Sampling Depth and Downsampling Effects

Genome sampling depth, clinical overrepresentation, differential missingness, and downsampling can substantially alter estimated relationships between environmental context and bacterial gene-content variation. Clinical sampling bias means overrepresentation of human-associated genomes in a comparative collection, potentially making genomic patterns appear ecological when they instead reflect epidemiological structure, sampling composition, or unequal statistical power. ₁ The Ecotype Reanalysis — Environmental vs Human-Associated Species directly tested whether this bias explained the weak environment–gene-content relationship and found that the bias was real, but did not support the hypothesis that removing or accounting for it would reveal substantially stronger correlations. ₁

The AlphaEarth Embeddings, Geography & Environment Explorer refines this context: among 83,287 genomes with AlphaEarth embeddings, 38% were human-associated, including 16,390 Human clinical genomes (20%), 13,466 Human gut genomes (16%), and 1,669 Human other genomes (2%), whereas Soil, Marine, and Freshwater each contributed 6,073 (7%), 5,850 (7%), and 5,840 (7%) genomes, respectively. ₂ Thus, clinical skew is directly visible in the embedding subset, but its magnitude should not be generalized to the full pangenome because AlphaEarth covered 28.4% of 293,059 genomes. ₂

Core Finding

The reanalysis used all genomes with AlphaEarth embeddings, including up to 3,505 genomes per species, whereas the original analysis used diversity-maximizing downsampling with a maximum of 250 genomes per species. ₁ Across all 183 species, the reanalysis produced a median partial correlation of 0.081, compared with 0.003 in the original analysis, a difference characterized in the report as 27x. ₁ A partial correlation measures the association between environmental embedding similarity and gene-content similarity after accounting for the analysis covariates used by the project. ₁

The report attributes the discrepancy partly to different genome sets and resulting changes in distance distributions, while cautioning that absolute correlation values should not be compared across the two methodologies. ₁ This supports the methodological principle that genome inclusion and sampling depth can change pangenome correlation estimates even when the biological question is unchanged, but it does not establish which method gives the more accurate absolute estimate because both the sampling strategy and genome sets changed. ₁

The independent Ecotype Correlation Analysis supports the weak-signal interpretation: across 172 species, the median partial correlation was 0.0025 for environment and 0.0143 for phylogeny; significant positive environmental effects occurred in 12 species (7.0%), significant negative effects in 4 species (2.3%), and no significant environmental effect occurred in 156 species (90.7%). ₃ Phylogeny dominated in 60.5% of species, while environment dominated in 39.5%. ₃ This refines the sampling result rather than resolving the absolute-scale discrepancy, because the analysis used a distinct species and genome subset.

Thus, sampling choices affect correlation distributions, but the available analyses caution against interpreting a larger environmental correlation as evidence of a stronger genome-wide ecological effect without matching the genome universe and procedure. ₁

Clinical Sampling Composition, Missingness, and Within-Method Comparisons

Among 224 species selected for the reanalysis using at least 20 genomes with AlphaEarth embeddings and at least 30% coverage, 106 species (47%) were majority human-associated, 47 (21%) were majority environmental, and 71 (32%) were Mixed/Other. ₁ Environmental categories included Soil, Marine, Freshwater, Extreme, and Plant; classification used a harmonized env_category mapping followed by majority voting over genome-level isolation_source assignments. ₁ This composition demonstrates strong clinical sampling bias in the AlphaEarth subset because human-associated species were the largest classification group. ₁

The majority-vote rule can classify a species with 51% gut genomes as Human-associated, so the analysis also used continuous fractions of environmental or human-associated genomes to reduce dependence on a categorical threshold. ₁

Within the reanalysis methodology, Environmental species had a median partial correlation of 0.051, mean 0.073, standard deviation 0.299, and range [-0.50, 0.78]. ₁ Human-associated species had a median of 0.084, mean 0.110, standard deviation 0.226, and range [-0.30, 0.73]. ₁ Mixed/Other species had a median of 0.109, mean 0.148, standard deviation 0.261, and range [-0.38, 0.69]. ₁ Environmental species therefore did not show stronger environment–gene-content correlations than Human-associated species; the Human-associated group had a slightly higher median and mean. ₁

The one-sided Mann-Whitney U test for Environmental > Human-associated gave U=1536 and p=0.83, so the null hypothesis was not rejected. ₁ The continuous Spearman analysis found no relationship between the fraction of environmental genomes per species and partial-correlation strength, with rho=-0.085 and p=0.25; the corresponding analysis for the fraction of human-associated genomes gave rho=0.030 and p=0.69. ₁ These results contradict the explanation that clinical sampling composition alone caused the weak ecological signal.

The original analysis likewise found no significant difference between environmental and host-associated bacteria, with p=0.66. ₃ This supports the reanalysis despite the different workflows, while the systematic genome-level classification and p=0.83 result refine the earlier coarse comparison rather than making the analyses numerically interchangeable. _3,1

These within-method comparisons refine the interpretation of the 27x discrepancy: sampling and extraction choices changed the absolute correlation scale, but the environmental-versus-human-associated comparison remained internally consistent under the reanalysis protocol. ₁ The pangenome-openness null result supports treating openness as an insufficient explanation for these group-level patterns, although it does not test the specific within-method comparisons. ₄

Nonrandom missingness means that observations are more likely to be absent in some biological or sampling groups than in others, potentially changing the apparent strength or direction of comparative-genomic associations. ₁ Of the 30 species with NaN partial correlations, the NaN rate was 10/47 = 21% for Environmental species, 13/66 = 20% for Mixed/Other species, and 7/100 = 7% for Human-associated species. ₁ Environmental species were therefore disproportionately removed by NaN filtering rather than Human-associated species. ₁ The report argues that this filtering would, if anything, bias the comparison toward finding a stronger environmental signal, which was not observed. ₁

This supports explicit missingness audits but does not establish why environmental species had more NaN correlations: the report does not demonstrate whether the cause was genome count, distance structure, gene-content variation, or another property of the analysis. ₁ Comparative analyses can become biased when filtering removes more observations from one ecological or taxonomic group than another, because retained observations may no longer represent the original group composition. ₁ The missingness pattern is therefore relevant even though it does not by itself show that missingness concealed a stronger environmental signal. ₁

Unequal sampling depth remains a plausible contributor because species with more genomes may have greater statistical power to detect weak correlations, but this explanation remains untested: genome count was not included as a covariate, and the authors flag that species with more genomes may have inflated correlations. ₁ Species with more genomes were often clinical species, and the Mixed/Other group had the highest median partial correlation, 0.109, possibly because it includes diverse sampling campaigns; this explanation was not demonstrated. ₁

Coverage, Metadata, and Unequal Power

The original analysis adds a separate coverage limitation: AlphaEarth embeddings covered only 28.4% of genomes, while geographic metadata were often missing or imprecise. ₃ This supports treating the weak environmental result as conditional on incomplete and noisy environmental representation rather than as proof that ecological adaptation is absent. ₃

The explorer refines this coverage limitation with a larger audit: AlphaEarth embeddings were available for 83,287 of 293,059 genomes, 79,449 had valid values across all 64 dimensions, and 3,838 contained at least one NaN. ₂ Among the embedding records, isolation_source was available for 76,295 (91.6%), host for 53,091 (63.7%), env_broad_scale for 34,800 (41.8%), env_local_scale for 31,541 (37.9%), and env_medium for 31,483 (37.8%). ₂ These unequal fields create additional opportunities for selection and unequal power beyond species-level genome counts; they therefore support joint modeling of genome count, embedding validity, and metadata completeness rather than treating embedding coverage as a neutral sample. ₂ The pitfalls digest quantifies the same embedding gap as 3,838 of 83,287 genomes (4.6%) with NaN in at least one of the 64 embedding dimensions. It warns that UMAP, cosine distance, and other operations will fail or produce NaN results silently. It prescribes filtering such genomes out before any embedding-based computation, which reduces the dataset from 83,287 to 79,449 genomes. ₅

The explorer refines metadata uncertainty further: keyword harmonization mapped 5,774 unique isolation_source values to 12 broad categories but captured 71% of genomes with a label; 17% remained Other and 12.5% were Unknown. ₂ The structured env_broad_scale field was cleaner but covered only 41.8% of the embedding subset. ₂ Thus, changing genome inclusion is not the only source of correlation-scale uncertainty: changing environmental classification and retaining or excluding ambiguous records can also change the effective genome universe. ₂

The Gene Function Ecological Agora reports metadata coverage on a different universe, its 18,989 P1B-qualified species-representative substrate. In ncbi-environment-metadata, isolation_source covered 76.8%, geo_loc_name 88.8%, ENVO env_broad_scale 48.6%, and lat_lon 47.3%. ₆ The report assigns biomes using mgnify, ENVO env_broad_scale, and isolation_source, with 76.8–88.8% coverage. ₆ This supports the explorer’s pattern that the structured ontology field is sparser than free-text isolation_source. The percentages are not interchangeable with the explorer’s embedding-subset figures, because the denominators differ: species representatives in one case and genomes with AlphaEarth embeddings in the other. _6,2

The original and reanalysis results should therefore be interpreted conditionally. A null group comparison should not be treated as evidence that missingness is harmless when missingness rates differ across groups. ₁ For this reanalysis, however, the direction of differential loss makes the simple explanation that clinical overrepresentation alone suppressed an environmental signal inconsistent with the reported results. ₁ The strongest supported conclusion is that, within the reanalysis methodology, environmental species did not show stronger environment–gene-content correlations despite having a higher NaN exclusion rate. ₁

Embedding Signal Is Not Necessarily Ecological Signal

Environmental embeddings had a 3.4x geographic-signal ratio, whereas Human-associated embeddings had a 2.0x geographic-signal ratio. ₁ Despite this stronger geographic signal, environmental embeddings did not correspond to stronger gene-content correlations. ₁ This supports environment-embedding-geography by showing that embedding similarity should not automatically be interpreted as ecological similarity.

The explorer supports the geographic-distance component of this interpretation: across 50,000 sampled genome pairs, mean embedding cosine distance increased from 0.41 for pairs <100 km to 0.82 for pairs 10K–20K km, with a plateau at intercontinental scales. ₂ Environmental categories showed mean cosine distance rising from 0.27 within <100 km to 0.90 above 10,000 km, compared with 0.37 to 0.75 for human-associated categories. ₂ This refines the meaning of the 3.4x and 2.0x ratios: the embedding captures spatially autocorrelated context, but the distance relationship is strongest below 2,000 km and plateaus above 5,000 km, so raw geographic distance is not a simple ecological proxy. ₂

The report proposes, as a hypothesis rather than an established mechanism, that Human-associated species can show geographic structure because regional epidemiological patterns may cause different lineages of species such as Klebsiella or Enterococcus to dominate different regions. ₁ Under that hypothesis, AlphaEarth embeddings may capture regional epidemiological patterns rather than ecological differences. ₁ The result refines environment-embedding-geography: geographic or collection-level context may encode real structure while remaining an imperfect proxy for the microenvironmental pressures that shape gene content. ₁ The original analysis makes this limitation explicit for host-associated organisms, whose coordinates may describe collection sites rather than actual microenvironments. ₃

The explorer further supports this collection-context caution: among 83,286 records with coordinates, 60.2% were classified as Good, 36.6% as Suspicious cluster, and 3.3% as Low precision; the heuristic flagged both likely institutional locations and legitimate field sites such as Rifle and Saanich Inlet. ₂ Consequently, coordinate quality can alter apparent sampling depth and spatial similarity, and should not be treated as a resolved nuisance variable. ₂

Interpretation for Pangenome Integration

The result supports pangenome-integration by showing that integrating environmental embeddings with gene-cluster data requires explicit control of genome-set construction, sampling depth, missingness, and metadata completeness. ₁ It also connects to ecotype-environment-gene-content, because the environmental-versus-human-associated null result persisted after replacing the original sampling strategy with a full-genome extraction approach. ₁

The analysis depended on combining genome metadata, AlphaEarth embeddings, ANI distances, and gene-cluster memberships, linking missingness assessment to cross-tenant-data-bridging and pangenome-integration. ₁

The reanalysis does not show that downsampling is intrinsically invalid, nor that using all available genomes is intrinsically preferable. ₁ Instead, the two approaches generated materially different correlation distributions whose absolute values should not be treated as interchangeable. ₁ The ecotype_analysis refines this conclusion by suggesting that environmental adaptation may affect specific gene subsets rather than whole-genome gene content, and that AlphaEarth embeddings may not capture all ecologically relevant variation. ₃

The Core Gene Paradox — Why Are Core Genes More Burdensome? supports this subset-level safeguard: core-gene burden was function-specific, with condition-dependent trade-off genes and costly-but-conserved genes identified from laboratory fitness measurements rather than as a uniform genome-wide property. ₇ This refines the interpretation that weak whole-genome correlation does not exclude ecological effects on particular gene subsets, while also cautioning that the Fitness Browser conditions are biased toward experimentally convenient rather than necessarily ecologically relevant conditions. ₇

The analyses also refine condition-space-dimensionality and environmental-resistome as interpretive safeguards: changing genome inclusion and metadata classification changed absolute correlations while preserving the within-method group comparison. ₁ Partial correlations assume linear relationships between distance matrices and may miss nonlinear ecological effects, so weak whole-genome correlation does not exclude environment-dependent effects on particular gene subsets. ₃

The pangenome-openness analysis supports this integration principle but refines its scope: openness showed no significant relationship with either environmental or phylogenetic effect size, so open-versus-closed status should not be assumed to identify which driver dominates gene-content variation. ₄ Because openness is a single summary metric and the analysis was limited to species with both openness statistics and ecotype results, this does not establish independence between pangenome structure and ecological dynamics. ₄ The report also notes that the upstream ecotype analysis may have limited statistical power for some species with few genomes. The per-species effect sizes entering the openness test therefore inherit uneven genome depth. ₄

Genome Caps, Ortholog Scope, and Coverage Filters

The Within-Species AMR Strain Variation shows the inverse of the downsampling problem. Instead of reducing large species, it limited ANI extraction for mantel-test analyses (tests of correlation between two distance matrices) to species with <=500 genomes for computational feasibility. This excluded mega-species such as escherichia-coli (15,388 genomes) and klebsiella-pneumoniae (14,240 genomes) from the phylogenetic-signal analysis. E. coli was also excluded from case studies because it exceeds the 500-genome computational cap. ₈ Subsampling strategies to run ANI-based Mantel tests on species with >500 genomes are proposed future work, not a reported result. ₈ This refines the page’s downsampling theme: a hard cap can remove the most heavily sampled, clinically important species entirely. Results that depend on the cap should therefore not be generalized to those species. ₈ The pitfalls digest records the computational reason for such caps. ANI queries for species with >500 genomes can take 30+ minutes per species and may time out Spark connections. K. pneumoniae (14,240 genomes) and staphylococcus-aureus (14,526 genomes) generate IN clauses with 14K+ IDs that overwhelm the query planner. The digest recommends capping Mantel tests at <=500 genomes, or subsampling. ₅

The scope of the comparative universe also matters for ortholog-based inference. Bidirectional-best-hit (BBH, reciprocal top sequence matches) pairs were compared between 5 organisms (10K pairs, 1,861 OGs, i.e. ortholog groups) and all 32 organisms (1.15M pairs, 13,402 OGs). Moving to all 32 organisms changed module families from 27 to 156 (6x), families spanning 5+ organisms from 0 to 28, and family-backed predictions from 31 (4%) to 493 (56%). ₉

The initial 5-organism run found just 27 families, and no family spanned more than 4 organisms. The digest concludes that the ortholog graph is not additive because adding organisms creates new transitive connections. Orthologs should therefore be extracted for all organisms in an analysis rather than a pilot subset. ₉ This supports the principle from the ecotype reanalysis that changing the genome universe can materially change an estimate, here for network structure rather than correlation scale. _9,1

The Functional Dark Matter — Experimentally Prioritized Novel Genetic Systems gives a parallel example: full-pangenome ortholog-group species counts range from 1 to 27,482 (median 135, mean 2,128), replacing the previous 1-to-33 range from the Fitness Browser-only analysis. ₁₀ This supports treating conservation or breadth metrics as conditional on the reference collection from which they are computed. ₁₀

Species-level coverage is a stricter filter than genome-level coverage. Only 6.8% of species (1,872/27,690) have sufficient AlphaEarth coverage (≥5 genomes with embeddings), which the digest attributes to missing lat/lon metadata for most NCBI genomes, especially clinical isolates. ₉ This refines the 28.4% genome-coverage limitation reported by the original ecotype analysis, because a species-level minimum turns sparse metadata into whole-species exclusion. _9,3

Single-genome filtering creates a further, taxonomically nonrandom gap. Twelve pangenomes without matching species clades are mostly obligate symbionts (e.g. Portiera aleyrodidarum, a whitefly symbiont, and Profftella armatura, a psyllid symbiont) or uncultivated lineages with UBA, TMED, or SCGC prefixes. They are valid pangenomes but were filtered from species metadata because of single-genome status. ₉

Small Cohorts and Representativeness

The Self-Sufficiency, Anaerobic Toolkit, and Cultivation Bias in Clay-Confined Cultured Bacterial Genomes illustrates how quality filtering can shrink an already small cohort. The deep cohort comprised 9 genomes before and 6 after filtering (Mont Terri Opalinus borehole 8, from BRC-3 and BIC-A1, plus bentonite formation 1). All 30 shallow-cohort genomes passed (Coalvale silty clay 8, Cerrado clay 1, agricultural clay 21). The phylum-stratified soil/sediment baseline with no clay mention declined from 150 to 137 genomes; its pre-filter phyla were Pseudomonadota 50, Bacillota 40, Bacillota_B 20, Bacteroidota 20, and Actinomycetota 20. ₁₁

After CheckM≥80 filtering, the 6 deep anchors had lower mean pathway completeness than 137 baseline genomes (15.50 versus 17.14; Cohen’s d, a standardized mean difference, of −0.84; p=0.009). The 30 shallow anchors had higher mean pathway completeness than the baseline (17.87 versus 17.14; d=+0.43; p=0.029). ₁₁ These are single-project results from very unequal group sizes and should be read alongside the report’s own power caveat. ₁₁

The clay report states that n=9 deep-confined genomes is power-limited and that only large effect sizes (Cohen’s d > 0.7) are reliably detectable in unfiltered comparisons. It adds that marginal p-values, such as the H1 within-Bacillota_B p=0.07, should be treated as descriptive. ₁₁ The filtered deep cohort is smaller still, so the stated detectability threshold for unfiltered comparisons should not be assumed to carry over to the filtered result. ₁₁

The Subsurface Bacillota_B Specialization — What Distinguishes Deep-Clay Lineages from Soil Congeners? has a similar design constraint. With 10 anchor versus 62 baseline genomes, the report describes Fisher’s exact tests as adequate for large effects and reports the 547 enriched OGs as robust. Marginal effects with anchor counts of 3–5 should be treated descriptively rather than inferentially. The cohort spans four orders (Desulfotomaculales, Desulfitobacteriales, Ammonifexales, Thermacetogeniales), which only partly mitigates genus-level phylogenetic confounding. ₁₂ The report also says n=10 anchors is at the limit of statistical resolution for genus-level decomposition. ₁₂ Mean CheckM completeness was similar, 94.7% versus 94.3% (Cohen’s d +0.08; p 0.93), which weakens MAG (metagenome-assembled genome) quality artefacts as an explanation for the genome-size difference. ₁₂ Within these stated power limits, this result supports subsurface-bacillota-specialization, and it connects to phylogenetic-confounding-of-pangenome-associations. ₁₂

Sparse metadata impose the same constraint in host-associated work: in the Rational Design of Protective Microbiome Formulations for Competitive Exclusion of *Pseudomonas aeruginosa* in Cystic Fibrosis Airways, only 21 lung genomes across 5 species were available, limiting the lung-adaptation comparison. ₁₃

Species sampling can also limit representativeness. In the Ecotype Functional Differentiation, 12 species from 15 sampled (80%), out of 456 eligible, contributed valid ecotypes. The report notes that stratification across pangenome sizes may not capture phylogenetic or ecological breadth. ₁₄

The COG Functional Category Analysis interprets its cross-phyla COG (Clusters of Orthologous Groups functional category) pattern as holding universally across bacterial phyla and as suggesting deep evolutionary constraint. The same report notes that the analysis uses 32 species and that a larger sample might reveal phylum-specific patterns. ₁₅ Universality should therefore be treated as a hypothesis extrapolated from a 32-species sample rather than an established finding; this refines two-speed-bacterial-genome. ₁₅

Physical sample depth, a distinct sense of “sampling depth”, shows how missing covariates restrict inference. In the Metadata Correlates of Eukaryotic Contamination in NMDC Prokaryote-Targeted Metagenomes, the NEON soil study had zero non-null depth values, so depth was not part of its batch-controlled analysis. ₁₆ A cross-study association was present (Spearman ρ = −0.29, p=5.2×10⁻⁷, n=292 runs with measured depth), with shallower samples carrying more eukaryotic DNA. It was not batch-controlled because the measured-depth runs came from a handful of non-soil studies, and the report treats it as suggestive only. ₁₆ This links depth effects to study-batch-confounding-of-environmental-associations. ₁₆

The same project provides a direct missingness artifact that supports this page’s call for missingness audits. An earlier version that retained the Unknown/missing-metadata bucket, which had the highest median eukaryotic fraction, reported an inflated p≈10⁻⁵⁰. After that bucket was excluded, ecosystem_type reduced to the same three biomes as matrix (Soil / Freshwater / Roots) and was not an independent confirmation. ₁₆ As literature context rather than a project measurement, the report cites Ortiz-Chura et al. (2024, PMID 39456104) for >40% missing basic fields in public collections. ₁₆

Point Estimates That Do Not Survive Scaling

The Gene Function Ecological Agora tested Alm 2006’s correlation between histidine protein kinase (HPK) count and gains of two-component system (TCS) genes. It reports that Alm 2006’s r ≈ 0.74 in 207 genomes was NOT REPRODUCED at gtdb (Genome Taxonomy Database) scale, across 18,989 P1B-qualified species-representative genomes (one per species). All four framings were statistically significant (n = 18,989) but biologically modest (r = 0.10–0.29; all r<0.30). The strongest framing, HPK count versus recent TCS gains at genus rank, recovered r = 0.29. ₆ The report says the methodology generalization holds. The qualitative TCS HK recent-skew holds at architectural resolution, with NB17 consumer-side architectural concordance r = 0.67, while the quantitative r ≈ 0.74 point estimate does not survive scaling from 207 to 18,989 genomes. The report thus distinguishes architectural concordance from numerical replication. ₆ This result comes from a different biological question, but it supports the page’s central caution that changing the size and composition of the genome universe can change effect sizes even when direction is preserved; see gene-function-acquisition-depth and two component system histidine kinases. _6,1

The report proposes three mechanisms for the failed point-estimate reproduction: substrate-scale heterogeneity, tree-aware versus paralog-count operationalization, and tree-rank granularity. These are identified explanations rather than separately tested causes. ₆

Other clade-level effect sizes in the same report changed little after D2 residualization. In that step, producer_z and consumer_z scores were adjusted for clade size, annotation fraction, GC%, and genome size, and the report compared raw with residualized Cohen’s d and gave residualized p-values. For the mycolic acid order consumer_z test in Mycobacteriales, d changed from −0.29 to −0.28 (p <10⁻¹⁰). For cyanobacteriia × photosystem ii, class producer_z remained d = +1.50 (p = 2.1×10⁻⁵), and class consumer_z changed from d = +0.70 to +0.63 (p = 2.3×10⁻⁵). ₆ These values show that specific clade-level effects are robust to covariate adjustment for clade size and annotation density. They do not test robustness to genome subsampling. ₆

The D2 step regressed per-clade aggregate covariates (clade_size, mean annotated_fraction, mean GC%, mean genome_size) against producer_z and consumer_z separately using OLS (ordinary least squares). It then re-ran the NB11, NB12, and NB16 hypothesis tests on the residualized scores. ₆ Producer R² was 0.000: producer_z was uncorrelated with all 4 covariates. The report attributes this to its within-rank null model already absorbing prevalence and clade-size effects, so there was no producer-side bias to remove. ₆ Consumer R² was 0.053, small but non-zero. Its coefficients were −1.27 for mean_annotated_fraction_z (higher-annotated clades had more negative consumer_z), +1.13 for clade_size_z, −0.49 for mean_genome_size_z, and −0.05 for mean_gc_z. ₆ The report notes that this annotated-fraction adjustment was specified in plan v1 / v2 as a nuisance covariate but was deferred multiple times across phases, while repeated adversarial reviews pressed on annotation-density artifacts. Its answer is that producer_z is bias-immune (R² = 0), while consumer_z carries a small bias term (R² = 0.05) that does not change any verdict. ₆

The residualized tests support the robustness reading of the preceding paragraphs. NB11 regulatory-versus-metabolic producer_z stayed at d = +0.06 (p = 0.69), a null result before and after adjustment, while consumer_z stayed at d = −0.21 (p <10⁻¹⁰). ₆ For mycobacteriaceae × mycolic acid, family producer_z stayed at d = +0.31 (p = 2×10⁻⁶). Family consumer_z attenuated from d = −0.19 to −0.16 (p = 1.6×10⁻⁵), and Mycobacteriales order producer_z stayed at d = +0.29 (p = 5×10⁻⁶). ₆ The report’s verdict is that all hypothesis verdicts survive D2 annotation-density residualization. The largest attenuation is the NB12 family-rank consumer-side change (~16% relative attenuation, still significant). NB11 H1 REFRAMED, NB12 H1 SUPPORTED, and NB16 H1 SUPPORTED at class rank all preserve direction and significance. ₆ As above, this is robustness to covariate adjustment, not to genome subsampling. ₆

Substrate filters shrink the same analysis sharply. Of the 18,989 P1B-qualified species representatives, 10,856 have no_genomes ≥ 3, which is the multi-genome substrate on which the report considers openness meaningful. Of 3,539 genera with at least one multi-genome species, 894 have ≥3 multi-genome species and form the T1 substrate. ₆ In targeted tests, T3a Mycobacteriaceae × mycolic-acid recovered Pearson r = +0.46 (Spearman +0.41) across 10 genera. T3b cyanobacteriia × photosystem ii recovered Pearson +0.11 / Spearman +0.12 across 83 genera. Both directions are positive and consistent with the NB12/NB16 verdicts, but both confidence intervals span zero. ₆ The report identifies multi-genome species coverage as the limiting factor: only 289 species across 10 genera in Mycobacteriaceae, and 185 species across 83 genera in Cyanobacteriia. These targeted tests are therefore underpowered corroboration rather than independent confirmation; this links to pangenome-openness-determinants. ₆

Rarefaction, Prevalence Filters, and Taxon Duplication

The Metal Resistance Ecology — Phylogenetic Conservation vs. Environmental Selection directly tested whether genus-level sampling depth drives its association between inferred metal types and the niche-breadth score B_std. It used phylogenetic-generalized-least-squares (PGLS, regression that accounts for phylogenetic non-independence) models. With the species-with-AMR count (n_species) as a covariate, the metal-type coefficient was +0.0204 (SE 0.0057, p = 3.4×10⁻⁴), and n_species was +0.0093 (SE 0.0051, p = 0.068). With all three metal predictors plus n_species, metal types retained +0.0224 (SE 0.0067, p = 8.3×10⁻⁴), and n_species was nonsignificant at +0.0092 (SE 0.0051, p = 0.070). ₁₇ The report characterizes the covariate as borderline (p ≈ 0.07), indicating a modest but non-dominant contribution of sampling depth. ₁₇ In the report’s summary table, both covariate models (n=606) remained significant after benjamini-hochberg-fdr correction (BH-FDR, which controls the expected false-discovery rate), with q = 0.003 for the simple model and q = 0.004 for the multi-predictor model. The report also rejects a reviewer’s claim that the genome-count covariate was fit only by OLS. Both R1 and the later S4 sensitivity used gls() + corPagel (PGLS), and the metal-type β remained significant after adjustment. ₁₇

The covariate matters because genome sampling is itself associated with the predictor. The Spearman correlation between sequenced genomes per genus and inferred metal type diversity is r = 0.35 (p = 2.6×10⁻¹⁹). Single-genome genera have detectably lower metal type counts than multi-genome genera (Mann-Whitney p = 5.1×10⁻¹⁰). ₁₇ A log-transformed covariate (sensitivity S4: z-scored log(n_species), n=606) gives a different picture of the confound than the linear R1 covariate. Metal types remained significant (β = +0.0195, SE 0.0057, p = 6.4×10⁻⁴, q = 0.004). However, log(n_species) was itself significant (β = +0.0127, SE 0.0053, p = 0.016), whereas the linear covariate in R1 was borderline (p = 0.07). ₁₇ The report reads this as a log-linear genome-count effect, possibly because well-sampled genera include more ecologically diverse isolates. It states that the metal-type β drops only from +0.021 to +0.020, indicating only a small confound. It also reports that metal types retain a ΔAIC of approximately −10 beyond the log(n_species)-only model. ₁₇ This refines the R1 result: once the log-linear form is modeled, sampling depth is a detectable rather than merely borderline contributor, while the metal-type association still survives adjustment. The ecological-diversity mechanism is the report’s interpretation, not a tested result. ₁₇

A three-covariate model (R6) refines the S4 result further. It adds log(genome size) alongside log(n_species) and is fit on n = 527 genera with all three covariates, rather than the 606 used in S4. In R6, metal types (z) remained significant at β = +0.0218 (SE = 0.0061, t = 3.60, p = 3.5×10⁻⁴), while log(n_species) (z) was nonsignificant at β = +0.0052 (SE 0.0057, t = 0.90, p = 0.366). Log(genome size) (z) was independently significant at β = +0.0255 (SE 0.0069, p = 2.6×10⁻⁴), with λ = 0.628. ₁₇ The report interprets the loss of log-count significance as indicating that the log(n_species) effect in S4 was partly mediated by genome size, because larger genera tend to have larger genomes. That mediation reading is the report’s interpretation rather than a separately tested result. The S4 and R6 estimates also differ in both covariate set and genus sample, so both results should be kept rather than one replacing the other. ₁₇

To remove the genome-count bias formally, the report ran 200 PGLS iterations in which each genus was represented by a single randomly sampled species. Of the 606 PGLS genera, 383 had more than one species in the AMR database; the remaining 223 were singletons that rarefaction does not change. ₁₇ Across iterations, the median β for metal types → B_std was +0.0147 (IQR +0.0126 – +0.0166) and the median p was 0.0054. Of the iterations, 89.5% reached p < 0.05 and 57.5% were Bonferroni-significant (p < 0.0083). Median Pagel’s λ, a measure of phylogenetic signal, was 0.704. ₁₇ The report’s summary table lists the same rarefied median at n=606 as β = +0.0147 with SE ~0.011 and p = 0.005, and gives no q-value or q-significance decision for it. The limitations section rounds the median to +0.015 and repeats that 89.5% of iterations yield p < 0.05. ₁₇

The effect direction was consistent across all 200 iterations, but the median β (+0.0147) was smaller than the full-data estimate (+0.0215). The report attributes this attenuation to reducing multi-species genera, which have higher inferred metal types, to one representative, and concludes that the signal is not artefactual. ₁₇ This supports the page’s central pattern, also seen in the Alm 2006 reproduction above, that rebalancing sampling depth can preserve direction while shrinking effect size. It also refines the open question from the ecotype reanalysis: an explicit depth covariate plus rarefaction can be run within one project, rather than inferred by comparing methodologies. _17,6,1

The report is internally inconsistent about whether this rarefaction is finished. Its reviewer-response table states that R2 rarefaction shows a consistent positive direction, and that sensitivity S3 confirms genus means are not inflated by outlier species. ₁₇ Its Future Direction #1 nevertheless proposes pangenome rarefaction to formally control the genome-sampling depth confound. That proposal would resample genera to equal genome coverage (e.g., n = 1 or 2 species), repeat PGLS, and require the species-level AMR table stratified by genome count. ₁₇ The limitations section names the remaining gap as a formal pangenome rarefaction curve testing multiple species-per-genus thresholds, which would quantify the depth-of-coverage effect more precisely. ₁₇ The future-direction text should not be read as evidence that no rarefaction was performed. One reading consistent with both statements, though the report does not state it, is that single-threshold rarefaction was run but a multi-threshold curve was not. ₁₇

A second robustness filter shows that removing sparse detections also shrinks the analysis universe, and here the association did not survive at conventional significance. Niche breadth was recomputed using a strict 5% within-environment prevalence threshold: an OTU (operational taxonomic unit) counted as present only if it appeared in ≥5% of samples in that category. The aim was to reduce detections driven by contamination, cross-sample bleed-through, or rare transient events. ₁₇ The filter reduced passing OTUs from 98,919 to 10,433, genera with a B_std estimate from 3,160 to 1,120, and the PGLS sample with AMR data from 606 to 379 genera. Original and strict B_std had Pearson r = 0.680. ₁₇ Under the strict threshold, the metal-type effect lost statistical significance: β = +0.0166 (SE = 0.0099), p = 0.092, compared with β = +0.0215 (SE 0.0056), p = 1.5×10⁻⁴ in the full analysis; λ fell from 0.708 to 0.526. ₁₇ The report attributes the loss of significance primarily to reduced sample size (n drops 37%: 606 → 379) rather than to a change in direction or magnitude. It describes the β change from +0.0215 to +0.0166 as a 23% reduction, although the SE also rose from 0.0056 to 0.0099. The summary table lists this strict-prevalence row (n=379) without a q-value. The report says the 5% threshold is quite conservative, excluding 89% of OTUs, many of which are genuinely distributed across environments but uncommon within any one. It proposes a threshold of 1–2% as a reasonable middle ground for future work. It concludes that the signal is not driven entirely by spurious rare detections but that power requirements for strict prevalence-based niche breadth are substantially higher. This power explanation is the report’s interpretation, not a separately tested result, so the strict-filter null should be retained as a caveat rather than treated as confirmation. ₁₇

A milder abundance filter was applied to a different quantity: the phylogenetic conservation of niche breadth, rather than the metal-type coefficient. Per-OTU mean relative abundance was estimated using a mean library size of 87,595 reads/sample across 463,972 samples. Excluding OTUs below 0.01% mean relative abundance removed 66% of OTUs and left 33,676. Of these, 23,759 bacterial non-organellar OTUs covered 576 of 606 PGLS genera. ₁₇ Before filtering, bacterial B_std Pagel’s λ was 0.787 across all 1,264 genera and 0.763 for the same 576 genera; after filtering it was 0.750. The likelihood-ratio-test (LRT) p was 2.8×10⁻⁴⁰ after filtering, versus 7.9×10⁻¹⁰² and 5.9×10⁻⁴⁰ for the unfiltered sets. The report gives the change as −0.013 (−1.7%). ₁₇ The report concludes that phylogenetic conservation of niche breadth is not an artefact of rare transient OTU detections. This result contrasts with the strict 5% prevalence filter above: the phylogenetic-signal estimate was stable under abundance filtering, whereas the metal-type coefficient lost significance under prevalence filtering. The two filters should therefore not be read as a single robustness verdict. ₁₇

Some depth effects could not be corrected at all. The report records that primer bias and differential sequencing depth were not correctable with the available data, and acknowledges this as a limitation. ₁₇

Duplicate taxa can inflate effective sampling depth in the same way as clinical overrepresentation. In the Pan-Bacterial Metal Fitness Atlas, excluding 4 duplicate pseudomonas-fluorescens FW300 strains (keeping only pseudo3_N2E3) reduced the analysis from 22 to 18 organisms. The core enrichment remained at OR (odds ratio) = 2.065, p = 5.9e-141, versus OR = 2.083, p = 4.3e-162 with all organisms. The report concludes that the result is not driven by Pseudomonas overrepresentation. ₁₈ This supports treating duplicate-lineage removal as a routine sensitivity check, and connects to phylogenetic-confounding-of-pangenome-associations. ₁₈

Sequencing depth is another sense of sampling depth. In the Lignin Enrichment and Ecological Memory in Microbial Communities, fungal its amplicon sequencing (ITS) richness fell from 253 OTUs in Base to 3–8 OTUs per group after enrichment. ITS replicate consistency was poor, however: within-group bray curtis dissimilarity was 0.65 for ITS and reached 0.99–1.00 for several Round 2 groups, compared with 0.09 for bacterial 16s-amplicon-sequencing communities. This limits statistical inference for ITS. ₁₉

Among the contributors the report lists for poor ITS replicate consistency are low sequencing depth in some samples (ITS was rarefied to 5,900 reads versus 24,000 for 16S) and very low diversity in enriched groups (3–8 OTUs), which makes composition highly sensitive to stochastic variation. It also lists exclusion of sample LL_1 (74 reads after filtering), which reduced L-L to n=2, and possible underrepresentation of environmental taxa in the NCBI ITS_RefSeq_Fungi database. ITS depth ranged from 6,953 to 200,902 reads per sample, which may contribute to variability even after rarefaction. ₁₉ These are the report’s proposed explanations rather than separately tested causes. They suggest that rarefying to a common depth may not remove depth-related variability when post-enrichment communities are this sparse and replication is reduced, which refines this page’s theme and bears on ecological-memory analyses that rely on ITS composition. ₁₉

Training-set depth can change what a predictive model learns. In the Genotype × Condition to Phenotype Prediction from ENIGMA Growth Curves, with 7 anchor strains (NB06) the model learned genome scale (25.3%) and condition class (45.9%), which the report summarizes as essentially “big genomes grow on amino acids”. With 46K training pairs (NB07), it learned condition-specific KOs (KEGG orthologs), such as a ribose transporter that predicts ribose growth rather than generic carbon-source growth. ₂₀ In this single-project comparison, training-set size and design changed together. It therefore supports, but does not isolate, the hypothesis that shallow training sets push models toward coarse genome-scale features. ₂₀

Minimum-Genome Filters and Uneven Sampling Across Projects

The Pan-Bacterial Anti-Phage Defense Arsenal makes the coverage trade-off explicit. Its arms-race and syndrome tests use the ≥5-genome analysis set, because reliable core/accessory calls require ≥5 sequenced genomes per species. The filter reduces the analysis set to 7,323 species (26 % of 27,690 pangenome species), biasing it toward well-sampled, culturable, high-priority organisms. Extrapolating the arms-race pattern to the full 293K-genome tree, which includes many MAGs from environmental samples, is plausible but untested. ₂₁ This supports the species-level-coverage caution above. A minimum-genome threshold that makes per-species calls reliable also shifts the species universe toward heavily sampled lineages; see phage-defense-syndromes-and-arms-race. ₂₁

The Polyhydroxybutyrate Granule Formation Pathways — Distribution Across Clades and Environmental Selection reports the same AlphaEarth bottleneck for niche breadth. Only 28% of genomes (83K/293K) have AlphaEarth embeddings, which could skew its niche-breadth analysis toward better-sampled lineages. The 2,008 species analyzed represent 7.2% of total species diversity. ₂₂ This supports the 28.4% genome-coverage limitation reported by the ecotype analysis. The 7.2% figure and the discoveries digest’s 6.8% species-coverage figure are not interchangeable, because their inclusion criteria differ; see phb-granule-ecology. _22,9,3

Within-genus imbalance can be extreme. In the Carbon Source Utilization Predicts Ecology and Lifestyle in Pseudomonas, pseudomonas-aeruginosa comprises 53% of all genomes (6,760/12,732) because of its clinical importance, while many environmental species have <10 sequenced genomes. The report says this imbalance affects the power of species-level comparisons. ₂₃ Its environment prediction was run at species level. To increase statistical power, it proposes moving to genome-level analysis using the full 789K genome-pathway matrix with genome-specific isolation sources. ₂₃ This supports the clinical-overrepresentation theme of the ecotype reanalysis at the scale of a single genus; see cultivation-collection-bias-in-ecological-genomics. _23,1

The Metabolic Capability vs Dependency flags the same depth problem for within-species variation. Species with more sequenced genomes are more likely to show pathway variation and more ecotypes. Partial correlations controlling for genome count mitigate but do not fully eliminate this bias. ₂₄ This refines the ecotype-reanalysis proposal to add genome count as a covariate: a covariate is a partial rather than complete remedy, consistent with the attenuation seen under one-species-per-genus rarefaction in the metal-ecology project. _24,1,17

Genome-rich species can dominate a multivariate effect. In the Plant Microbiome Ecotypes — Compartment-Specific Functional Guilds and Their Genetic Architecture, the original NB04 permanova (a permutation-based multivariate analysis of variance) reported R² = 0.527 for plant compartment on the Phase 1 25-marker panel. R² dropped to 0.072 when the top-3 genome-rich species per compartment were excluded (an 86% loss). ₂₅ This large effect size did not survive removal of the most heavily sampled taxa. The result supports routine leave-out sensitivity checks like the duplicate-strain exclusion above, and it bears on ecotype-environment-gene-content. _25,18

The same report shows how changing a marker panel can also change the population under comparison. After panel refinement, the dual-nature rate among plant-associated species was 78.7% (878/1,115 species). Retained markers co-occur in plant-associated genomes: phosphate solubilization (57.9% prevalence), CWDE cellulase (63%), phenazine (63%), and T4SS (45.8%). ₂₅ The report describes this as an increase from 60.3%, but that earlier figure is 15,474/25,660 species overall, not plant-associated species. Because the populations differ, the comparison does not establish a within-population increase caused by refinement; see dual-nature-plant-associated-bacteria and functional-marker-validation. ₂₅

Fixed per-species subsampling is another depth choice. In the Prophage-AMR Co-mobilization Atlas, co-localization used 20 genomes sampled per species (NB02) rather than all 293K genomes. The report considers this sample representative but notes that exhaustive analysis would strengthen the findings. ₂₆

Small comparator groups limit cross-species tests. The Condition-Specific Respiratory Chain Wiring in ADP1 cross-species comparison has only 4 organisms without ndh 2, which is insufficient for statistical significance. ₂₇

Reference-collection growth can also change counts between planning and analysis. In the PGP Gene Distribution Across Environments & Pangenomes, the research plan estimated ~1,913 nifh clusters, but the actual count was 2,756 (43% higher). The report attributes the difference to incremental growth in the gtdb r214 pangenome and states that it does not affect any analysis. ₂₈ This supports the functional_dark_matter observation that breadth metrics are conditional on the reference collection. _28,10

Sampling effort can masquerade as a discovery gap. The Soil Microbial Dark Matter and the Clay Shield Null Result reports a pH discovery bias of +0.8 units and says it needs a reverse-causality check. Alkaline soils may have fewer genomes in databases simply because fewer samples from those pH ranges were ever sequenced, rather than because alkaline microbes are harder to assemble or less studied. ₂₉ Two analyses remain pending: control for the number of 16S samples per pH bin, and a rarefaction-corrected genomic discovery index (GDI) using uniform 16S sequencing depth before richness calculation. Until these are done, the pH gap should be treated as a hypothesis about genomic under-representation rather than an established finding; see genomic-under-representation and spatial-sampling-effort-confounding. ₂₉

Tensions

The principal tension is between confirmed clinical sampling bias and the absence of a stronger environmental correlation after group comparison. ₁ The AlphaEarth subset is clinically skewed, but the evidence does not support the claim that this skew alone explains the weak environment–gene-content relationship. ₁ The explorer independently confirms the skew but also shows that environmental samples have stronger geographic embedding structure, so spatial signal and gene-content signal remain discordant rather than reconciled. ₂

A second tension concerns missingness: Environmental species had a 21% NaN rate compared with 7% for Human-associated species, yet removing more Environmental species did not produce the expected stronger environmental signal. ₁ This indicates that missingness, sampling depth, and ecological classification must be analyzed jointly rather than treated as interchangeable explanations. ₁ The explorer adds 3,838 records with at least one embedding NaN and uneven metadata coverage, refining rather than resolving this tension. ₂

A third tension is between the large difference in overall correlation values and the stability of the within-method environmental-versus-human-associated comparison. ₁ The reanalysis reported a median partial correlation of 0.081 across 183 species, whereas the original analysis reported 0.003, but the absolute values are not comparable because the analyses used different genome sets, sampling strategies, and distance distributions. ₁ The ecotype_analysis provides a separate median environmental value of 0.0025 across 172 species and a phylogenetic value of 0.0143, but does not resolve the tension because its coverage and analysis population also differ. ₃

The function-specific fitness evidence adds a related interpretive tension rather than resolving the sampling discrepancy: core genes were more burdensome in several functional categories but less burdensome for Cell Wall genes, and the Fitness Browser condition types were biased toward experimentally convenient conditions. ₇ This refines the claim that sampling controls alone can explain weak whole-genome ecological associations: even with matched genome sampling, condition coverage and functional aggregation could affect which biological signal is visible. ₇

The pangenome-openness null correlations do not contradict the sampling-depth result: they test whether an openness summary predicts effect sizes rather than whether changing genome sampling changes correlation estimates. ₄ They leave unresolved whether openness fails because pangenome structure is genuinely decoupled from eco-phylogenetic dynamics, because the metric is too coarse, or because the matched species sample and upstream effect estimates limit power. ₄ Resolving whether the correlation-scale difference is driven mainly by downsampling, genome-set composition, extraction behavior, embedding coverage, condition coverage, missingness, or another methodological factor requires a controlled reanalysis. _1,3,7

The metal-ecology robustness checks carry internal tensions that remain only partly resolved. The log-transformed genome-count term was significant in S4 (p = 0.016, 606 genera) but nonsignificant in the three-covariate R6 model that added log(genome size) (p = 0.366, 527 genera). The report attributes this to genome-size mediation, but that is its interpretation, and the genus sample also changed between the models. Rarefaction is reported as completed (R2), yet also proposed as Future Direction #1. The strict-prevalence filter left the metal-type effect nonsignificant (p = 0.092), which the report attributes to power rather than testing that explanation. ₁₇

Open Directions

• Use the same species and genome universe to compare diversity-maximizing downsampling with full-genome extraction, using matched distance calculations, then test whether sampling strategy or genome-set composition explains the change from 0.003 to 0.081 and the reported 27x difference. ₁
• Add genome count as a covariate to the species-level correlation model, then test whether unequal sampling depth inflates correlations in species with more genomes. ₁
• Use the complete species-by-genome table and a missingness model, such as logistic regression or inverse-probability weighting, to test whether genome count, environment category, and distance structure predict NaN status. ₁
• Recalculate correlations after matched-depth downsampling and full-genome extraction, then test whether the missingness-rate difference and the 27x overall correlation discrepancy persist. ₁
• Recompute correlations after matched-depth downsampling across species, then test whether the environmental-versus-human-associated comparison remains null when statistical power is balanced. ₁
• Analyze transport, secondary-metabolism, and other functional gene subsets with identical downsampling and extraction settings, then test whether whole-genome Jaccard distances mask sampling-depth or ecological effects. ₁
• Replace majority-vote categories with structured ENVO terms from env_broad_scale and repeat group, continuous-fraction, and missingness analyses, testing whether finer environmental ontology changes the null result or group-dependent loss. ₁
• Reassess species with NaN correlations using alternative missing-data and minimum-sample thresholds, and model NaN outcomes jointly with environment category, genome count, and phylogeny to test whether the higher Environmental NaN rate changes the group comparison. ₁
• Compare AlphaEarth geographic signal with independent epidemiological and ecological metadata for species such as Klebsiella or Enterococcus, testing whether embedding structure reflects regional epidemiology rather than ecological differentiation. ₁
• Using the same matched genomes, compare AlphaEarth distances with direct environmental metadata and test whether COG categories such as V-Defense and L-Mobile reveal ecological effects hidden at the whole-genome level. ₃
• Reanalyze the 172 species with sufficient environmental and phylogenetic data using alternative embedding distances and direct environmental metadata, then test COG subsets and ecotype-cluster gene content to determine whether ecological effects are localized rather than genome-wide. ₃
• Recalculate openness using auxiliary fraction, Heap’s law alpha, and pangenome fluidity on the matched genome universe, then test whether functional subsets or lifestyle interactions reveal relationships hidden by the single openness metric. ₄
• Pair matched genome-set analyses with matched condition or functional-subset analyses, then test whether the observed correlation scale changes are attributable to sampling depth, condition coverage, or aggregation across heterogeneous gene functions. _7,1
• Repeat the environmental-only ecotype analysis after excluding ambiguous coordinates and records classified as Other or Unknown, then test whether the environment–gene-content relationship changes when spatial and harmonization uncertainty are reduced. ₂
• Compare keyword harmonization with env_broad_scale on the 41.8% of records covered by the structured field, using matched genomes and identical downsampling to test whether classification uncertainty contributes to the correlation-scale discrepancy. ₂
• Analyze transport and secondary-metabolism gene subsets with the same missingness diagnostics to test whether whole-genome Jaccard distances mask environment-specific associations. ₁
• Develop repeated ANI subsampling for species with >500 genomes, including E. coli and K. pneumoniae, then test whether Mantel-based phylogenetic signal estimated under the <=500 cap generalizes to mega-species. ₈
• Rerun the Alm 2006 HPK–TCS framings on nested genome subsets between 207 and 18,989, then test whether the drop from r ≈ 0.74 tracks sample size, substrate heterogeneity, or tree-rank granularity. ₆
• Add deep genomes to the small subsurface anchor cohorts (n=9 or n=10), then repeat the pathway-completeness and OG-enrichment tests to see whether marginal, descriptive effects persist at adequate power. _11,12
• Recompute B_std at the report’s suggested intermediate 1–2% prevalence threshold and rerun the one-species-per-genus rarefaction, testing whether the metal-type effect that lost significance under the strict 5% filter (p = 0.092, 379 PGLS genera) is recovered when sparse-detection filtering and depth rebalancing are combined. ₁₇
• Expand multi-genome species coverage for Mycobacteriaceae and Cyanobacteriia beyond 289 and 185 species, then retest T3a and T3b to see whether their positive correlations lift the confidence intervals off zero. ₆
• Resequence or subsample ITS libraries to matched depth across replicates, then test whether within-group Bray–Curtis distances of 0.99–1.00 in Round 2 groups reflect sequencing depth or stochastic community assembly. ₁₉
• Build the multi-threshold species-per-genus rarefaction curve that the metal-ecology report names as its remaining gap. Refit S4 on the 527 genera with genome-size data, with and without log(genome size), to test whether the loss of log(n_species) significance in R6 reflects genome-size mediation or the change in genus sample. ₁₇
• Control GDI for the number of 16S samples per pH bin and recompute it after rarefying to uniform 16S depth, testing whether the pH discovery bias of +0.8 units persists as an assembly or annotation gap. ₂₉
• Repeat the plant-compartment PERMANOVA with repeated per-species genome subsampling instead of top-3 exclusion, testing how much of the drop from R² = 0.527 to 0.072 reflects genome-rich species. ₂₅
• Test whether the phage-defense arms-race pattern holds outside the 7,323-species ≥5-genome set, using presence-only calls for species with fewer genomes, to address the untested extrapolation to the full tree. ₂₁