employ clinically relevant large animal models, and systematically evaluate both efficacy and long-term safety.
The authors would like to acknowledge Professors An Hong and Xiao-Jia Chen of Jinan University for their help during manuscript preparation. During the preparation of this work, the authors used DeepSeek, Kimi, and Zhipu Qingyan (ChatGLM) to assist with R scripting for statistical analysis and English language polishing. After using these tools, the authors reviewed and edited the content as needed and accepted full responsibility for the content of the article.
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