Firstly, in this response to the earlier comments of Deborah L. Lokken and Beverley H. Johnson of February 24, 2023, we agree that patient participation in patient safety is of huge importance. Sorry that we may be gave you the wrong impression and we would like to apologize for this. We see it as a positive development towards a true partnership in healthcare between patient and professional, however, there can be also concerns or risks if patients participate. We therefore also need the negative effects of patient participation in patient safety to take the next step in the development of patient participation.

To take the next step in the contribution of patients and their families to patient safety, it is important to examine the full context and see which ‘gaps’ need to be addressed. Even if focusing only on negative effects could lead to a bias, identifying these gaps will us learn which ones there are and therefore also what we need to work on in order to make that positive contribution of patients in patient safety. For that reason, we have also indicated as a recommendation from this study that it is necessary to find the measures that need to be taken to either prevent these negative effects or address them ad hoc as soon as they occur.

We can understand that the authors have some questions about the initiatives mentioned or about the small sample size. We have included the small sample size as a limitation. However, as also described in our published article, we only reached these conclusion by reaching saturation. The examples of initiatives cited in the research such as the participation in medication safety that you are refer to, are not new initiatives but rather demonstrated initiatives of patient participation in patient safety within an Obstetrics department. In this study, it was decided to offer a new insight based on the respondents from the professional- and patient side. We recognize that in the future it may be interesting to also include the families of pregnant woman in the study, to see and investigate what findings emerge.

Axel Skafte-Holm 1, Thomas Roland Pedersen 1 and Jørgen Skov Jensen 1*
1 Department of Bacteria, Parasites and Fungi, Research Unit for Reproductive Microbiology, Statens Serum Institut, Copenhagen, Denmark

*Corresponding author
Jørgen Skov Jensen
Consultant physician, MD, PhD, DMedSci.
Statens Serum Institute
5 Artillerivej
DK-2300 Copenhagen S
Denmark
Research Unit for Reproductive Microbiology.
Division of Diagnostic Infectious Disease Preparedness
Telephone +45 3268 3636
jsj@ssi.dk

To the Editor,

We read with interest the systematic review and meta-analysis by Jonduo et al. [1], investigating the association between Mycoplasma (M.) hominis, Ureaplasma (U.) urealyticum and U. parvum colonisation of the genital tract of pregnant women and adverse pregnancy outcomes. This is a highly relevant analysis, as this subject is a matter of ongoing debate, due to the complex interactions with other microbial and non-microbial factors. It is also a subject where enormous taxonomic confusion exists due to the re-classification of the ureaplasmas. We were, consequently, interested in the comprehensive analysis on the relative importance of the two Ureaplasma spp. Unfortunately, we detected some shortcomings, which need to be discussed.
(I) Culture-based studies. The review excluded articles published before the year 2000 if unspeciated U. urealyticum were reported alone, as Ureaplasma spp. detected by culture previously were reported as U. urealyticum. In this matter, it is surprising that seven of the included articles [2-8] on U. urealyticum were culture-based. Although bacteriological culture is considered the gold standard it only identifies bacteria at the genus level, preventing differentiation between U. urealyticum (formerly biovar 2, T980, T960T or A) and U. parvum (formerly biovar 1, parvo or B). In the review, all results from culture-based articles were reported as U. urealyticum, probably because primary authors wrongly reported cultured ureaplasmas as U. urealyticum. Unless additional typing of isolates is performed, cultures should always be reported as Ureaplasma spp.
(II) Confusion on nomenclature. Harada et al. determined the biovar of colonies using PCR-based typing where they reported all U. urealyticum (i.e. Ureaplasma spp.) colonies as biovar type 1 i.e. U. parvum among 23 women experiencing preterm birth, but the systematic review reported findings as U. urealyticum [9]. Two other articles [10, 11] reported on biovar 1 and biovar 2, but were cited only as U. urealyticum and the review failed to include these results in the U. parvum analysis.
(III) Shortcomings in methodology. Most articles were based on real-time PCR and two articles [12, 13] used multiplex PCR to identify sexually transmitted infections. Some articles used conventional PCR, but one [14] failed to report information on PCR method and consequently evaluation of the species differentiation was not possible. In order to evaluate primers and probes in the studies included in the meta-analysis, we aligned sequences and queried them using the Basic Local Alignment Search Tool (BLAST) [15] against U. urealyticum serovar 8 (NCBI Reference Sequence: NZ_AAYN02000002.1) and U. parvum serovar 3 (NCBI Reference Sequence: NC_002162.1). Most studies correctly distinguished ureaplasmas at the species level. Unfortunately, we found methodological shortcomings in one paper [16], as primer/probe design did not allow discrimination of Ureaplasma spp. Two studies [17, 18] reported U. urealyticum, but alignment results indicated that the primers were 100% specific for U. parvum and contained several mismatches with the U. urealyticum sequence, thus, at best detecting Ureaplasma spp.
In general, Mollicutes are complicated pathogens and our assessment of the literature demonstrates a laissez-faire approach to nomenclature and methods applied. The diagnostic methodologies applied should be carefully evaluated when assessing studies to allow conclusions about the relation between Ureaplasma spp. and clinical outcomes. The taxonomic and methodological confusion in the literature is concerning, so an in-depth analysis of the area is warranted and we suggest that the review authors update their analysis of associations between the two Ureaplasma spp. and adverse pregnancy outcomes. The review conclusions may not change because the majority of the studies suffered from lack of control for major confounding factors, but at least the combined effect estimates will be more correct.

References

1. Jonduo ME, Vallely LM, Wand H, Sweeney EL, Egli-Gany D, Kaldor J, et al. Adverse pregnancy and birth outcomes associated with Mycoplasma hominis, Ureaplasma urealyticum and Ureaplasma parvum: a systematic review and meta-analysis. BMJ Open. 2022;12(8):e062990. DOI: 10.1136/bmjopen-2022-062990.
2. Lee MY, Kim MH, Lee WI, Kang SY, Jeon YL. Prevalence and Antibiotic Susceptibility of Mycoplasma hominis and Ureaplasma urealyticum in Pregnant Women. Yonsei Med J. 2016;57(5):1271-5. DOI: 10.3349/ymj.2016.57.5.1271.
3. Daskalakis G, Thomakos N, Papapanagiotou A, Papantoniou N, Mesogitis S, Antsaklis A. Amniotic fluid interleukin-18 at mid-trimester genetic amniocentesis: relationship to intraamniotic microbial invasion and preterm delivery. Bjog. 2009;116(13):1743-8. DOI: 10.1111/j.1471-0528.2009.02364.x.
4. Usui R, Ohkuchi A, Matsubara S, Izumi A, Watanabe T, Suzuki M, et al. Vaginal lactobacilli and preterm birth. J Perinat Med. 2002;30(6):458-66. DOI: 10.1515/jpm.2002.072.
5. Kwak DW, Hwang HS, Kwon JY, Park YW, Kim YH. Co-infection with vaginal Ureaplasma urealyticum and Mycoplasma hominis increases adverse pregnancy outcomes in patients with preterm labor or preterm premature rupture of membranes. J Matern Fetal Neonatal Med. 2014;27(4):333-7. DOI: 10.3109/14767058.2013.818124.
6. Kafetzis DA, Skevaki CL, Skouteri V, Gavrili S, Peppa K, Kostalos C, et al. Maternal genital colonization with Ureaplasma urealyticum promotes preterm delivery: association of the respiratory colonization of premature infants with chronic lung disease and increased mortality. Clin Infect Dis. 2004;39(8):1113-22. DOI: 10.1086/424505.
7. Abele-Horn M, Scholz M, Wolff C, Kolben M. High-density vaginal Ureaplasma urealyticum colonization as a risk factor for chorioamnionitis and preterm delivery. Acta Obstet Gynecol Scand. 2000;79(11):973-8. DOI.
8. Kacerovský M, Pavlovský M, Tosner J. Preterm premature rupture of the membranes and genital mycoplasmas. Acta Medica (Hradec Kralove). 2009;52(3):117-20. DOI: 10.14712/18059694.2016.115.
9. Harada K, Tanaka H, Komori S, Tsuji Y, Nagata K, Tsutsui H, et al. Vaginal infection with Ureaplasma urealyticum accounts for preterm delivery via induction of inflammatory responses. Microbiol Immunol. 2008;52(6):297-304. DOI: 10.1111/j.1348-0421.2008.00039.x.
10. Mitsunari M, Yoshida S, Deura I, Horie S, Tsukihara S, Harada T, et al. Cervical Ureaplasma urealyticum colonization might be associated with increased incidence of preterm delivery in pregnant women without prophlogistic microorganisms on routine examination. J Obstet Gynaecol Res. 2005;31(1):16-21. DOI: 10.1111/j.1447-0756.2005.00246.x.
11. Povlsen K, Thorsen P, Lind I. Relationship of Ureaplasma urealyticum biovars to the presence or absence of bacterial vaginosis in pregnant women and to the time of delivery. Eur J Clin Microbiol Infect Dis. 2001;20(1):65-7. DOI: 10.1007/pl00011237.
12. Koucký M, Malíčková K, Cindrová-Davies T, Smíšek J, Vráblíková H, Černý A, et al. Prolonged progesterone administration is associated with less frequent cervicovaginal colonization by Ureaplasma urealyticum during pregnancy - Results of a pilot study. J Reprod Immunol. 2016;116:35-41. DOI: 10.1016/j.jri.2016.04.285.
13. Peretz A, Tameri O, Azrad M, Barak S, Perlitz Y, Dahoud WA, et al. Mycoplasma and Ureaplasma carriage in pregnant women: the prevalence of transmission from mother to newborn. BMC Pregnancy Childbirth. 2020;20(1):456. DOI: 10.1186/s12884-020-03147-9.
14. Schwab FD, Zettler EK, Moh A, Schötzau A, Gross U, Günthert AR. Predictive factors for preterm delivery under rural conditions in post-tsunami Banda Aceh. J Perinat Med. 2016;44(5):511-5. DOI: 10.1515/jpm-2015-0004.
15. Zhang Z, Schwartz S, Wagner L, Miller W. A greedy algorithm for aligning DNA sequences. J Comput Biol. 2000;7(1-2):203-14. DOI: 10.1089/10665270050081478.
16. Aaltone R, Jalava J, Laurikainen E, Kärkkäinen U, Alanen A. Cervical ureaplasma urealyticum colonization: comparison of PCR and culture for its detection and association with preterm birth. Scand J Infect Dis. 2002;34(1):35-40. DOI: 10.1080/00365540110077074.
17. Montenegro DA, Borda LF, Neuta Y, Gómez LA, Castillo DM, Loyo D, et al. Oral and uro-vaginal intra-amniotic infection in women with preterm delivery: A case-control study. J Investig Clin Dent. 2019;10(2):e12396. DOI: 10.1111/jicd.12396.
18. Nasution TA, Cheong SF, Lim CT, Leong EW, Ngeow YF. Multiplex PCR for the detection of urogenital pathogens in mothers and newborns. Malays J Pathol. 2007;29(1):19-24. DOI.

Dear Editor,

To Prof Forrest and the authors of the Chaudhary et al paper(1): Thank you for your response to our review(2) in which you highlight that there was a significant reduction in alcohol-related liver disease (ALD) discharges following the introduction of minimum unit pricing (MUP) at your unit. This is an important point to highlight as a misrepresentation of the Chaudhary et al study in our review.

In our review, we reported the outcome measure of mean weekly ALD discharges before and after MUP for 'All hospital episodes' which did not reach pre-defined significance (6.2 versus 5.2; p = 0.123) in the Chaudhary et al study, however the outcomes for 'individual patients' and those 'actively drinking' did indeed reach pre-defined significance and should have been included in our review. These outcomes from the Chaudhary et al study would certainly be consistent with the overall conclusion of our review, adding further support to the impact of MUP reducing alcohol-related hospital burden as you have highlighted.

We would also like to correct the reference to your study in the main text of our review which should read “Chaudhary et al” and not “Ferguson et al” (found under ‘Results’, subheading ‘Natural experiments’).

References
1. Chaudhary S, MacKey W, Duncan K, Forrest EH. Changes in Hospital Discharges with Alcohol-Related Liver Disease in a Gastroenterology and General Medical Unit Following the Introduction of Minimum Unit Pricing of Alcohol: The GRI Q4 Study. Alcohol and Alcoholism 2022; 57(4): 477–482.
2. Maharaj T, Angus C, Fitzgerald N, et al. Impact of minimum unit pricing on alcohol-related hospital outcomes: systematic review. BMJ Open 2023; 13: e065220. doi: 10.1136/bmjopen-2022-065220

Dear Editor,
The article by Yang et al. (2022) is fundamentally flawed due to a number of serious methodological shortcomings. These deficits are of such crucial relevance that it is in our view highly doubtful whether the conclusions the authors draw from their research are valid.

1) Data extraction is not transparent and sometimes false:
We were not able to replicate any of the values included in the main analysis of pain (Figure 4). In at least one study, values were extracted from the wrong group. In two further studies, the given values are incompatible with the values reported in the study. In at least three studies, sample sizes were falsely extracted.
Specifically:
Only in one of the included studies (Bishop et al., 2016) the values given in Figure 4 (Mean, SD) were found (Table 6, Bishop et al., 2016). However, the values of the control group were extracted from the false group (see below). For all other included studies, the values (Mean, SD) given in Figure 4 were not found. We were not able to find a description of how the authors may have transformed the values to explain the disagreement. In some studies, the given values in Figure 4 are not only not replicable but are incompatible with the values reported in the studies:
o In Bishop et al. (2016), values were extracted from the false group. Values were taken from standard care group but Yang et al. stated in Table 1 to have used the placebo acupuncture group as control group. The placebo acupuncture group actually had better pain scores than the experimental group. This is the opposite effect of what is used in Figure 4.
o Elden et al. (2005) reported morning and evening pain values post treatment in three groups. For all three groups and both measures (morning, evening), Elden et al. (2005) reported different medians. However, in Figure 4, equal means are given for experimental and control group for Elden et al. (2008) (which is a follow-up publication of the same study as Elden et al., 2005; see below).
o Lund et al. (2006) compared deep and superficial acupuncture. They did not report mean values but concluded that, regarding pain levels, "according to our study, there is not enough evidence of different treatment effects between the two stimulation modes of acupuncture". However, in Figure 4, the effect estimate presented for Lund et al. (2006) strongly favors the experimental group und the confidence interval does not include 0.
o In at least three studies, the extracted sample sizes were too large. Here, Yang et al. seemed to have used the number of participants that were included in the beginning of the study but failed to recognize that the analysis was done for a smaller number of patients. In the following, actual and falsely reported numbers are given for the groups Yang et al. presented in Table 1 (experimental group / control group): Bishop et al. (2016) reported 32 / 27, Yang et al. used 42 / 41; Ekdahl and Petersson (2010) reported 16 / 16, Yang et al. used 20 / 20; Elden et al. (2005) reported 107 / 108, Yang et al. used 130 / 125.

2) The same study is included twice:
Yang et al. included two publications of the same study (Elden et al., 2008; Elden et al., 2005) and presented them as two different studies in Table 1 and throughout the manuscript. Elden et al. (2005) reported pain endpoints whereas Elden et al. (2008) did not report values of pain. In contrast to that, in Figure 4, pain values are assigned to Elden et al. (2008).

3) The choices of the comparator group are not comprehensible:
Five of the nine included studies analyzed more than two groups (e.g. true acupuncture, placebo acupuncture, and standard care). Yang et al. did not give reasons for their choices of which group is used as control group. When three- or four-armed studies included both a placebo acupuncture group and a standard care group, Yang et al. sometimes chose the placebo acupuncture group as control (Bishop et al., 2016) and sometimes the standard care group (Jorge et al., 2019; Wang et al., 2009). One study (Ekdahl and Petersson, 2010) compared two acupuncture groups where the intervention was equal but began at different gestational weeks. It is not transparent why one of the groups was chosen as experimental group and the other one as control group.

3) Effects were pooled and interpreted as significant results with staggering heterogeneity and scarcity of data:
Despite the major heterogeneity observed, studies were pooled and effects were presented as statistically significant. This is contrary to the Cochrane recommendations for dealing with large heterogeneity (Cochrane Handbook Section 10.10.3 “Strategies for addressing heterogeneity” (https://training.cochrane.org/handbook/current/chapter-10#section-10-10-3): “1. Check again that the data are correct / 2. Do not do a meta-analysis”)

4) Choice between fixed-effect-model and random-effects-model was done in hindsight:
The authors stated “If p<0.1 or I**2 >50% we combined results using a random-effect model (29).” This is considered as bad practice, see, e.g. Borenstein et al. (2010) (https://doi.org/10.1002/jrsm.12): “In some circles, researchers tend to start with the fixed-effect model, and then switch to the random-effects model if there is a compelling reason to do so. Usually, this means that the test for heterogeneity across studies is statistically significant. This is a bad idea for many reasons.”
Furthermore, the cited reference (29) gives no justification for the applied approach.

In addition to the above points, some further issues came to our attention:
Figure 6 is falsely labelled. The left side of the forest plot should favor experimental.
The choice of the pain endpoint is not transparent: The included studies collected multiple different measures of VAS-pain. Two studies (Wedenberg et al., 2000; Elden et al., 2005) collected morning and evening values. One study (Kvorning et al., 2004) collected minimal and maximal pain. Yang et al. did not describe or explain which values they used.

In summary, due to its serious weaknesses in conduct, methods, and reporting, the article by Yang et al. does in our view not contribute to clarify the value of acupuncture for low back and/or pelvic pain during pregnancy but is misleading and thus does a disservice to physicians and patients.