The study by Brandt et al. (A flexible pipeline combining bioinformatic correction tools for prokaryotic and eukaryotic metabarcoding) brings new insights into data analysis of metabarcoding datasets covering both prokaryotes and eukaryotes as well as mitochondrial (e.g. COI) and nuclear genes (e.g. 18S and 16S), particularly with the inclusion and testing of new methods/bioinformatic tools (e.g. DADA2 and LULU). It is an interesting and well-written paper, likely to be very useful to many biologists/ecologists dealing with these types of datasets. The reviewer has done minor comments/changes in the pdf file (see attachment). Additionally, the authors should consider the following major points:

• Expected relative abundance: multi copy nature of rRNA genes, PCR bias, etc., might confound our expectations. How close is it good enough?
• Intragenomic/intraspecific polymorphism: is this a real problem? Can we alleviate by using phylogenetic methods?
• General trend/patterns: although the different methods produced different results (e.g. alpha/beta diversity), how strongly did they impact the overall pattern?
• In the pipeline, what seems to be the crucial step (e.g. clustering methods/thresholds or taxonomic assignment) in order to produce realible/accurate findings with respect to biodiversity and ecological patterns?

Finally, the reviewer recommends the preprint to be published after minor revisions.

Brandt et al., present a study on bioinformatic processing of metabarcoding data that implements two currently wide applied tools (DADA2 and Swarm) in combination with a post-clustering tool (LULU). By proposing to combine DADA2 and Swarm, their study allows another perspective on the debate whether ASVs or OTUs should be used for metabarcoding datasets. However, this combination (and the further post-clustering process with LULU) opens up some major issues, which have to be addressed before I see this manuscript ready for publication. Especially the choice of some parameters is not justified properly. I will focus in my review on these major issues.

That being said, large parts of the manuscript read very well and there are few corrections needed on the language. My review of the language will therefore be very short and does not include typos (but there are some!). I would suggest, though, to re-structure the order of some paragraphs, which might improve the reading experience of the manuscript even further.

Major concerns:
i) The authors present their study -and especially the implementation of LULU- as a novel approach for studying metazoan diversity. However, a quick literature search returned another study from 2018 by Stefanni et al., that also targeted the COI and 18S gene for analyzing metazoan metabarcoding data with LULU (Stefanni et al., 2018; Multi-marker metabarcoding approach to study mesozooplankton at basin scale. Scientific Reports 8:12085). Stefanni et al., made some different choices regarding their bioinformatic pipeline, but their work and results should at least be discussed in the context of the current manuscript here. In general, I have some doubts regarding the extent of novelty presented by Brandt and colleagues. Using LULU in combination with DADA2 was originally tested by Frøslev et al., 2017 on plant data. I am not convinced that simply applying the same combination on metazoan, eukaryotic and prokaryotic data is enough for a study that proposes a ‘flexible pipeline combining bioinformatic correction tools’, because neither tool was developed by the authors, nor is said combination a novel idea of the authors. Maybe the authors refer to the combination of DADA2 and Swarm for being the proposed novel flexible pipeline. If that is what they are aiming at, they may want to consider putting the combination of DADA2 and Swarm (and LULU) in the focus. Momentarily it reads as the focus is on DADA2 and LULU.

ii) Several parameters were chosen in the bioinformatic pipeline that are currently not justified in the text. The most prominent example is Swarm’s d value, which is set to 4 for 18S data, 6 for COI data and 1 for 16S data (lines 261-262). I am aware of only few studies that do not use Swarm’s default of d=1, most likely because the results become harder to interpret. Allowing a difference of one nucleotide between two sequences in one OTU can easily be justified by naturally occurring sequence variation or artificially introduced sequencing errors. Every value beyond d=1 is harder to justify and may be just as arbitrary as the clustering thresholds the authors try to avoid. In fact, I was surprised that the authors use the avoidance of arbitrary sequence similarity clustering thresholds as an argument for Swarm (lines 54-55 and 113-115), but then try to set d to a value that mimics a 1% sequence divergence threshold, which is just the invers of a 99% sequence similarity threshold (lines 349-351). The situation gets even worse, because Swarm OTUs clustered with a different d value are pooled and analyzed in the same context. In my opinion, OTUs that are analyzed together should always be treated as similar as possible. I suppose the size of the 18S V1/V2 region is nearly as long as the 16S V4/V5 region; why were then so different thresholds chosen for the clustering of the respective OTUs? The authors need to justify these decisions and if they cannot come up with scientifically sound justifications, they should consider sticking to those values that are justifiable.
Other more or less arbitrary values for which I found no explanation or justification were the maximum error rate for primer removal in CUTADAPT (lines 231-232), the truncation length, maximum expected error rates (line 243) as well as the minimum overlap for paired-end assembly (line 247) in DADA2, the very low identity (70%) cutoff for BLAST (line 254) and the minimum match values for LULU (line 280). All of these parameters have a severe effect on downstream data processing and ultimately on the results. Maybe the authors chose the values for a good reason or they followed default values from the literature. But without further explanations, the readers cannot understand their decisions and I would not recommend using a bioinformatic pipeline that does not inform about such important steps.

iii) In abstract and introduction, the authors make a point about the importance of multiple marker metabarcoding approaches. However, they conclude that DADA2 is not fit for analyzing metabarcoding datasets of metazoan organisms (lines 504-507). In contrast to this finding, there are at least two publications that analyzed metazoan metabarcoding datasets with DADA2 and did not report the problems presented by the authors here. One of the publications used the 18S V4 marker region and was cited by the authors (Xiong & Zhan 2018), the other publication used the 18S V9 marker region and was not cited by the authors (Leff et al., 2018; Predicting the structure of soil communities from plant community taxonomy, phylogeny, and traits. ISME Journal 12:1794-1805). These studies show that i) the conclusions about metazoan metabarcoding data drawn by the authors on base of the COI region cannot be generalized to all gene regions and ii) the authors may have targeted a less suited gene region for their approach. In any case the results of the current study should be discussed in the context of these previous studies.
Although I admit that it is a tedious topic, I was also surprised about the author’s choice of the 18S V1/V2 region instead of the more commonly used V4 or V9 region. Can the authors please comment on why V1/V2 was chosen? Much more reference data seems to be available for V4 and V9. Since correct taxonomic assignments were an important topic in the current study, using a marker gene for which more reference data is available would have been beneficial for the authors’ study design.

Minor comments:
- Two sentences I struggled the most with:
‘As metabarcoding with multiple markers, spanning several branches of the tree of life is becoming more accessible, bioinformatic pipelines need to accommodate both micro- and macro biologists.’ (lines 2-4).
‘The results also confirm an important variation in the amplification success across taxa (Bhadury et al., 2006; Carugati, Corinaldesi, Dell’Anno, & Danovaro, 2015), supporting the present approach combining nuclear and mitochondrial markers to achieve more comprehensive biodiversity inventories (Cowart et al., 2015; Drummond et al., 2015; Zhan, Bailey, Heath, & Macisaac, 2014).’ (lines 542-546).
Could you please rephrase to make it clearer to the reader what you want to express?

• The numbering of the manuscript sections is askew. Introduction should be ‘1’, but Methods ended up being ‘1’ and so on.
• Reference style is not uniform. For instance: ‘Bista et al., 2015‘ next to ‘Deiner, Fronhofer, Mächler, Walser, & Altermatt, 2016‘ (line 36).
• Singletons consist of only one read. If the OTU consists of two reads, it is a doubleton (line 68). By the way, DADA2 is very effective in removing singletons (see Callahan et al., 2016). Thus, if you think that singleton removal ‘…is arbitrary and potentially hinders the detection of rare species.’ you should not use DADA2.
• Though different important topics are mentioned in the introduction it is not getting absolutely clear what the authors aim to achieve and how they want to do it. Especially the late mentioning of Swarm and how this algorithm will be connected to what had been said before is confusing.
• What do the authors mean by amplicons obtained from negative controls (lines 317-318)? They cannot possibly refer to negative controls of the PCR that yielded amplicons? I am sure there must be another explanation, but could not find it in the manuscript’s methods section. There is just the cryptic sentence ‘Negative extraction controls were included in each extraction run.’ (line 152). Could you please explain what exactly these controls are, what you used them for and why they had been pooled with the rest of the amplicons?
• Do more abundant species in the mock communities lead to more ASVs/OTUs?
• Table 1: Maybe the comparison of the pipelines’ results could also be presented as a figure. All these numbers separated by a slash are hard to read and may look more impressive e.g. in barplots.
• Table 2: Could also be a ‘real’ colored heatmap.
• I struggled with the order of the paragraphs and would ask the authors to disentangle the results of the mock community approach from the results of the ‘true’ samples. One possibility is to restrict oneself first to the mock community results, because they allow for setting the further results in a context. Then present the alpha- and beta-diversity results of the ‘true’ samples.