Reviewer report for manuscript JEcol-2024-0366, “Ectomycorrhizal tree islands in arbuscular mycorrhizal forests: hotspots of fungal inoculum important for seedling establishment of historically dominant trees”

Article summary:
The authors identified 20 Betula and 20 Acer trees (with 20cm+ DBH and at least 50 m apart from each other), located over three sites (Mianus River Gorge, Heiberg Memorial Forest and Tuller Hill State Forest) and established there paired (with or without the addition of forest litter) 1 square meter fenced subplots. At least two of these sites had been agricultural sites in the 1930s (line 111), suggesting that there was a paucity of ectomycorrhizal propagules in these sites at the time. Each of the subplots received three 4 – 6 months old seedlings per species Tsuga canadensis, Pinus strobus and Quercus sp. However, some Tsuga seedlings were replaced with Pinus. The authors monitored monthly survival and seedling height but also engaged to periodic clipping of competing vegetation (!) to “minimize understory competition”. At harvest the authors assessed root colonization in the seedlings. The authors also assayed eumycota via RFLP analysis (primers ITS1 and ITS4) which they coupled with occasional sequencing (i.e. the authors do not report to what extend they engaged into sequencing) to identify RFLPs. The analysis involved a series of fixed effects (even though the authors also used the library lme4 they do not report any random effects parameters) linear models which the authors present with fancy names (e.g. “multilevel logistic analysis of variance”). The authors observed no differences in survival (Table S2) or growth (Table S4) of seedlings in relation to their two manipulations (i.e. forest tree type and EM forest soil; actually, there is some weak evidence (F=3.9, P=0.047, for forest soil impacting Quercus seedling growth but this is quite likely an artifact of the analytical procedures). When the authors, however focused on seedlings from the second year they did observe some differences in total height (Table S6). They also found differences in fungal community structure (Table S8 and Table S9). The authors conclude (line 22) that “Agricultural land use legacies have resulted in expansive secondary forests dominated by AM trees. In these forests, establishment of EM tree seedlings outside of existing EM tree patches may be inhibited by a lack of EM fungi, but local soil inoculum from EM tree-dominated forests can reintroduce native EM fungi into secondary forests lacking established EM trees.”

I develop my report in relation to the main publication criteria of the journal:

Novelty:

The article addresses competitive dynamics of plants in woody habitats which are manifested via mycorrhiza. There has been considerable progress in our understanding of those interactions and they appear to act in a comparable way for arbuscular mycorrhiza- and ectomycorrhiza associating woody plants. A missed opportunity in my opinion was to integrate together, at least in the literature survey, those studies that address arbuscular mycorrhizal constraints in ectomycorrhizal dominated habitats with studies addressing ectomycorrhizal constraints in arbuscular mycorrhizal dominated habitats. I nonetheless find the specific topic that the authors address exciting and I feel that it would be a great consideration for a journal such as Journal of Ecology.
The biggest strength of the study is that the authors provide evidence that the sites had originally been agricultural. This backs up the idea that the main means with which ectomycorrhizal fungi could arrive to the sites is via source – sink relationships and propagation of ectomycorrhiza forming vegetation.
The biggest weakness of the study, in my view, is that the authors downplay the possibility that the actual driver of many of the differences was differences in the availability of nitrogen (N). The authors assayed total N (and they did observe differences) but we are aware that there can be massive difference in available N between ectomycorrhizal and arbuscular mycorrhizal vegetation in temperate forests (I would really love to cite here the study from Averill et al. 2014 Nature 505: 543 - 545). There is plenty of support that N availability lowers the richness but also induces massive shifts in the community structure of ectomycorrhizal communities. The authors report such changes between Acer- and Betula- habitats in relation to ectomycorrhizal communities. To me the possibility that a lot of the differences are induced by N availability reads as a much more parsimonious explanation and presents a possibility that the authors have not considered!
Overall, I think that the study ticks the box for novelty but the narrative is not quite there!

Scientific Writing:

I found the presentation reasonable. My two main concerns were the following:
1. Already from the beginning of the manuscript (lines 35 – 38) the authors present the transition to arbuscular mycorrhizal associating vegetation as an issue that they couple to the introduction of pests and pathogens. I have to admit that my expertise is on arbuscular mycorrhiza and I do not think that this is a disaster. First, I think the cause of the transition is the increases in N deposition which currently the authors do not consider. More N triggers a better performance of AM-associating plants over ECM-associating ones. However, increases in AM-associating trees coincide with increases in the richness of the understory and overall increases in biodiversity, which is desirable. This is particularly the case in relation to the low richness temperate forests. I recommend against using such red flag statements, which will bring a lot of unwanted attention to the article!
2. The materials and methods were painful to read. The authors nowhere declare the exact experimental design and the only way to deduct it is to go up and down the section several times to mine the appropriate information. I guess that this is possible at a review stage but unlikely to be done by the average reader.
Some additional comments in relation to the presentation:
The last paragraph in the introduction (lines 81 – 88) motivating the study reads as an endless list of unconnected ideas that is difficult for the reader to follow. Why do not the authors reformulate it in the form of two - three expectations/hyoptheses?
The article currently contains an absurd number of display items – ten: Six tables and four figures. Are all these needed?
There are some mis-citations every now and then. As an example, I do not think that Hoeksema et al. (2010 – line 67) showed anywhere that the effectiveness of soil inoculum type is context dependent!
The authors often present p values without their respective effect sizes. This is really a bad practice in papers.
I had a hard time in the paragraph in lines 469 – 478 to understand what parameters exactly the authors have assayed. As an example in line 473 (R-squared of 0.018) was it the interaction term?
There are some speculation jumps in the discussion. I will give two examples on this. In lines 502 – 504 the authors state that “EM tree seedling growth in secondary forests was enhanced through access to EM fungi via mycorrhizal networks associated with existing EM trees or by the addition of local EM forest soil inoculum.”. How do the authors know that it was mycorrhizal networks (which they did not assay) and not other parameters such as nutrient availability? Had it been mycorrhizal networks I would have expected stronger results over the first year of their experiment (help in seedling establishment), or else overall changes in seedling performance, which was not the case. A second example is in lines 539 – 540 is in relation to the statement (line 539) “The low levels of EM colonization of seedlings planted near AM Acer trees is likely due to fungal dispersal limitations". Yes, under some settings we can observe island biogeography effects in relation to ectomycorrhizal fungi but what is your support for this statement in your study!

Statistical Analysis:
I was a little disappointed that I could not find the exact code, data or model formulation that the authors have used. The supplementary tables present the output but I had to guess the model formulation. Unless there is a misreporting of the statistical procedures, the authors sufficed it to use fixed-effects statistics. The problem that I see is that in a lot of the general and generalized linear models (particularly the logistic ones) they most likely have used as a unit of their analysis the seedling and not the subplot. The way I read the methods part there is an apparent split-block design which needs to be taken in consideration (at minimum I think that the authors should have included as a random effects parameter the block ID) and which the authors did not do.
Also, I found the modelling procedure a little obscure (possibly a statistical editor can advise on whether my point here is valid). The authors combine experimental manipulations (i.e. focal tree type and EM forest soil) with observational ones such as pH. In the model building however they fit the experimental manipulations first without subjecting them into the model selection process and the same applies to some specific observational variables such as plot stem density. But then they engage into a forward stepwise selection based on likelihood ratio tests. There is a common understanding that most linear models (including those in the packages lme4 and car) use Type I Sums of Squares and the order with which variables are included can determine significance. I would have thus either expected the authors to narrow their models down to experimental manipulations or engage in a model building from scratch including first the most influential predictors. Otherwise, the model building reads dodgy: explaining more variance through adding covariates can increase the significance of parameters that have been included early on in the model.
Two more questions I had is (1) How the authors compare diversity in their molecular work without standardizing the sampling intensity? (2) on what grounds did the authors narrowed the analysis down to seedlings from the second year (Table S6)? – it reads a little like data-dredging!

Methodological Issues:
One of my major concerns was that the authors were clipping the understory vegetation periodically. I believe that this action induces massive shifts to the soil fungal community which the authors subsequently assayed.
Could the practice of moving soil have also introduced pathogens, pests and nutrients to the locations where it was applied? I think that the authors should discuss this possibility.
The authors did not assay mycorrhiza on the species but inferred it from the existing literature. I think some of the species have been reported to develop multiple types of mycorrhiza or not associate at all. Any mycorrhizal data would have thus been really welcomed.
Will the authors make their data available if the article gets accepted? I could not find any statement on this!

Overall recommendation:
I see a lot of issues with the manuscript. But at the same time I see a high potential. I think that the literature needs such articles right now. My feeling is that the authors should be given the chance to respond to comments and work out the, unfortunately many, issues on transparency and correct framing of their analysis.