Transdermal testosterone gel vs placebo in women with diminished ovarian reserve prior to in vitro fertilization: a randomized, clinical trial

Domain: neuroscience
Published: 2026-02-12
Editorial outcome: minor_revision

Abstract
Diminished ovarian reserve (DOR) is common in women with infertility and is associated with poorer in vitro fertilization (IVF) outcomes. Testosterone is widely used off-label in this patient group, although evidence for its efficacy and safety is limited. To address this, we conducted a triple-blind, placebo-controlled, randomized clinical trial evaluating whether transdermal testosterone gel prior to IVF improves clinical pregnancy rates in women with DOR. Females aged 18-43 with infertility and DOR according to the Bologna criteria were recruited at 10 fertility clinics in Europe between April 2015 and November 2022. Of 316 assessed for eligibility, 290 were enrolled and randomized. Two were excluded from the primary analysis as their treatment coincided with the onset of the COVID-19 pandemic, and they did not start ovarian stimulation, leaving 288 participants. Participants were randomized to 5.5 mg of transdermal testosterone or matching placebo once daily for ~9 weeks prior to ovarian stimulation. All participants received ovarian stimulation in a long GnRH-agonist cycle with 300 IU/day of highly purified human menopausal gonadotropin; fresh embryo transfer was performed if an embryo was available. The primary outcome was clinical pregnancy rate following fresh embryo transfer, defined as an intrauterine gestational sac with an embryo demonstrating cardiac activity at ≥7 weeks’ gestation. Of the 288 participants, 134 were randomized to testosterone and 154 to placebo. Clinical pregnancy rates did not differ significantly, occurring in 21 women (15.7%) in the testosterone group and 23 (14.9%) in the placebo group (risk ratio (RR), 1.05; 95% confidence interval (CI) 0.61 to 1.81, p = 0.86). The study was terminated for futility at the prespecified interim analysis based on a conditional power calculation once 70% of the target sample size were randomized. In this study, transdermal testosterone did not improve clinical pregnancy rates compared with placebo in patients with infertility and DOR.

Introduction
Infertility is increasing globally, affecting 1 out of 6 couples worldwide1. One of the major causes of infertility is delayed childbearing, which is associated with a profound decline in ovarian reserve, oocyte quality and embryo euploidy rates2. According to the CDC, diminished ovarian reserve (DOR) was the reason for undergoing in vitro fertilization (IVF) in 27% of IVF cycles in 2021, making it the third most frequent indication3.

Considering that the probability of live birth following IVF is associated with the number of oocytes retrieved4–8, numerous treatments have been proposed prior to IVF for women with DOR to increase oocyte yield and improve pregnancy rates9. Despite widespread use, these therapies frequently lack substantial evidence for their safety and efficacy9. One such proposed treatment is testosterone prior to ovarian stimulation.

Animal studies have shown that testosterone treatment promotes the initiation of follicular growth, increases FSH-receptor expression, augments responsiveness to FSH stimulation, and may prevent apoptosis and follicular atresia, thus facilitating oocyte maturation10. This has led to the off-label use of testosterone as a pre-treatment for women with DOR undergoing IVF to increase the number of oocytes retrieved and ultimately to improve live birth rates11,12.

Seven randomized controlled trials (RCTs)13–19 and an even greater number of meta-analyses10,20–24 have investigated the effects of testosterone in women with DOR. However, the sample sizes of the RCTs were small (ranging from 50 to 159 participants), and only one was placebo-controlled13. Additionally, there is substantial heterogeneity in the dose and the duration of testosterone treatment used10,25,26, leading to inconclusive findings26. Despite clinical practice guidelines not routinely recommending or lacking specific guidance on the use of testosterone9,27, approximately 50% of reproductive medicine specialists prescribe it off-label for women undergoing fertility treatment11,12. To address this uncertainty, we performed the first multicenter, multinational, randomized, placebo-controlled study, the Testosterone Transdermal Gel for Poor Ovarian Responders Trial (T-TRANSPORT), to test the hypothesis that transdermal testosterone gel treatment in women with DOR would improve the clinical pregnancy rate compared to placebo, and to evaluate the efficacy and safety of this treatment.

Results
There were 290 eligible participants individually randomized between 24 April 2015 and 12 August 2022, 136 to testosterone and 154 to placebo (Figs. 1 and 2). Two participants in the testosterone group were excluded from the efficacy analyses as their treatment coincided with the start of the COVID-19 pandemic and their IVF cycles were cancelled; both subsequently re-entered the study after a wash-out period >3 months and were re-randomized. Therefore, 288 participants were included in the efficacy analysis. Overall, 255/288 (88.5%) completed the study according to the protocol: 134/154 (87.0%) in the placebo group and 121/134 (90.3%) in the testosterone group. All 290 participants who were randomized were included in the safety analysis. The number of participants included from each study site is shown in Supplementary Table 1.

The baseline participant characteristics were similar in the two groups (Table 1). The higher number of patients randomized to placebo was a result of the stratified block randomization and the small patient numbers in some age groups at some sites.

In the intention-to-treat analysis, the clinical pregnancy rate was 15.7% in the testosterone group and 14.9% in the placebo group (RR 1.05; 95% CI 0.61 to 1.81, p = 0.86; Table 2). There were no between-group differences in the pre-specified secondary endpoints of: cycle cancellation; cycles reaching embryo transfer; biochemical pregnancy rate; ongoing pregnancy rate; number of oocytes retrieved; number of mature (metaphase II) oocytes retrieved; number of top-quality embryos available on day 3; or number of cycles with supernumerary embryos available (Tables 2 and 3). The antral follicle count did not differ on the day of starting stimulation (5.0 ± 2.3 in the placebo group compared to 5.0 ± 2.8 in the testosterone group). There were no significant between group differences in the rates of live birth, multiple pregnancy, miscarriage, stillbirth or ectopic pregnancy (Table 2). Obstetric and neonatal outcomes were similar between the two groups (Table 4).

All 23 clinical pregnancies in the placebo group were singleton pregnancies; in the testosterone group, 4 out of 21 clinical pregnancies were twin pregnancies, and the remainder were singletons. Of the 6 miscarriages in the testosterone group, 1 occurred in a twin pregnancy. There was a single stillbirth in the study, of a singleton pregnancy in the testosterone group. There were no congenital anomalies reported in either group.

A planned subgroup analysis for participants aged <36, 36–39 and ≤40 did not reveal any between-group differences; however, event rates were low in these analyses, and the study was underpowered to detect differences in these subpopulations (Table 2).

As expected, serum total testosterone levels were significantly higher in the testosterone group than the placebo group on the day of starting ovarian stimulation (at completion of the study drug), measuring 3.11 ± 2.61 nmol/L compared to 0.61 ± 0.36 nmol/L (MD 2.50; 95% CI 1.99 to 3.01, p < 0.001) (Fig. 3).

The study was terminated for futility by the DSMB based on the results of the pre-planned interim analysis. After 72.5% of the target sample size was randomized, a conditional power calculation was performed, which predicts the likelihood of rejecting the null hypothesis if the study were to be continued. Using the current trend assumption gave a conditional power of 0.08%; using the hypothesized effect assumption gave a conditional power of 6.2%28,29. Both were well below the pre hoc futility threshold of 20%, indicating that the likelihood of the study demonstrating a significant difference in the primary outcome between groups if continued was extremely low. Based on these results and as per the study protocol, the study group terminated the trial on advice of the DSMB.

The safety analysis included all randomized participants (n = 290). Overall, 154 (53.1%) participants experienced at least one adverse event. There were no significant differences between groups in the incidence of adverse events, serious adverse events, withdrawal due to adverse events, application site reactions or androgenic events overall, however more participants in the testosterone group reported increased hair growth (14.7% vs 7.1% (RR 2.05; 95% CI 1.02 to 4.14, p = 0.03)) (Table 5). There was no difference in the Ferriman-Gallwey (FG) scores or the incidence of hirsutism (FG score ≥ 8) between groups (Table 5).

Two participants in the placebo group reported pre-specified serious adverse events: an extrapyramidal reaction and an overdose of the placebo gel. The study medication was discontinued in the second participant. Neither participant was withdrawn from the study due to these side effects. There were no serious adverse events in the testosterone arm. Two participants discontinued the placebo gel due to adverse events. One reported acne and irritability/bad mood; the other reported per vaginal bleeding. There were no discontinuations for adverse events in the testosterone arm.

Methods
Study design and setting
This multicenter, parallel, randomized, triple-blind, placebo-controlled clinical trial was conducted across 10 tertiary fertility clinics in 4 European countries (Spain, Belgium, Denmark and Switzerland) between April 2015 and November 2022, with the final participant randomized in August 2022. Participants were followed up until delivery if pregnant. The trial was approved by the Medical Ethics Committee of the Universitair Ziekenhuis Brussel (Ref: 2014/148) and by the ethics committees of each participating center (Belgium: Comissie Medische Ethiek UZ Brussel; Spain: Comité Ético de Investigación Clínica del Grupo Hospitalario Quironsalud; Denmark: Videnskabsetiske Komitéer for Region Midtjylland; Switzerland: Swissethics). The study was monitored by an independent Data Safety Monitoring Board (DSMB) as well as an independent Clinical Research Organization. The trial was prospectively registered at ClinicalTrials.gov (NCT02418572).

Study participants
Eligible participants were females with infertility and DOR aged 18–43 years old and planning ovarian stimulation for IVF. DOR was defined by the Bologna criteria35. Specifically, if aged <40 years, participants were required to have had ≤3 oocytes retrieved in a previous IVF cycle and an antral follicle count (AFC) <7; or ovarian surgery/chemotherapy and an AFC <7; or ≤3 oocytes in at least 2 previous cycles with ≥300 IU gonadotropins per day. If aged ≥40 years old, they were required to have had ≤3 oocytes retrieved in a previous cycle or have an AFC <7. Exclusion criteria included perimenopause, a basal FSH >20 IU/L, uterine malformations, hydrosalpinx (unless clipped), recent history of an untreated endocrine abnormality, contraindication to the use of gonadotropins, recent history of a severe disease requiring regular treatment, use of androgens within the previous 3 months, SHBG <20 nmol/L or >160 nmol/L, or planning to use surgically retrieved sperm.

All participants provided written informed consent. Participants did not receive compensation in exchange for their participation.

Randomization and blinding
Potential participants were screened for eligibility, and consent was obtained at the pre-treatment visit. Randomization was performed on day 1 of the subsequent menstrual cycle. Participants were randomly assigned to 5.5 mg per day of transdermal testosterone as 1% gel or an identical placebo in a 1:1 ratio, both supplied in identical metered-dose pumps by Besins Healthcare. The placebo gel was identical in composition to the active gel except for the 1% testosterone, which was replaced with 1% water. The randomization sequence was prepared and held centrally by an independent statistician using a random number table in permuted blocks of 6 participants, stratified by age (<36, 36–39 and ≥40 years old) and study site. Participants, clinicians, outcome assessors and statisticians were all blinded to group allocation. Figure 1 shows the CONSORT Study Flow Diagram.

Procedures
Each participant was instructed to apply 0.55 g (one pump) of either 1% testosterone gel (5.5 mg of testosterone) or placebo gel to their thighs each morning from the day of randomization for approximately 9 weeks. Approximately 7 weeks later, on day 21 of the subsequent menstrual cycle (i.e. after one intervening menstrual period), pituitary downregulation commenced with 100 mcg subcutaneous triptorelin daily. After 14 days, and once pituitary downregulation was confirmed by a serum estradiol <70 ng/L, the study medication was ceased and ovarian stimulation with 300 IU/day of subcutaneous highly purified human menopausal gonadotropin commenced. Once two follicles ≥17 mm were observed on transvaginal ultrasound, 250 mcg of subcutaneous recombinant human chorionic gonadotropin was administered. Thirty-six hours later, oocytes were collected and fertilized by intracytoplasmic sperm injection (ICSI). On day 3 after oocyte retrieval, a maximum of 2 embryos were transferred according to each center’s criteria on single/double embryo transfer. Luteal phase support was prescribed with 200 mg intravaginal micronized progesterone three times daily commencing the day after oocyte retrieval and continuing for at least 6 weeks, or until a negative pregnancy test ≥12 days after the embryo transfer (Fig. 2). Compliance and adverse events were assessed using a patient diary, which was completed daily.

Outcomes
The primary outcome was clinical pregnancy rate, defined as the presence of an intrauterine gestational sac with an embryonic pole demonstrating cardiac activity at 7 weeks’ gestation. Secondary outcomes were defined a priori and included: cycle cancellation due to poor ovarian response; cycles reaching embryo transfer; ongoing pregnancy rate; biochemical pregnancy rate; number of cumulus-oocyte complexes retrieved; and number of metaphase II oocytes retrieved. We recorded live birth outcomes and maternal and neonatal outcomes. Adverse events and their severity were assessed at each visit; a Ferriman–Gallwey hirsutism score was completed prior to starting the study medication and on completion of the study medication. Serum total testosterone levels were measured at five time-points for each participant, including prior to starting the study medication and at the completion of the study medication but prior to commencing ovarian stimulation (Fig. 3). Testosterone was measured using the Roche Elecsys® electrochemiluminescence immunoassay on a Roche cobas® e411 Analyzer which has a coefficient of variation of 8.4% at a concentration of 0.33 nmol/L and of 3.2% at 2.40 nmol/L36.

Sample size calculation
Based on the results of earlier studies, the expected clinical pregnancy rate in the placebo group was estimated to be around 14.5%, and approximately twice this in the testosterone group10,14. Therefore, this superiority study was designed to have 80% power to detect an increase in clinical pregnancy rate from 14.5% in the placebo group to 26% in the testosterone group, with a two-sided α of 0.05. To achieve this, 190 participants were required for each group. Allowing for a dropout rate of 5%, the planned sample size was 200 participants per group.

Statistical analysis
All data was collected using standardized electronic case report forms in REDCap (Vanderbilt University).

Descriptive summary measures are expressed as mean (SD) or median (inter-quartile ranges) for continuous variables and frequencies (percentage) for categorical variables. The analysis and reporting of the results of the clinical outcomes follow the CONSORT guidelines (www.consort-statement.org).

An intention to treat approach was used for the primary analysis. For the primary outcome (clinical pregnancy rates) and the secondary clinical outcomes (ongoing pregnancy and biochemical pregnancy), results were analyzed using a two-sided chi-square test with a two-sided P value of less than 0.05 considered significant. A secondary per-protocol analysis was performed for the primary outcome among participants who adhered to the study protocol (i.e., excluding any withdrawn patients as per Fig. 1). Spontaneous pregnancies were included in the analysis.

Secondary outcomes were analyzed with the chi-square or Fisher exact tests if categorical (cycle cancellation due to poor ovarian response, cycles with embryo transfer, number of cycles with frozen supernumerary embryos) or with the independent Student’s t test or Mann–Whitney test if continuous (number of oocytes, number and quality of embryos and endocrine parameters). If a subject did not reach a certain stage in IVF treatment, zero values were imputed for the primary outcome (i.e. pregnancy outcomes were set to not pregnant). For other outcomes, missing values were not imputed. Results for the secondary outcomes, including the width of confidence intervals, were not adjusted for multiplicity.

Prespecified subgroup analyses were performed by age groups (<36, 36–39 and ≥40 years old). Analyses were performed with SPSS (Version 29.0.0.0, IBM Corporation) or R (Version 4.5.0, The R Foundation for Statistical Computing.) The study statisticians were blinded to group assignment.

A planned interim analysis of the primary outcomes was performed by an independent statistician once primary outcome data were available for 70% of the intended sample size, with the results reviewed by the DSMB. If the conditional power was ≥80% then we would continue with the planned sample size; if it was 40–80% the sample size would be increased to reach a conditional power of 80%; if the conditional power was 20–<40%, we would proceed with the planned sample size; if the conditional power was <20%, the study would be terminated for futility. This was included in the study design to prevent unnecessary continued recruitment and ongoing exposure of participants to an off-label medication in the event of futility. Trial statisticians were blinded to group allocation during the interim analysis.

The trial was prospectively registered at ClinicalTrials.gov (NCT02418572).

Peer review rounds
[{"round": 1, "reviewer_comments": {"reviewer_1": "Thank you for the thorough replies to my comments. I have no further comments on the manuscript.", "reviewer_2": "The authors performed a triple blinded, randomized clinical trial to determine if pretreatment with transdermal testosterone could improve clinical pregnancy rates in women with diminished ovarian reserve undergoing in vitro fertilization. The investigators have attempted to answer an important question in the field of reproductive endocrinology. Furthermore, the rigor of their study is impressive. The methodology could benefit from some clarifications. However, somewhat concerning is the way that the authors attempted to assess the efficacy of testosterone. The population of participants was broad. While a multicenter trial could enhance the applicability of the study, potential variations in laboratory quality and determination of the number of embryos to transfer, could add a significant amount of noise, when assessing efficacy.\n\nMajor\n1) Could the authors consider analyzing whether or not baseline antral follicle count changed? Could they also present the data on oocytes collected? They state that there wasn’t a difference but perhaps I missed seeing the mean/median and variation in the results section. In relation to my point below, it is possible that the impact of testosterone is more subtle – unlikely to double pregnancy rates in a single cycle. For women with DOR, they will likely need several cycles of IVF to see success, with or without an adjunct that can improve their odds of success. Since some studies suggest that supplemental testosterone may improve the follicular pool available for recruitment during ovarian stimulation, it would be helpful to see this data.\n2) The primary outcome of a double clinical pregnancy rate seems high. The authors hypothesize that the testosterone group would have a pregnancy rate twice that of the placebo (estimated to be 14.5%.) I recognize that they cite Kim et al who demonstrated a doubled pregnancy rate. However, subsequent studies do not suggest such a magnitude of impact and there are no other adjunct interventions for IVF that purport to have such an impact that believably double pregnancy rates. Therefore, the authors may consider reconciling that perhaps their hypothesized primary difference in pregnancy rates was too high and therefore they were underpowered to detect a more subtle difference. I will note, the authors do briefly address this on line 433 “. Smaller increases than this could still be considered clinically meaningful and there is a risk of type II error.” I do think that this is a significant enough issue, that the conclusion of their study should be tempered.\n3) In the methods section, it would be helpful to present the expected pregnancy rates for an ideal group (eg. Age <35) per study site. Readers should know at baseline that the clinics comparable. If there is significant noise introduced into pregnancy rates due to lab variability, that could obscure the results of the study\n4) In the methods section, the authors should provide a supplemental section on standard practice for the number of embryos to transfer per site – if it differed. This could introduce some noise if certain sites would only transfer a single day 3 embryo in an older population which is unlikely to be successful.\n5) In the results section, the authors state 4 of the 21 pregnancies in the testosterone group were twin pregnancies. If implantation (an intermediary outcome were considered), then there would be 25 pregnancies in the testosterone group and 23 in the placebo group. Furthermore, there were 3 spontaneous pregnancies in the placebo group and one in the testosterone group. With more granular data such as the number of embryos transferred, number of implantations and the ratio of the two, we might see that the testosterone group had either more embryos available to transfer and/or more implantations. Without more granular data, it is hard to discern. These data would be helpful intermediaries to present, particularly if the study is underpowered to detect differences in clinical or live birth rates (if we agree that a doubling of pregnancy rate is too high).\n\nMinor\nMethods\nIn the methods section, what defines recent for recent medical issues that would exclude patients\nThe authors describe 2 time points for testing testosterone, what were the other 3?\nHow were patients handled who had supernumerary embryos. I assume this is a small group, but it is important for readers to understand, were those patients able to contribute additional transfer cycles or was it solely first transfer", "reviewer_3": "Authors have answered most questions from reviewers in a satisfactory way. There are still some unclear parts, addressed below. It is particularly the ITT and the PP populations that are unclear.\n1.Flowchart (and text, line 284): 316 were assessed for eligibility-26 non eligible, 290 eligible. Among those eligible-did not any decline participation? Maybe some patients declined earlier in the process?? Can you clarify?\n2. Flowchart:2 patients were randomized but excluded in efficacy analysis-do you mean ITT analysis? , due to covid, and did not start IVF. Then re-randomized?? Why re-randomize and then exclude?? Was this a mistake at one unit? Randomize and exclude from ITT due to not starting treatment sounds to me as a FAS (full analys set) instead of an ITT and which is a common way of analysis. You then include in FAS all randomized patients having at least one outcome. Alternatively you need to explain how you did define ITT? All randomized?? (seems not to have been done), all randomized receiving at least one dose of study drug?? And what is the difference between these two patients and the 5+4 covid excluded from PP?\n3. Flow chart: 4+1 withdraw informed consent. Are you allowed to include these patients in the ITT? I mean to use their data if withdrawing informed consent? Did these patients start testosteron/placebo? IVF?\n4. Flow chart: 2+1 contraindication to treatment-did these patients start treatment? If not-what is the difference to the two covid patients excluded from ITT?\n5. Line 350. I earlier wrote that is not the DSMB that terminate a trial but the study group after advice from the DSMB. You have answered that this is correct but not changed the text.", "reviewer_4": "The authors have thoroughly answered my concerns. In particular I was unaware of the Mehta and Pocock paper, and thank the authors for bringing to my attention. This is an interesting paper, albeit not without controversy. I am surprised that the authors referenced the JAMA paper (Ref 30 Saville et al.) rather than the Mehta and Pocock paper if this earlier paper was indeed the basis of their calculation. In addition the Mehta and Pocock paper has an excellent commentary by Scott Emerson et al. accompanying the article. These are important tools for statisticians to think about when designing trials.\nI ask the authors to consider adding the Mehta and Pocock paper, or if there are publisher constraints on length, replacing Saville et al. paper with Mehta and Pocock.\nI do not see a supplement but including the table with the sample size of each of the centers in a supplement would be helpful for others in the field thinking about how to generalize the results of this study."}, "author_response": "Response: Thank you for the positive feedback, and for the comment regarding the multicenter nature of the trial. Acknowledging the potential for variation between sites, the randomised nature of the trial and the approach to randomisation (block randomisation with stratification by study site and age) aimed to ensure balanced groups across site, reducing the impact of any site-to-site variation. In response to this, and the feedback from Reviewer #4, we have included a supplemental table with data on the number of participants at each site.\nMajor\n1) Could the authors consider analyzing whether or not baseline antral follicle count changed? Could they also present the data on oocytes collected? They state that there wasn’t a difference but perhaps I missed seeing the mean/median and variation in the results section. In relation to my point below, it is possible that the impact of testosterone is more subtle – unlikely to double pregnancy rates in a single cycle. For women with DOR, they will likely need several cycles of IVF to see success, with or without an adjunct that can improve their odds of success. Since some studies suggest that supplemental testosterone may improve the follicular pool available for recruitment during ovarian stimulation, it would be helpful to see this data.\nResponse: Thank you for this comment. Table 4 describes the outcomes of ovarian stimulation, including the number of oocytes retrieved, the number of MII oocytes retrieved, and the subsequent embryological outcomes. This provides additional granularity of data to consider the questions raised by the reviewer with regard to more subtle changes that might be observed.\nWe analyzed the AFC as suggested by the reviewer and no difference was observed. This has been included as a sentence in the third paragraph of the results section.\n2) The primary outcome of a double clinical pregnancy rate seems high. The authors hypothesize that the testosterone group would have a pregnancy rate twice that of the placebo (estimated to be 14.5%.) I recognize that they cite Kim et al who demonstrated a doubled pregnancy rate. However, subsequent studies do not suggest such a magnitude of impact and there are no other adjunct interventions for IVF that purport to have such an impact that believably double pregnancy rates. Therefore, the authors may consider reconciling that perhaps their hypothesized primary difference in pregnancy rates was too high and therefore they were underpowered to detect a more subtle difference. I will note, the authors do briefly address this on line 433 “. Smaller increases than this could still be considered clinically meaningful and there is a risk of type II error.” I do think that this is a significant enough issue, that the conclusion of their study should be tempered.\nResponse: Thank you for this feedback. We acknowledge that the study was underpowered to detect a smaller difference. The doubling in pregnancy rates was not only reporting in the Kim trial, which was used to make the sample size calculation, but also in the most meta-analysis which reported a RR of 2.07 in pregnancy rates in favour of the testosterone (Neves et al. 2022). However, we acknowledge the comment of the reviewer which is very reasonable and have altered the conclusion to address this.\n3) In the methods section, it would be helpful to present the expected pregnancy rates for an ideal group (eg. Age <35) per study site. Readers should know at baseline that the clinics comparable. If there is significant noise introduced into pregnancy rates due to lab variability, that could obscure the results of the study\nResponse: Thank you for this feedback. Given the study was randomised with stratification by study site and balanced groups at each site, we would expect this to mitigate the impact of clinic-level success rates given that all participants at each site were treated the same at that site. Overall, we would therefore expect any negative or positive effect of each site to be equal across both groups. These data (individual clinic outcomes for good prognosis patients) are not typically reported as part of a study manuscript. We do acknowledge the feedback of the reviewer, and emphasise that all clinics included are highly respected units in Europe with excellent pregnancy rates as reported to their national registries. The study group was, by design, a poor prognosis group, resulting in low pregnancy rates, and several centres only recruited a small number of patients, and therefore per-clinic results are unlikely to be informative or meaningful.\n4) In the methods section, the authors should provide a supplemental section on standard practice for the number of embryos to transfer per site – if it differed. This could introduce some noise if certain sites would only transfer a single day 3 embryo in an older population which is unlikely to be successful.\nResponse: Thank you for this comment. Table 4 describes the number of embryos transferred per patient, with no difference between groups. On average, 1.1 embryos were transferred per patient, with fewer than 10% of patients having supernumerary embryos available for transfer (also included in Table 4), suggesting that the majority of patients had all available embryos transferred. Additionally, given the randomised nature of the study, we would expect patients in each group at each site to be treated the same, mitigating the impact of site-to-site variability in practice. We have included the data for each site in the table below, however due to the small numbers in several sites (see new table regarding the number at each site) we do not believe that this data would contribute meaningfully to the manuscript.\n[Table omitted for brevity]\n5) In the results section, the authors state 4 of the 21 pregnancies in the testosterone group were twin pregnancies. If implantation (an intermediary outcome were considered), then there would be 25 pregnancies in the testosterone group and 23 in the placebo group. Furthermore, there were 3 spontaneous pregnancies in the placebo group and one in the testosterone group. With more granular data such as the number of embryos transferred, number of implantations and the ratio of the two, we might see that the testosterone group had either more embryos available to transfer and/or more implantations. Without more granular data, it is hard to discern. These data would be helpful intermediaries to present, particularly if the study is underpowered to detect differences in clinical or live birth rates (if we agree that a doubling of pregnancy rate is too high).\nResponse: Thank you for this feedback. We reported outcomes per patient treating each pregnancy as a single event regardless of plurality, as that is the suggested approach in the COMMIT guidelines on reporting outcomes in clinical trials in reproductive medicine, however we acknowledge that the implantation rate may be of interest to readers. We note that the number of embryos transferred is described in Table 4 and did not differ between groups.\nIn response to this question, we have included the implantation rate per embryo transferred below. This excludes the spontaneous pregnancies, hence the total numbers of 24 and 20, rather than 25 and 23.\nTestosterone: 26.4% (24/91)\nPlacebo: 17.1% (20/117)\nRR: 1.54 (0.91 to 2.61), p = 0.10\nWhilst the implantation rate is provided here for the reviewer, we have not included it in the manuscript as it was not a predefined outcome and is not included in the COMMIT guidelines on outcome reporting in reproductive medicine trials. We will leave it to the discretion of the editor as to whether this data should be included in the paper or not.\nMinor\nMethods\nIn the methods section, what defines recent for recent medical issues that would exclude patients\nThe authors describe 2 time points for testing testosterone, what were the other 3?\nHow were patients handled who had supernumerary embryos. I assume this is a small group, but it is important for readers to understand, were those patients able to contribute additional transfer cycles or was it solely first transfer\nResponse: Thank you for the comments. Recent medical issues were defined as any medical condition that the site investigator considered to indicate that the patient was not suitable to commence a cycle of IVF at the moment of inclusion (prior to randomisation).\nRegarding the time points for testing testosterone levels, the other time points are seen in Figure 3, along with the levels at each time point. A reference to Figure 3 has been added in the text at the relevant point. Specifically, it was measured at: Visit 2: Day of starting treatment with testosterone or placebo (day 1 of menstrual cycle); Visit 3: Day 1 of the subsequent menstrual cycle; Visit 4: Day 21 of the subsequent menstrual cycle; Visit 5: Final day of treatment with testosterone or placebo and day of starting ovarian stimulation; Visit 10: day of oocyte collection.\nRegarding supernumerary embryos, as outlined in Table 4 there were 16 participants in the testosterone group with supernumerary embryos (11.9%) and 11 participants in the placebo group (7.1%). The outcomes were reported based on the first transfer.\nReviewer #3 (Remarks to the Author):\nAuthors have answered most questions from reviewers in a satisfactory way. There are still some unclear parts, addressed below. It is particularly the ITT and the PP populations that are unclear.\n1.Flowchart (and text, line 284): 316 were assessed for eligibility-26 non eligible, 290 eligible. Among those eligible-did not any decline participation? Maybe some patients declined earlier in the process?? Can you clarify?\nResponse: Thank you for the question. A total of 316 were assessed for eligibility, of whom 26 were not eligible and 290 were eligible. Of those who were eligible, none declined participation and all 290 were randomised and initiated treatment.\n2. Flowchart:2 patients were randomized but excluded in efficacy analysis-do you mean ITT analysis? , due to covid, and did not start IVF. Then re-randomized?? Why re-randomize and then exclude?? Was this a mistake at one unit? Randomize and exclude from ITT due to not starting treatment sounds to me as a FAS (full analys set) instead of an ITT and which is a common way of analysis. You then include in FAS all randomized patients having at least one outcome. Alternatively you need to explain how you did define ITT? All randomized?? (seems not to have been done), all randomized receiving at least one dose of study drug?? And what is the difference between these two patients and the 5+4 covid excluded from PP?\nResponse: Thank you for this question. These two patients were randomised and initiated treatment with the study drug (in this case testosterone), however a lockdown was then declared by the Spanish government and their treatments were halted. These two patients were then re-randomised at a later date and entered the study again (after a ≥3 month washout period in order to fulfil the study inclusion criteria). As they were randomised twice, only the second randomisation is included in the analysis to avoid multiple observations of the same patients. The other patients who were included in the ITT analysis but who had COVID were different to these two in that they contracted COVID at a later date and therefore their cycles were not cancelled by the Government decree, and they continued with treatment. They were considered a protocol violation due to the comorbid conditions (COVID).\n3. Flow chart: 4+1 withdraw informed consent. Are you allowed to include these patients in the ITT? I mean to use their data if withdrawing informed consent? Did these patients start testosteron/placebo? IVF?\nThese 5 patients were randomised and started treatment, however they later decided to withdraw from the study. Although they withdrew consent to participate, they provided consent for their data up until that point to be used.\n4. Flow chart: 2+1 contraindication to treatment-did these patients start treatment? If not-what is the difference to the two covid patients excluded from ITT?\nResponse: Yes, these patients did start treatment before later being excluded when the contraindication was identified.\n5. Line 350. I earlier wrote that is not the DSMB that terminate a trial but the study group after advice from the DSMB. You have answered that this is correct but not changed the text.\nResponse: Thank you for identifying this – we have changed the text to “Based on these results and as per the study protocol, the study group terminated the trial on advice of the DSMB.”\nReviewer #4 (Remarks to the Author):\nThe authors have thoroughly answered my concerns. In particular I was unaware of the Mehta and Pocock paper, and thank the authors for bringing to my attention. This is an interesting paper, albeit not without controversy. I am surprised that the authors referenced the JAMA paper (Ref 30 Saville et al.) rather than the Mehta and Pocock paper if this earlier paper was indeed the basis of their calculation. In addition the Mehta and Pocock paper has an excellent commentary by Scott Emerson et al. accompanying the article. These are important tools for statisticians to think about when designing trials.\nI ask the authors to consider adding the Mehta and Pocock paper, or if there are publisher constraints on length, replacing Saville et al. paper with Mehta and Pocock.\nI do not see a supplement but including the table with the sample size of each of the centers in a supplement would be helpful for others in the field thinking about how to generalize the results of this study.\nResponse: We have cited the Mehta and Pocock paper as suggested, in addition to the Saville paper.\nSupplemental table will be added as requested:\n[Table omitted for brevity]"}, {"round": 2, "reviewer_comments": {"reviewer_3": "Thank you. Authors have answered my comments satisfactory. I think the authors have answered all comments in a satisfactory and very balanced way, and made revisions in the ms according to ref 2.\nI have no further comments. In my view, this paper can be accepted for publication."}, "author_response": ""}]

Decision letter